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Referee #3

Evidence, reproducibility and clarity

The manuscript entitled "Arp2/3 Complex Activity Enables Nuclear YAP for Naïve Pluripotency of Human Embryonic Stem Cells" by Nathaniel Meyer, Tania Singh, Matthew Kutys, Todd Nystul, and Diane Barber analyzes the formation of the actin ring that surrounds naive but not primed colonies of human embryonic stem cells (hESCs). The authors claim that the formation of this actin ring requires Arp2/3 which also modulates YAP localization. Despite the overall topic is relevant to understand key aspect of stem cells and embryo development, I have found several flaws in the manuscript (stated below) that, in my opinion, prevent its publication in its current form:

1. Many of their conclusions seem to be based on the qualitative analysis of a single image (e.g. Figures 1D-G, Fig 2G, Supplementary Figure 2). The authors should provide quantitative information regarding these analyses and indicate the number of cells/replicas collected for each experiment.
2. Many of the images seem to require a flat-field correction. Could the authors check that the illumination is homogeneous? This artifact could affect the data analysis.
3. The actin ring surrounding hESCs colonies was previously described by Närvä et al. Although the authors cited this previous work, they do not discuss in deep the differences and similarities with their observations.
4. There are many experimental details missing that are extremely relevant to fully understand the experiments and evaluate the robustness of the analyses (e.g., microscopy setup, fluorescent probes used for immunostaining, incubation conditions with the inhibitors SMIFH2 and CK666).
5. The qualitative observation of Figure 3F suggests a lower overall YAP levels in primed and +CK666 cells in comparison to naive cells. Could the authors check if this is correct and, if this is the case, explain the observation?
6. The authors should discuss deeper the rationale of the pan-ERM immunostaining experiments (since they used the individual antibodies afterwards) and provide a brief discussion of their results and, in particular, the colocalization with moesin but not with ezrin or radixin.

Minor observations:

1. The Introduction makes the reader think that actin is the only cytoskeletal network involved in embryo development and stem cell properties. They should also include a brief discussion on the relevance of the other cytoskeletal networks in mechanotransduction and cell fate decisions.
2. There are many abbreviations that are not defined in the text and are extremely specific to the field.
3. Could the authors explain the selection of the pluripotency markers studied by qPCR? Specifically, why they studied DNMT3L, DPPA3, KLF2, and KLF4 (Fig. 1B) and the different set PECAM1, ESRRB, KLF4, and DNMT3L in Fig. 2B.
4. Figures 1G and 2G, please include the images of the colonies.

Significance

The manuscript analyzes the formation of the actin ring that surrounds naive but not primed colonies of human embryonic stem cells (hESCs). The authors claim that the formation of this actin ring requires Arp2/3 which also modulates YAP localization. Despite the overall topic is relevant to understand key aspect of stem cells and embryo development, I have found several flaws in the manuscript (stated below) that, in my opinion, prevent its publication in its current form (see Evidence, reproducibility and clarity)

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Referee #2

Evidence, reproducibility and clarity

Summary:

This paper describes the involvement of the actin regulator Arp2/3 in the dedifferentiation of primed human embryonic stem cells (hESCs) into naive pluripotency. The authors initially demonstrated a reorganization of the actin cytoskeleton during the transition to naive pluripotency, which included the formation of a contractile actin ring at the colony periphery. Actin reorganization was also associated with a reduction in cell-substrate traction forces and an increase in cell-cell junction traction forces. The authors showed that the activity of the Arp2/3 complex was required for actin reorganization and acquisition of a naive pluripotent state. RNA-seq analysis revealed that the Arp2/3 complex regulates Hippo signaling. Furthermore, inhibition of Arp2/3 suppressed the nuclear localization of YAP, and expression of nuclear-localized YAP restored naive dedifferentiation of the Arp2/3 inhibited hESCs. Based on these results, the authors have proposed a model in which naive pluripotency is characterized by Arp2/3 complex-dependent remodeling of the actin cytoskeleton and colony mechanics. Additionally, it has been suggested that Arp2/3 activity facilitates naive dedifferentiation by promoting the nuclear translocation of YAP.

Major comments:

The experiments were of high quality, and the paper was clearly written with these major conclusions being supported by the experiments. However, the three-dimensional (3D) organization of F-actin, including the actin ring surrounding naive colonies, is unclear.

1. The authors found that a ring of actin filaments at the colony periphery was characteristic of the naive hESCs. However, because all the data are presented as an image of a single confocal section, the 3D organization of the actin filaments is not clear. Although the authors drew a scheme for this actin ring being located in the apical domain of polarized cells, such data have not been provided in the manuscript. Since naive hESCs form dome-like colonies, it is important to show the 3D organization of actin filaments in the colony. 3D reconstruction of confocal microscopy images of the naive hESC colonies is required to show the relationship between actin filaments, adherens junctions, and the nuclei (as a reference for the Z axis). If 3D reconstruction is not technically possible, confocal images at different Z levels and maximum projection images should be obtained and provided.
2. Some of the statistical analyses were inappropriate. The authors have used Student's t-test for all analyses,; however, one-way ANOVA and post-hoc analysis must be used to compare three or more groups (Figs. 2B, D, E, 3G, 4B, D, E).

Minor comments:

1. Page 9, second paragraph. In the discussion section, authors have written that "Cells within the ICM of mouse blastocysts exclude YAP from the nucleus whereas cells within the ICM of human blastocysts maintain nuclear YAP." However, a recent study has reported that the ICM/epiblast of mouse late blastocysts also express nuclear YAP.

Epiblast Formation by TEAD-YAP-Dependent Expression of Pluripotency Factors and Competitive Elimination of Unspecified Cells. Hashimoto M, Sasaki H. Dev Cell. 2019, 50:139-154.e5. doi: 10.1016/j.devcel.2019.05.024.

Significance

The importance of actin dynamics and cell mechanics as regulators of cell fate transition has been demonstrated in several systems, including the differentiation of hESCs (ref 54). The importance of YAP in the generation of naive hESCs has been reported previously (24). This study further extends this knowledge by showing the importance of actin dynamics and cell mechanics during the naive dedifferentiation process of hESCs. Although the advancement is not significant, the identification of the Arp2/3 complex as an essential upstream regulator of actin dynamics, cell mechanics, and YAP provides novel and important information for the field of stem cell biology, specifically for researchers working on hESC reprogramming and regenerative medicine.

The field of expertise of this reviewer is mouse preimplantation development and Hippo signaling.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Meyer et al., shows that the transition from primed to naïve human Embryonic Stem cells is associated with changes with the organization of the actin cytoskeleton, mechanics exerted on the substratum and YAP activity. These changes require Arp2/3 activity and if these changes are blocked with an Arp2/3 inhibitor, the phenotype can be rescued by the expression of a constitutively active YAP form.

This brief manuscript is overall well written and presented. The results are quite original, since branched actin polymerized by Arp2/3 is generally associated with membrane protrusions, and not with contractile actin fibers, as described here. Similarly, YAP activation has been shown to be regulated by RhoA-mediated contractility and here seems to depend on branched actin networks. I have nothing against these provocative conclusions, but I believe that to make their point stronger, more than just the use of an Arp2/3 inhibitor is required.

Major Comments

1. The results of experiments where Arp2/3 is blocked (Fig.2) should be confirmed by Arp2/3 knock-down and with an independent Arp2/3 inhibitor. Several are available (CK-869, Benproperine, Pimozide). For Fig.3 and 4, that would not be necessary, but to establish the specificity of the effect in fig.2 this is absolutely required.
2. I believe that the status of the actin cytoskeleton in both states is not well enough characterized. This is especially obvious for branched actin networks themselves that depend on the Arp2/3. To this end, the authors may localize Arp2/3 or cortactin, a useful surrogate that often gives a better staining. This point is particularly important since contractile fibers are not made of branched actin. Myosin cannot walk or pull along branched actin networks because of steric hindrance. It might well be that branched actin networks are debranched after Arp2/3 polymerization. I suggest staining tropomyosins that would indicate where the transition between branched and unbranched actin would be. Along this line, phosphoERMs should be localized and revealed by Western blots (we expect an increase from primed to naive state) because they cannot perform the proposed function of linker between the membrane and actin filaments if they are not phosphorylated.
3. Branched actin is required for cell cycle progression and cell proliferation in normal cells. This requirement is lost in most cancer cells (Wu et al., Cell 2012; Molinie et al., Cell Res 2019). This would be really important to know whether ESCs stop proliferating upon CK-666 treatment. In other words, do they behave like normal cells or transformed cells. Proliferation is a major function that depends on the YAP pathway. Cell counts and EdU incorporation can easily provide answers to this important question.

Minor comments

1. Fig2F: non-representative pictures or wrong quantification of the CK666 condition.
2. Fig3A: Y-axis ? What is it ? How is it adjusted ? -Log P ?
3. Colors of dots not really visible.
4. What about the rescue of cell morphology ? Does active YAP restore the intercellular contractile bundle ?
5. Typos: Apr2/3 in the abstract, Hoeschst in Fig.S1B.

Significance

This brief report would be a strong report if the major points are addressed. The conclusions are original, with a role of branched actin in inducing an intercellular contractile bundle and activating YAP, and important for a cell system of importance, human ESC. It would interest a wide variety of readers with either an interest in the actin cytoskeleton or in stem cells.

I believe that the time required to address these 3 points is reasonable in the order of 3 months only.

My expertise is the actin cytoskeleton.

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Reply to the reviewers

1. General Statements

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

2. Point-by-point description of the revisions

Reviewer 1

Summary

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

Major Comments

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Minor Comments

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

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

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

We have revised this sentence.

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

We have now cited this paper in the Introduction.

Significance Comments

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

See reply to Major Comment 3 above.

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

See reply to Major Comment 6 above.

Reviewer 2

Major Comments

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

Thank you.

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

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

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

We have added justification for our choices.

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

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

Reviewer 3

Summary

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

Major Comments

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

Thank you.

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

Thank you.

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

Thank you.

Minor Comments

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

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

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

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

Significance Comments

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

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

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

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

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

See reply to Significance Comment 3 above.

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Referee #3

Evidence, reproducibility and clarity

Summary

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

Major comments:

1. The key conclusions are convincing, as the authors demonstrated LimoRhyde2's ability to fit non-sinusoidal rhythms and prioritize high-amplitude rhythms over monotonic rhythms with high signal-to-noise ratios. This is shown by the comparison with BooteJTK, a popular method in the field, and by the analysis of real circadian transcriptome data from mouse tissues. However, the authors acknowledged some limitations that could impact the method's broader applicability.
2. Data and methods are presented in a reproducible manner, with detailed descriptions of the periodic spline-based linear models, the use of Mash for moderating raw fits, and the calculation of rhythm statistics. This information is sufficient for other researchers to replicate the study and apply the LimoRhyde2 method to their own datasets. The code is available already.
3. Adequate replication and statistical analysis are provided, with the authors analyzing the same datasets using both LimoRhyde2 and BooteJTK to compare their performance. The use of Spearman correlation to assess the relationship between the adjusted p-values from BooteJTK and the amplitudes from LimoRhyde2 further supports the statistical rigor of the study.

Minor comments:

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

Significance

1. This study represents a technical advance in the field of genomic analysis of biological rhythms by introducing LimoRhyde2, a method that prioritizes high-amplitude rhythms and directly estimates biological rhythms and their uncertainty. The method's ability to capture non-monotonic rhythms and account for uncertainty makes it a valuable tool for researchers interested in understanding circadian systems and their physiological impact.
2. The work is placed in the context of existing literature, as the authors compare LimoRhyde2 with BooteJTK, a refinement of the popular JTK_CYCLE method. The comparison highlights the differences in output, prioritization, and runtime, demonstrating LimoRhyde2's potential advantages over traditional methods in the field.
3. However, BooteJTK is relatively underused compared to many other methods, partly because of the difficulty and time required to run the analysis. The paper would be improved by comparing LimoRhyde2 to JTK_Cycle itself, as well as RAIN and ARSER. The latter are the most commonly used methods for rhythm detection, and thus the value of the paper's findings would be far greater by comparing to these methods. Like LimoRhyde2, they are also not resource-intensive to run.
4. LimoRhyde2's ability to efficiently prioritize large effects with functional significance in the circadian system can provide valuable insights for these researchers and advance the understanding of biological rhythms. The LimoRhyde2 approach is different to conventional reliance on arbitrary p- or q-values, which are taken as almost sacrosanct in the field as a measure of a dataset's worth. LimoRhyde2 could thus help to change this false perception of how to rate a circadian rhythm, which has particularly been ushered in by a reliance on JTK_Cycle p- and q-values as the method of choice for assigning meaningfulness to rhythms. Unfortunately, JTK_Cycle is very conservative and is limited to detecting sinusoidal-type rhythms. LimoRhyde2 could overcome these limitations (as RAIN does too) if widely adopted. However, to do this, it must be compared to things like JTK_Cycle directly.

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Referee #2

Evidence, reproducibility and clarity

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

Significance

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

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

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

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

Summary:

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

Major Comments:

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

Minor Comments:

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

Significance

General assessment:

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

Advance:

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

Audience:

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

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Referee #2

Evidence, reproducibility and clarity

In this report, Bilgic and colleagues study the diversity of progenitor cell types in the developing ferret cerebral cortex, a valuable in vivo model to understand cortex expansion and folding, as in primates including human. Using a single-cell transcriptomics approach, they describe a diversity of progenitor cell types and their interrelation by transcriptomic trajectories, which are conserved but biased as development progresses. Most interestingly, they identify in ferret a type of cell only identified in human before, tRG, which they then characterize throughoutly by transcriptomics. They also identify these cells in histological sections, and via time-lapse videomicroscopy they characterize their cell type of origin. They also provide indirect evidence that tRG may be the source of ependymal cells in the ventricle of the mature cerebral cortex, as well as astroglial progenitor cells. Finally, they extend their analyses to identify oRG in ferret based on previous human single cell data, concluding that they have in ferret a quite different transcriptomic profile than in human.

Major issues:

The authors must provide evidence that the cortical area they are examining will give rise to Somatosensory cortex. Their sampling area appears more like Cingulate cortex, while somatosensory may be a bit more lateral. The cingulate cortex is a very unique region, with some unique characteristics including lamination and connectivity. It would be important to provide some justification as to why they chose this particular part of the cerebral cortex, and keep this into consideration when discussing the general value of their findings.

It seems that the single cell datasets were collected from only 1 replica at each developmental stage. Current best practice sets the inclusion of several biological replicates. Whereas this represents multiplying the workload (and costs) and re-doing many of the analyses, it is currently highly valued. On the other hand, the authors already have their analysis pipelines defined, and so the time involved should be much shorter than before.

Single cell QC methods are incomplete as described in Methods. It is key to consider the relative abundance of mitochondrial RNAs when assessing the integrity and validity of cells, and thus a key criterion to select the cells for clustering analysis. The criteria for the selected choice of clustering resolution is also missing.

When first describing tRGs (line 171), orthogonal views of the image z-stacks must be shown to demonstrate the full morphology of these cells. The basal process might have been cut during tissue sectioning. The same applies to images in Fig. 2C, 2D, S3A.

In Figure 3, the authors perform time-lapse imaging to visualize and characterize the cells and lineage that give rise to tRGs. While very nice and a technical challenge that must be properly acknowledged, they unfortunately only obtained a total of three examples, which is clearly insufficient to reach any meaningful conclusion on this respect. These conclusions, while fascinating, are based only on 3 cell divisions. If this is to be taken as a strong argument for the conclusions of the study, the authors must obtain. If the authors want to make a solid statement out of this experimental approach, they must obtain a sufficient amount of additional data, which will depend on the variability of the results they find.

Still regarding the time-lapse results presented in Figure 3, it is unclear why after first division the authors identify the blue cell as IPC, when it has the exact features of tRG: apical process anchored in VZ surface + short basal process. This is applicable to all three examples shown. For example, the authors describe: "the mother IPC of tRG also possessed both an apical endfoot and a short basal fiber (Fig. 3D)". Why is this identified as IPC, when it looks exactly like vRG, NOT as an IPC? The interpretation of IPCs being the mother cells to tRGs must be changed, to those being vRGs. Or else, more convincing data must be provided. In fact, their analyses in Fig 4A contradict their interpretation on tRG mother cells, showing that the transcriptomic trajectory leading to tRGs does not inlcude Eomes+ cells, accumulated in the neurogenic state 2. At the end of this section, the authors indicate: "our data suggest that tRG cells are formed by apical asymmetric division(s) from unique apical IPC with a short basal fiber (Tsunekawa et al, in preparation).". Being as important as this point is, if there is solid supporting data the authors must include it in this study.

Alternative interpretation of time-lapse images (lines 196-197): maybe a tRG can generate one tRG CRYAB+, and one IPC CRYAB-.

Arrows in Fig 5E are shifted between the top and bottom panels. There is no obvious evidence of mitosis visible. This should be unequivocally labeled with anti-PH3 antibodies.

Line 277: "Transcriptomic trajectories were homologous across the two species". What does this refer to? What are these trajectories? Pseudotime? Is this statistically tested?

When comparing tRG cells between ferret and human, the authors indicate a remarkable similarity between the two species as represented by CRYAB, EGR1, and CYR61 expression. As shown in Fig 6E, EGR1 and CYR61 are not expressed selectively in human tRG as they clearly are in ferret tRG. Hence, this argument is not valid.

In the last part, the authors try to identify oRG-like cells in ferret by comparison with their transcriptomes identified in human. For this, they decide to call ferret oRG-like cells those that are near human oRGs in the integrated UMAP, as identified in a previous human study. What was the criterion for this? How much near is "near"? The fact that the selected cells have higher oRG scores is expected and obvious, as these cells were selected precisely based on their proximity in the UMAP. Even more importantly, the identification of oRGs in the human study is not unambiguous. Therefore, the correlate in ferret cells is also non-conclusive as to the identity of such cells.

Discussion is surprisingly short, given the emphasis that the authors place on the importance of their findings. I would suggest extending it for a better coverage of those findings that have the greatest relevance and interest to a wider readership.

In Discussion, the authors state that "ferret (and presumably also human) tRG cells differentiate into ependymal cells and astrogenic cells." Again, this conclusion is purely based on transcriptomic trajectories, which must not be confused with cell lineage. This sentence must be rephrased and toned down accordingly.

In Discussion: "our cross-species analysis highlights the notable role of tRG as progenitors contributing to the formation of the ependyma and white matter". As mentioned above, this is only based on transcriptomic trajectories, it is not demonstrated in this study. In vivo analyses of cell fate are needed to support this conclusion, and a more extensive videomicroscopy analysis is needed to confirm the cell lineage progression suggested by transcriptomes.

Minor issues:

In line 59, the authors state: "cerebral carcinogenesis independently evolved to gain an additional germinal layer (outer SVZ (OSVZ);". Assuming that they mean "cerebral neurogenesis", what is the evidence for this independent evolution? Original publications demonstrating this must be cited.

Lines 60-61, the third key publication reporting the existence of bRG must be cited together with Hansen 2010 and Fietz 2010: Reillo et al., 2011, Cerebral Cortex.

When introducing ferret as an interesting or important animal model, suitable original studies should be cited.

In Figure 2F-H, layer borders should be labeled. The density of CRYAB+ cells in VZ (?) at P5 seems much greater in Fig 2E,F than in Fig. 2B. Clarifying this discrepancy is important to validate the quantification of Fig 2D.

Co-expression of CRYAB and FOXJ1. In Fig 5B this must be demonstrated with merged channels.

Line 247: "near which nuclear line aggregates are observed more frequently (Fig. 2B)". It is very much unclear what the authors refer to. Please, define nuclear line aggregates.

There are a number of typos along the main text and figures, which must be fully checked and corrected. For example, line 59 "cerebral carcinogenesis"; also in Figure S4, Figure 5E. Labeling of graphs in Fig 5C is wrong. The plots present the fraction of CRYAB+ cells that express FOXJ1 (FOXJ1+/CRYAB+ cells), not the reverse.

Significance

This manuscript is of interest for being the first ferret single-cell study, and for identifying and characterizing to a great extent a unique population of cortical progenitor cells that so far had only been observed in human. The study is presented as a resource for studies of ferret cortex development, which as such is clearly of interest to a very limited audience. A more appealing perspective might be if this study in ferret is of interest or of use to the more general community studying cortex development, or even maybe cortex evolution.

Advance: it is, so far, the first study of single cell profiling of the ferret cerebral cortex, a well established and highly valued model of gyrencephalic mammals, and a suitable best-alternative to work in primates. In addition to the technical advance, providing a new resource for work in ferret, it shows for the first time the existence of truncated Radial Glia (tRG) in a non-human cortex, and even more importantly in this model, strengthening even more its value.

This study as is presented will be of most interest to a specialized audience, those directly working with ferret. Nevertheless, it will also be of conceptual interest to the community of cortex development and evolution for the concepts that one can extract on cell type conservation.

My expertise: cerebral cortex development, brain evolution, ferret, cortex folding, neurogenesis, progenitor cell lineage, transcriptomics of developing brain

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Referee #1

Evidence, reproducibility and clarity

Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

In this manuscript, the authors conduct a series of single-cell transcriptomic analyses and imaging assays in the developing ferret cortex suggesting that (1) ferrets harbor a radial glia (RG) subtype similar to the truncated radial glia (tRG) described previously in humans that may have the potential to (2) produce ependymal and astrogenic lineages which (3) can also be found in the developing human cortex. These findings appear to be an important step in the validation and development of the ferret model towards a tool that can be used to study tRG cell biology, a feat currently difficult due to the inaccessibility of a genetically tractable source of tRG for molecular and cell biology experiments.

Major comments:

• Are the key conclusions convincing?

I found the key conclusions described above and in the authors' abstract convincing. I found the identification of a distinct, tRG-like cell type from the authors' single-cell transcriptomic analysis of the ferret cortex compelling, particularly because (1) the expression of the previously utilized tRG marker gene CRYAB is specific to the tRG-like cluster and (2) the tRG-like cluster marker genes (including CRYAB) are relatively unique to the tRG-like cluster. I found this strengthened by their morphological analyses showing the tRG-characteristic apical endfoot and short basal process in these CRYAB+ cells in the ferret cortex. I found the combination of imaging and bioinformatic analyses showing the increase in FOXJ1 co-expression in CRYAB+ cells to compellingly suggest that CRYAB+ cells can produce FOXJ1+ ependymal cells, and similarly with the authors' analyses to suggest that tRG-like cells can also contribute to SPARCL1+ astrocyte cells. I found that the cluster score analyses compelling suggest that the tRG-like cells in the ferret dataset correlate with the tRG cells annotated in a separate, human developing cortical dataset. I also appreciated the comparison of astroglial, ependymal, and uncommited ferret tRG sub populations from the pseudo time analysis with the clusters generated from the integrated ferret-human dataset in Fig. 7.<br /> - 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.

The weakest claim in the paper is lines 202: "...tRG cells are formed by apical asymmetric division(s) from unique apical IPC". From my understanding, the main evidence that the tRG parent cells shown in Fig. 3 are not tRGs are the data from Fig. 2E-G showing the low amounts of CRYAB+ cells co-expressing KI67, TBR2, or OLIG2 in P5 and P10. Especially given that these timepoints are after those used in Fig. 3, I believe further evidence is needed to confirm the cell type identity of tRG parent cells in Fig. 3. Such experiments (isolating IPCs from ferret cortex and growing in vitro to determine progeny cells) may be outside of the scope of this paper, in which case I believe the text can be strengthened with either (1) presenting the data from the cited Tsunekawa et al, in preparation that would suggest this claim or (2) rephrasing these claims to omit the mention of IPCs.

I also believe the claim in Line 365-366 is overstated: "We found that ferret (and presumably also human) tRG cells differentiate into ependymal cells and astrogenic cells." While I believe the transcriptomic comparisons suggest the presence of uncommitted tRG in both the ferret and human datasets, I would appreciate further analyses to confirm the prevalence of astroglial and ependymal tRG in the humans and/or functional analyses before claiming that human tRG cells make ependymal and astrogenic cells. I appreciate the authors' note that "GW25 is...the latest stages experimentally available" (line 376-377), but their comparative approaches could be applied to existing datasets of the human cortex (Herring et al., 2022, PMID: 36318921) that span later developmental ages. Identifying the presence of astroglial and ependymal tRGs in this and/or similar datasets would provide more convincing evidence of the tRGs' developmental potential. If this computational analysis is outside the scope of the paper, I believe paring the certainty of these claims (especially lines 379 - 383) and recognizing the need for further functional analyses would negate the need for deeper mechanistic validation.

I believe the most significant advance for this paper is the potential to use ferret tRG cells to model those of the human brain. However to support this claim (see Lines 83-84), I believe a comparison of the ferret tRG cells with existing cortical organoid datasets (Bhaduri et al., 2020, PMID: 31996853) would be helpful. If cortical organoids currently lack the presence of tRG cell types, that would strengthen the importance of the ferret model and the findings of this paper - otherwise, I feel that the use of the ferret model needs to be justified in light of the greater accesibility and genetic tractability of the cortical organoid system. - 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?

I found the total number of tRG-like cells in the ferret dataset quite small (162), but I understand the difficulty with isolating and sequencing rare cell types from primary tissue sources. I believe most of the transcriptomic analyses were conducted with this low n in consideration, but this caveat is even more reason to pare down the wording for the weaker claims mentioned above. - Are prior studies referenced appropriately?

I found it interesting that tRGs persist and even expand in number in postnatal timepoints (Fig. 2C). I'd be interested to know if this is in line with what is known in human developing cortex. If so, it would strengthen the conclusion that ferret tRGs can model that of humans - and if not, this would either be an important finding regarding tRG function or an important caveat in the use of ferret tRGs to model the cell type in humans. - 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?

For Fig. 2A, I would find it helpful to compare the morphology of GFP+/CRYAB+ cells vs GFP+/CRYAB- cells, with the hypothesis that GFP+/CRYAB- cells will have elongated basal processes. I believe this could be done by finding GFP+/CRYAB- cells in the raw images obtained to generate Fig. 2A (or similar), and showing those cells in an adjacent panel. This side-by-side comparison could provide more support that the CRYAB+ cells from the single-cell analyses are indeed specifically linked to tRG-like morphology.

Significance

This paper primarily presents a technical advance in the field, showing that tRG cells that can model those found in the developing human cortex are found in the developing ferret cortex.

• Place the work in the context of the existing literature (provide references, where appropriate).
• State what audience might be interested in and influenced by the reported findings. Several studies in the human and macaque brain have identified the presence of tRGs (deAzevedo et al., 2003; Nowakowski et al., 2016), but understanding the molecular functions and development of these cells - and many human-specific cell types in the brain - is difficult due to the lack of tractable models of human neurodevelopment. Ferrets, given their layered cortices, may be a potential model system for these cell types, but further analyses to determine their transcriptomic similarity to the developing human cortex and their ability to recapitulate human cell types are required in order to evaluate their use as a model system. By generating a useful resource in the ferret single-cell transcriptomic atlas, this study provides evidence that - at least for the tRG subtypes - ferrets may be useful in dissecting the generation and functional importance of tRG cells. With the caveat that a direct comparison with the use of cortical organoids to study tRG is lacking in this paper (see above), I believe this work can provide useful insight into the field's current search for model systems to functionally interrogate human-specific aspects of cortical development.
• 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.

Single-cell transcriptomic profiling of primary developing human cortex and cortical organoids

Did not have sufficient expertise in: - Ferret biology

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Reply to the reviewers

Manuscript number: RC-2023-01910

Corresponding author(s): Michael W. Sereda

1. General Statements

Reviewer #1:

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

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

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

Reviewer #2:

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

We thank Reviewer #2 for this positive evaluation.

Reviewer #3:

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

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

2. Description of the planned revisions

Reviewer #1

Regarding the activity of PTEN

Figure 1

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

Figure S1

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

Figure 5

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

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

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

Reviewer #1:

Figure 1

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

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

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

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

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

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

Figure 2:

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

Figure 3

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

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

Figure 4

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

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

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

Figure 5:

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

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

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

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

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

Figure 6:

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

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

Figure 7:

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

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

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

Reviewer #2:

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

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

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

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

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

Reviewer #3:

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

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

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

Reviewer #1:

Figure 1:

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

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

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

(Figure 2, Figure 4 and Figure 5e)

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

Figure 3:

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

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

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

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Referee #3

Evidence, reproducibility and clarity

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

Significance

These data are significant, since they would provide new targets for treating inherited neuropathy associated with altered PLP22 gene dosage.

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Referee #2

Evidence, reproducibility and clarity

This study investigates the modulation, both genetically and pharmacologically, of the PI3K/Akt/mTOR signaling in preclinical animal models for the inherited peripheral neuropathies HNPP and CMT1A. These conditions result from a gene dosage abnormality of the peripheral myelin protein gene PMP22. The exact biological molecular mechanisms remain enigmatic despite it having been over 30 years since the major genetic lesions, the CMT1A duplication and HNPP deletion, were described. With respect to myelin biology one observes focally slowed nerve conduction at pressure palsies and local/segmental hypermyelination in HNPP whereas hypomyelination occurs in CMT1A.

The study is nicely conducted, data illustrations very informative, and writing clear and concise. This paper will likely be of great interest to your readers. A few things the authors may want to consider:

1. Regarding in the Introduction: "...the molecular mechanisms causative for the abnormal myelination remain largely unknown and still no therapy is available." Suggest consider modifying to perhaps: '...no small molecule or pharmacological therapeutic intervention exist.' To say "no therapy" exist is 'myopic' and untrue.
2. Suggest adding question mark to end of sentence or changing 'asked' to "investigated" for following thought: "Here, we asked whether PI3K/Akt/mTOR signaling provides therefore a therapeutic target to treat the consequences of altered Pmp22 gene-dosage."
3. Rather than attempt to establish PRIORITY perhaps 'softening' the INTRODUCTION concluding statement "Our results thus identify a potential pharmacological target for this inherited neuropathy.
4. [This makes thePI3K/Akt/mTOR pathway a promising target for a preventive treatment of affected nerves also in human patients.] Does this belong in RESULTS? Or rather DISCUSSION?

Significance

The authors provide convincing evidence that the HNPP pathobiology is ameliorated by PI3K/Akt/mTOR inhibitors. Interestingly they found radial myelin growth was most affected by this approach and suggest an interesting transdermal approach in injured nerves in the acute prevention of pressure palsies.

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Referee #1

Evidence, reproducibility and clarity

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

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

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

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

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

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

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

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

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

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

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

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

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

Significance

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

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Reply to the reviewers

Reviewer 1:

• *

I am not an expert in algal ultrastructure or TEM, and I principally found this manuscript informative and well-written. I can only make minor recommendations, although I urge the Editors to supplement this review with others from specialists within the field.

We thank the reviewer for their positive comment on the manuscript as well as for the interesting following discussion points.

To date, to my knowledge, the Pentapharsodinium chloroplast has not been characterised at a molecular level. The placement of the nuclear lineage within the Peridiniales as a close relative or Durinskia spp. and other dinoflagellates with diatom endosymbionts raises the question of whether Pentapharsodinium possesses a peridinin-containing chloroplast, per most other dinoflagellates, or possesses a chloroplast of an alternative endosymbiotic derivation, although I suppose the single chloroplast would be typical for peridinin-containing chloroplasts from the Peridiniales. __Can the authors make any inference on this from their data? __

In the course of this study, we did not perform molecular characterization of the chloroplast. Therefore, formal answer to this question would not be possible based on our data.

However, we have evidence that suggest that the chloroplast from P. tyrrhenica does not come here from a diatom endosymbiont.

1/ In the suggested cases of diatom endosymbiont origin of the chloroplast, eg in the genus Durinskia, Yamada et al., 2019 show that Durinskia capensis or Durinskia kwazulunatalensis can present diatom organelles such as chloroplast, mitochondria, nucleus, or their remnants for a certain amount of time after uptake. The detailed analysis of our vEM data does not show these diatom organelles, thus ruling out the hypothesis.

2/ Additionally, the eyespot of dinoflagellate species possessing diatom association seems to be characteristic to these cells (Horiguchi., 2007, Hoppenrath et al., 2017). In our case, the eyespot of P. tyrrhenica corresponds to a distinct type (type IA, thought to be in peridinin dino-chloroplast according to Hoppenrath., 2017), that varies from the one observed in Durinksia baltica, or other dinoflagellates species possessing these diatom associations (Horiguchi., 2007, Hoppenrath et al., 2017).

Therefore, the chloroplast of our cell does not seem to be acquired from a diatom. However, as we don’t have molecular evidence at this stage, and are not able to perform such analyses, we prefer not to address this question in the manuscript.

While I appreciate that this is a study of a single cell only, I would prefer some more extensive evidence that the partial chromosome unfolding identified correlates to transcriptional activity. The nucleolus is surrounded by a layer of heterochromatin and perhaps the filamentous structures involved are transcriptionally quiescent. Were the authors able to take any preliminary images of cells harvested mid-day or exposed to higher light intensities, and do they see greater chromatin unfolding in this case? Similarly I would be curious if cells visualised later in the day possess multiple rather than single chloroplasts.

Our description is here based on one microorganism of very low abundance, and we do not have data for it across conditions. Therefore, we would not be comfortable inferring too many details in this paper and will thus modify the text in order be more careful about the potential role of these fibres and their putative association to transcription. We are planning to address this interesting point in the future, in a more biologically focused paper in preparation. Nevertheless, similar structures have been described protruding in the nucleoplasm in other species (Soyer., 1981, Bhaud et al., 2000, Decelle et al., 2021) and have been suggested to be associated to RNA transcription (Sigee., 1983). We will make sure to cite and discuss more literature on this point.

Line 39: should be "dinoflagellate biology" <br /> Line 131: "a far red signal" <br /> Line 196: should be "number of chloroplasts"

We thank the reviewer, the errors will be corrected in the revised version.

Line 200: by curiosity, how does the measured chloroplast volume compare to those computed in vEM studies of Symbiodinium (c.f., Uwizeye 2021)

The measured chloroplast volume in our cell differs to those computed in Symbiodinium in Uwizeye et al., 2021. Indeed, in Uwizeye et al., 2021, the chloroplast represents 30% of the cell volume. This is more than in our cell for which the chloroplast represents only 9.5% of the cell volume. However, these two cells are different species and come from different growth conditions (culture VS environment). These factors potentially contribute to morphometric variations as the environment possesses different types and amounts of nutrients and light resources.

Line 221: how does the number of observed chromosomes compare to estimated chromosome numbers in dinoflagellates from karyotyping or whole-genome sequencing?

To our knowledge, there is a wide variability in terms of number of chromosomes observed between dinoflagellate species. Bhaud et al (2000) reports the presence of between 4 and 200 chromosomes depending on the species. Unfortunately, we did not find information concerning the number of chromosomes for this species to compare with our analysis. However, we are planning in the revised version to discuss how our workflow is complementary to other methods such as genomics, transcriptomics and light microscopy towards better understanding of marine organism.

Line 240: does the eyespot show any proximity to the mitochondria, as per the hybrid chloroplast/ mitochondrial-derived eyespots found in Warnowiacean dinoflagellates?

In our study the eyespot is composed of pigment globules, organized as a sheet, located inside the chloroplast and facing towards the theca. This type of arrangement seems to be distinct to the chloroplast/mitochondria-derived eyespot described in Warnowiaceae (Colley and Nilson., 2016). Additionally, for the revision of this paper we will further segment the mitochondria to investigate any potential proximity to the eyespot. We will also put the eyespot of P. tyrrhenica in context with other types described in the literature.

Reviewer #1 (Significance (Required)):

The application of vEM to environmental algal samples has to my knowledge not been attempted previously. If these approaches could be scaled up to a multi-cell approach and is not completely destructive to the cells, it could provide a fascinating way to connect algal morphology in the wild to other culture-free methods to understand algal biology (e.g., meta-barcoding).

We would like to address the interesting comment concerning the possibility to combine vEM along with other molecular tools to study organisms from a culture free method. While FIB-SEM is a destructive method, it could be used in combination with other methods and thus synergize towards the characterization of the environmental samples. We will add a few sentences in the discussion, as a forward look, as it represents indeed an important axis of our future research, where molecular taxonomy (e.g. metabarcoding) will be correlated to morphological characterisations. We believe such approaches will be useful beyond the study of micro-algae, and will make this point clear in the discussion.

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

This is avery important and interesting contribution to the ultrastructural analysis of one scientific species among many others living together in a rich sample as a marine microplankton. In addition the work also shows the possibility to obtain fundamental volumetric informations on the various structures and organelles. The work was well planned and executed and certainly represents a tremendous effort of the members of the group. It is clearly written, explaining each detail of the methodology necessary to the understanding of the whole work.

Reviewer #2 (Significance (Required)):

This a phantatis piece of scientific work where the authros were able to use the moderns three dimensional reconstruction technique possible using high resolution scanning electron to reconstruct one specific cell in a large population of heterogenous cells. The identification of one specific cell based on fluorescence images detected in a light microscopy was very important to present one new methodology to observed such types of cells. In addition to a detailed description of the strucutres and organelles found they were able to determne the area/volume occupies by each of them in cells. <br /> Therefore I strong recommend the acceptance of the manuscript as it is.

We thank the reviewer for their appreciation of our work.

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

# Summary --

The authors present a workflow to characterize a microorganism, dinoflagellate cell, from environmental samples by vEM. The workflow enables the identification of specific taxa of interest in a heterogenous environmental sample and allows correlative fluorescence and FIB-SEM acquisition. I see no major flaws with this study. The authors present a proof of principle pipeline for utilizing CLEM to explore the ultrastructure of microorganisms.

# Major comments --

What is not clear, is how highly reproducible this workflow is. For example, what is the time required for each sample? How manual vs automated is each step? While, the workflow is important and sound, it would be helpful for the reader to understand a little more about the variability and throughput. It doesn't need to be exhaustive, but further characterization of the workflow would significantly improve the impact of the manuscript and should be included. As a reader, it would be tremendously helpful to clearly state what is part of the preparation/imaging workflow and what is an application example of the workflow. If it is intended that the post-processing is also part of the workflow, there should be significantly more details provided into the segmentation and analyses processes.

We thank the reviewers for pointing this out. This workflow has been applied to several blocks and repeated imaging of a subset of species could be achieved with 100% success. We will show this in a follow up paper. Moreover, the same method has been applied for targeted FIB-SEM acquisition of samples expressing fluorescent proteins (Ronchi et al., 2021). Therefore, we believe our workflow is highly reproducible and robust. We are planning to address the concern on technical variability in our revised version, together with a better explanation of time scales and automated VS manual aspect of the steps that are used for this workflow. We will also add information concerning the segmentation.

# Minor comments --

As this study describes a workflow that was developed for identification and imaging of microorganisms, it would be highly beneficial to the reader to have a figure that shows each of the steps, end to end.

We thank the reviewer for this suggestion. We plan to add a supplementary figure that describes the workflow step by step.

It would also be helpful to add annotation labels and a scale bar to supplemental video 2.

We thank the reviewer for spotting this missing information. We plan to add annotation labels as well as a scale bar to the video S2.

Do the nonphotosynthetic species also have nuclear autofluorescence or is this just a trait of a subset of the photosynthetic species?

We thank the reviewer for this question. From our analysis, we can’t conclude that it is a trait of some photosynthetic species compared to non-photosynthetic ones. However, heterogeneous autofluorescence profiles, even though unexplained, represent a valuable tool to discriminate between cell types. We would like to further address this point in the manuscript that such fluorescence profiles, even though unexplained, can contribute to the identification of specific cell types.

Reviewer #3 (Significance (Required)):

# General assessment --

The authors present an important, yet missing, workflow for characterizing microorganisms from environmental samples using vEM and CLEM. A strength of the study is that it enables identification and selection of taxa in heterogenous samples. Using correlative, confocal imaging of both auto-fluorescence and transmitted light, the authors show that specific taxa can be identified and selected for according to the organism's photosynthetic and morphological properties.

We thank the reviewer for their positive comments.

To improve upon this, it could be useful for the authors to provide a list or table of potential organisms that could be selected for in this manner to exemplify the use cases of this protocol.

We thank the reviewer for their suggestion. We plan to add a supplementary figure with a gallery of different cells and their identification.

# Advance --

This study, while a proof of concept, is also one of the first examples of using vEM on environmental studies. The author's also present the potential value add of using CLEM, not just for selection purposes, but also more comprehensive identification and mapping of subcellular structures. While the workflow itself is incremental (and important), the application is quite novel.

# Audience --

Because the authors' study combines a vEM workflow and microorganism characterization, the potential audience is broad reaching. The workflow itself could be adapted to many different systems - beyond microorganisms - making it of use to several biological fields.

We thank the reviewer for their positive comments.

# Expertise --

vEM, CLEM, FIB-SEM, membrane trafficking, cell biology, tissue cell biology, machine learning

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Referee #3

Evidence, reproducibility and clarity

Summary

The authors present a workflow to characterize a microorganism, dinoflagellate cell, from environmental samples by vEM. The workflow enables the identification of specific taxa of interest in a heterogenous environmental sample and allows correlative fluorescence and FIB-SEM acquisition. I see no major flaws with this study. The authors present a proof of principle pipeline for utilizing CLEM to explore the ultrastructure of microorganisms.

Major comments

What is not clear, is how highly reproducible this workflow is. For example, what is the time required for each sample? How manual vs automated is each step? While, the workflow is important and sound, it would be helpful for the reader to understand a little more about the variability and throughput. It doesn't need to be exhaustive, but further characterization of the workflow would significantly improve the impact of the manuscript and should be included.

As a reader, it would be tremendously helpful to clearly state what is part of the preparation/imaging workflow and what is an application example of the workflow. If it is intended that the post-processing is also part of the workflow, there should be significantly more details provided into the segmentation and analyses processes.

Minor comments

As this study describes a workflow that was developed for identification and imaging of microorganisms, it would be highly beneficial to the reader to have a figure that shows each of the steps, end to end.

It would also be helpful to add annotation labels and a scale bar to supplemental video 2.

Do the nonphotosynthetic species also have nuclear autofluorescence or is this just a trait of a subset of the photosynthetic species?

Significance

General assessment

The authors present an important, yet missing, workflow for characterizing microorganisms from environmental samples using vEM and CLEM. A strength of the study is that it enables identification and selection of taxa in heterogenous samples. Using correlative, confocal imaging of both auto-fluorescence and transmitted light, the authors show that specific taxa can be identified and selected for according to the organism's photosynthetic and morphological properties. To improve upon this, it could be useful for the authors to provide a list or table of potential organisms that could be selected for in this manner to exemplify the use cases of this protocol.

Advance

This study, while a proof of concept, is also one of the first examples of using vEM on environmental studies. The author's also present the potential value add of using CLEM, not just for selection purposes, but also more comprehensive identification and mapping of subcellular structures. While the workflow itself is incremental (and important), the application is quite novel.

Audience

Because the authors' study combines a vEM workflow and microorganism characterization, the potential audience is broad reaching. The workflow itself could be adapted to many different systems - beyond microorganisms - making it of use to several biological fields.

Expertise

vEM, CLEM, FIB-SEM, membrane trafficking, cell biology, tissue cell biology, machine learning

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Referee #2

Evidence, reproducibility and clarity

This is avery important and interesting contribution to the ultrastructural analysis of one determoned species among many others living together in a rich sample as a marine microplankton. In addition the work also shows the possibility to obtain fundamental volumetric informations on the various structures and organelles. The work was well planned and executed and certainly represents a tremendous effort of the members of the group. It is clearly written, explaining each detail of the methodology necessary to the understanding of the whole work.

Significance

This a phantatis piece of scientiic work where the authros were able to use the moderns three dimensional reconstruction technique possible using high resolution scanning electron to reconstruct one specific cell in a large population of heterogenous cells. The identification of one specific cell based on fluorescence images detected in a light microscopy was very important to present one new methodology to observed such types of cells. In addition to a detailed description of the strucutres and organelles found they were able to determne the area/volume occupies by each of them in cells. Therefore I strong recommend the acceptance of the manuscript as it is.

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Referee #1

Evidence, reproducibility and clarity

I am not an expert in algal ultrastructure or TEM, and I principally found this manuscript informative and well-written. I can only make minor recommendations, although I urge the Editors to supplement this review with others from specialists within the field.

To date, to my knowledge, the Pentapharsodinium chloroplast has not been characterised at a molecular level. The placement of the nuclear lineage within the Peridiniales as a close relative or Durinskia spp. and other dinoflagellates with diatom endosymbionts raises the question of whether Pentapharsodinium possesses a peridinin-containing chloroplast, per most other dinoflagellates, or possesses a chloroplast of an alternative endosymbiotic derivation, although I suppose the single chloroplast would be typical for peridinin-containing chloroplasts from the Peridiniales. Can the authors make any inference on this from their data?

While I appreciate that this is a study of a single cell only, I would prefer some more extensive evidence that the partial chromosome unfolding identified correlates to transcriptional activity. The nucleolus is surrounded by a layer of heterochromatin and perhaps the filamentous structures involved are transcriptionally quiescent. Were the authors able to take any preliminary images of cells harvested mid-day or exposed to higher light intensities, and do they see greater chromatin unfolding in this case? Similarly I would be curious if cells visualised later in the day possess multiple rather than single chloroplasts.

Finally, I have a few (very) small grammatical corrections:

Line 39: should be "dinoflagellate biology"

Line 131: "a far red signal"

Line 196: should be "number of chloroplasts"

Line 200: by curiosity, how does the measured chloroplast volume compare to those computed in vEM studies of Symbiodinium (c.f., Uwizeye 2021)

Line 221: how does the number of observed chromosomes compare to estimated chromosome numbers in dinoflagellates from karyotyping or whole-genome sequencing?

Line 240: does the eyespot show any proximity to the mitochondria, as per the hybrid chloroplast/ mitochondrial-derived eyespots found in Warnowiacean dinoflagellates?

Significance

The application of vEM to environmental algal samples has to my knowledge not been attempted previously. If these approaches could be scaled up to a multi-cell approach and is not completely destructive to the cells, it could provide a fascinating way to connect algal morphology in the wild to other culture-free methods to understand algal biology (e.g., meta-barcoding).

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Reply to the reviewers

The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

The authors of this study utilize a novel nanobody-based technique to specify the location of the SPT complex to either the peripheral or nuclear membrane-associated endoplasmic reticulum membranes. Considering the potential importance of sub-ER compartmentalization on metabolic enzymes of the ER, this is a novel and useful approach. The studies are, with the minor exceptions noted below, comprehensive and very well executed and documented. The authors have combined genetic, proteomic, lipidomic, and flux experimental approaches to test whether sub-ER compartmentalization affects the function and regulation of the SPT complex. The results are, for the most part, negative, although there does seem to be some effect on the overall activity of the SPT complex as measured with flux analysis. Overall, while the authors do not detect dramatic effects on SPT complex localization, the technical advance using tethered nanobodies to direct complex localization, and the complementary approaches to testing SPT function and regulation, will be useful to workers in the sphingolipid field.

Minor points:

The results with YPK1-linker-CAAX are confusing. This construct does not result in Orm2 phosphorylation with heat shock, whereas endogenous YPK1 does. Yet it can support viability even without Orm deletion. In other words, this tethered construct appears functional in viability assays, but not in a biochemical assay.This discrepancy is not discussed by the authors. The manuscript would be improved by a discussion by the authors that addresses this issue. It is not clear why the figure legend to Figure 2 suggests that Ypk1 regulates Orms mainly in the peripheral ER. Considering that WT Ypk1 is more efficient than CAAX tethered YPK1, this statement does not seem supported. Perhaps the authors can elaborate on how they came to this conclusion.

The figures depicting Orm phosphorylation (Figure 1e, f Figure 2d,e, Figure 6 b,c) should be improved. The resolution of two forms is not sufficient in Figure1 and 2. The use of Phos-Tag might solve this issue. It would be helpful to the reader to include arrows that indicate the phosphorylated and unphosphorylated forms of Orm. Quantitation of these gels is essential.

Lines 318 and 319. Figure 6e and 6f are referred to. The correct assignment is 6f and 6g.

Referees cross-commenting

I agree with Reviewer #2's assessment that some of the conclusions are over stated. While Reviewer #2 is correct that the advances in this manuscript are modest, this is principally because expected differences in the function and regulation of the SPT in different ER sub-domains did not materialize. This may be disappointing, but is still important to document

Significance

This is a very well performed study, utilizing a variety of approaches to test whether localization of the SPT complex impacts on it activity and regulation. With very minor exceptions, it is well executed and documented.

The advances reported here are two-fold. First, the authors introduce a novel approach using nanobodies that are tethered to distinct regions of the yeast endoplasmic reticulum to localize intact and unmodified complexes to distinct locations. This could be a very useful tool in other contexts to examine the role of subcellular compartmentalization in the function of enzymes and signaling components. This targeting system is well characterized in this study. The second advance, utilizing this targeting system, is that localization of the SPT complex to distinct subcompartments of the ER has minimal effects on regulation, and observable, but relatively minor effects on SPT function in terms of sphingolipid production. While a positive result would have been more exciting, negative results can be equally informative.

This study will be of interest to workers in the signaling and metabolic fields that may utilize this unique targeting strategy. It will also be of interest to the sphingolipid community.

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Referee #2

Evidence, reproducibility and clarity

This manuscript uses a combination of immunoblotting, microscopy, and MS-based lipidomics to study sphingolipid synthesis in S. cerevisiae. The authors recently published a paper demonstrating that exogenous serine taken from the medium is preferentially used to generate LCBs. Given multiple levels of regulation of the SPT complex, the authors postulate that SPT in different sub-compartments of the ER could be differently regulated or at least have variable activities. Using a nanobody capture approach, they can restrict SPT activity to the peripheral ER and nuclear ER. Using this model, they investigate the role of Orm phosphorylation and SPT activity in response to 5-min heat shock. Phosphorylation does not seem to be a key element of the regulation. Ultimately, this is a collection of experiments without a clear story. In the end, the only take-home message I can find is that peripheral SPT is able to use exogenous heavy Serine as a substrate better than nuclear SPT.

Page 4. "We had previously demonstrated that increased de novo LCB biosynthesis is directly dependent on the uptake of exogenous serine through the general amino acid permease Gnp1. Consistent with our previous findings, deletion of GNP1 resulted in a blunted heat shock response, while deletion of the endogenous serine biosynthesis pathway (ser2) had no effect on LCB biosynthesis". This claim is too strong. If they feel this strongly, the authors should test a gnp1 agp1 double mutant. The alternative explanation is that to support the rapid increase in SPT activity, the Lcb1-Lcb2 enzyme use both a pre-existing cytoplasmic pool of serine and exogenous serine.

If cells are grown for 1 generation with heavy serine to label the cytoplasmic pool of serine and then cells as shifted to serine-free media and heat shock is induced is there any difference in LCB synthesis between allSPT, nSPT and pSPT?

It would be worth re-doing some of these experiments in rtn1 rtn2 yop1 yeast triple mutant (Stefan...Emr Cell 2011) or the delta super-tether mutant (Quon...Menon PLOS Biology 2016) both of which have substantially less cortical ER.

The authors make strong claims that are not supported by the data. Further, the presentation of the data is not optimal, and much of the data is qualitative, not quantitative. Too much of the data is presented as fold-change and i believe that the base-line LCB levels may change. The raw data should be included in a supplement excel file.

The blots of FLAG-tagged Orm1 and Orm2 are a critical part of this manuscript, but the data is not compelling in most figures. There is a lack of quantitation and replication. On the surface I agree with the authors that the phosphorylation is hard to align with the stimulation, but a more rigorous analysis is needed. Additionally, does the expression of an Orm2 mutant without the Ypk1 phosphorylation sites prevent the heat shock-induced increase in LCBs?

If this remains in the manuscript, the difference between ypk2 Ypk1-CaaX and ypk2 Ypk1-103aa-CaaX should be better highlighted in the main document. However, this whole course of experiments is problematic, and the authors' narrative changes to accommodate the findings; the arguments aren't internally consistent. Ypk is essential to regulate Orms. Ypk1-linker-CaaX can regulate Orms, Ypk1-linker can't increase Orm2 phosphorylation. Furthermore, a single prenyl group is not sufficient to restrict the localization of a protein. If there are other targeting motifs in addition to the last 4 amino acids this should be indicated. Ultimately, this is all negative data. Without a better interrogation of Orm phosphorylation it seems to have little value.

The "Orm proteins mediate SPT upregulation after heat shock" should be re-worded. The orm1 orm2 mutant already has a 25-fold increase in LCBs, and heat shock is unable to stimulate SPT activity any further. It suggests that heat shock is directly inhibiting Orm proteins which in turn removes the feedback inhibition on the SPT.

Figure 7b - the Y-axis scale needs to be corrected. A break should be inserted to alert the reviews of the scale's narrow range.

Is GFP-Orm1 and Orm2 functional? Both are more abundant in the nER than the peripheral.

Most papers I have read use "SL" as the abbreviation for sphingolipids, not SP. Consistency would be nice for readers.

Significance

The work appears technically sound but there are issues with the presentation of the data. Lack of raw data for the lipidomics, lack of quantitation.

The findings here are rather modest and much of the data is inconclusive or suggests certain pathways aren't involved rather than defining a clear mechanism.

This is an incremental finding that supports the 2020 PLOS genetics paper from the same authors. The target audience for this would be people interested in sphingolipid metabolism in yeast.

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Referee #1

Evidence, reproducibility and clarity

This is a nice paper showing that the intracellular location of the SPOTS complex affects SL de-novos synthesis. The experiments are well designed including a comprehensive set of controls. I just have a few minor points: It is hard for me to see the differences in ORM phosphorylation on the blots. Does phosphorylation refer to the more intense upper band (Fig 1e+f)? Given the general variability of WBs it might be better to demonstrate the differences in ORM phosphorylation with a more specific and quantitative method? e.g by a phosphoprotein stain or (better) by targeted (phospho)proteomics.

Significance

Unfortunately, the discussion focusses mostly on technical aspects of the method. However, the biological observations concerning the regulation of the SL metabolism itself are interesting and relevant too. They should be discussed in more detail, which might also be of interest to a more general readership. Concerning the factors involved in regulating SL de-novo synthesis, the authors did not mention CERT which also contributes to the regulation of SL de-novo formation (PMID: 36976648) and connects to SacI which is a component of the SPOTS complex.<br /> Why does yeast have two ORM isoforms and to which extend are they redundant? The authors see functional difference between the two ORM isoforms, which could be discussed in more depth. It might also be interesting to interlink the findings to the mammalian system, which is based on three ORMDL isoforms, and appear not to be regulated by phosphorylation. Another aspect that could be discussed in this contet is the observation that mammalian SPT appears preferentially located at MEM contact sites, which indicates a special role of SL de-novo synthesis at this location (PMID: 34785538). However, overall this is a well done paper.

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Reply to the reviewers

Reply to Reviewers

We thank both Reviewers for their comments which we believe could greatly improve the manuscript by adding more functional data. Part of the revision process has been already carried out and part of it is ongoing as detailed in the following sections.

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

Comments to the Authors In this manuscript, Girolamo et al., describe the differences in molecular signature and biological features of MuSC populations between extraocular (EOM) and limb (Tibialis anterior, TA) muscles. Comprehensive approaches including scRNA-seq, bioinformatics, and live-cell imaging reveal that EOM MuSCs is more proliferative in vitro and express ECM components at high levels as well as non-myogenic markers such as Foxc1 and Pdgfrb. The transcription factor network described in this study will characterize the identity of EOM MuSCs, providing insights into stem cell-based therapies for muscle diseases.

Major comments 1. In Figure 1A, EOM-MuSCs appear to form myotubes as efficiently as TA-MuSCs. If so, why myotube formation is not affected in EOM-MuSCs even with lower Myog expression compared to TA-MuSCs? The authors should discuss about this point.

We thank the reviewer for raising this point. Actually, EOM myoblasts show a delay in activation of Myog that allows their sustained expansion, however Myog activation per se is not impaired. This is reflected by the presence of the EOM Differentiating cluster in our sc-RNAseq analysis which converges towards the TA Differentiating cluster and shows co-expression of Myog and canonical differentiation markers such as Myh3 and Troponins (Figure 2C, D). Accordingly, Stuelsatz et al. (Dev Biol 2015) showed efficient and robust differentiation of EOM myoblasts in vitro, while a higher fraction of self-renewed (Pax7+) cells was observed in long term cultures.

To formally address this point, we propose to:

• Isolate EOM and TA MuSCs from Tg:Pax7-nGFP;MyogtdTom mice, plate them at low density and quantify the tdTom+ cell proportions in short vs longer term cultures (D3 vs D5, D8).
• Re-isolate the tdTom+ mononucleated fraction at D4-5 upon activation to:
• plate EOM and TA myoblasts at high density and assess their fusion index. Here, we will evaluated fusion independent of proliferation history and Myog activation.
• perform qRT-PCR for Myomixer/Myomaker on the tdTom+ mononucleated fraction to assess the extent of fusion potential.

  1. In Figure 2, activated EOM-MuSCs express Myod1e at lower levels compared to TA-MuSCs. Are MyoD protein levels are also lower in EOM-MuSCs?

We have performed quantitation of the intensity of fluorescence for Myod at D3.5 in culture. In agreement with the sc-RNAseq in vitro activated dataset, we have noted lower Myod protein levels in EOM MuSCs. This data is now included as part of Suppl Fig 2A.

In Figure 7E-G: Does the Foxc1 knockdown change the myogenic potential, especially on myotube formation? In addition to FOXC1 and Myog, the mRNA levels of Pax7 and Myod1 would be better to be provided.

Previously, we used siRNA for short term silencing. As siRNA are diluted upon cell division, we now use lentivirus-mediated KD, which provides more consistent results. To address this point, we propose to use lentivirus carrying 3 different shRNAs for Foxc1 and address expression levels of Pax7, Myod, Myog together with EdU detection and assessment of myotube formation. Given that cell density influences myotube formation, we will pre-amplify the cells, replate them at high density, and silence Foxc1 concomitantly with induction of differentiation. These 3 shRNAs have been already validated in vitro and induce a massive reduction in EOM cell numbers. This data is now included as part of __Figure 7E-L. __

Please state a reasonable explanation for the physiological role of high amounts of ECM produced by EOM-MuSCs.

We regret that this explanation did not come across clearly on the manuscript. Previous studies have demonstrated a greater cellular output of cranial MuSCs in clonal assays in vitro (Ono Dev Biol 2010, Stuelsatz et al. Dev Biol 2015; Randolph et al. Stem Cells 2015) and better engraftment capacity in vivo (Stuelsatz et al. Dev Biol 2015). On the other hand, it has been shown that fetal MuSCs, which produce high amounts of extracellular matrix (ECM) cell autonomously, expand more efficiently and contribute more to muscle repair than the adult counterparts (Tierney et al. Cell Reports 2016). Finally, while in vitro expanded MuSCs show a reduced engraftment potential (Montarras et al. Science 2005, Ikemoto et al. Mol Therapy 2007), recapitulation of the endogenous niche ex vivo, allows maintenance of an undifferentiated proliferative state and their capacity to support regeneration in vivo (Ishii et al. Stem Cell Reports 2017). Therefore, we hypothesize that in vitro activated EOM MuSCs secrete high amounts of ECM to self-autonomously maintain stemness when removed from their niche. Alternatively, EOM MuSCs might contribute to connective tissue cells postnatally in vivo as we described previously in the embryo (Grimaldi et al. elife 2022). Secretion of ECM and expression of ECM-related regulons when activated in vivo might recapitulate this process.

To address these hypotheses, we propose to:

• Culture EOM and TA MuSCs, generate EOM and TA decellularized ECM (dECM) and test the proliferation/differentiation potentials of MuSCs on the dECM versus that on wells coated with Matrigel or Fibronectin alone. Shall this experiment not give conclusive results, we propose to assess the proliferation/differentiation potential of TA MuSCs on dishes coated with proteins present in the EOM ECM such as Sparc, Bgn, Mgp, Fbn1, Fn1, for which recombinant proteins exist.
• Assess the expression levels of EOM-specific ECM proteins and TF regulons identified in vitro expressed in EOM MuSCs activated in vivo. To do so we are trying to optimize an EOM injury protocol based on previous observations highlighting the sensitivity of EOMs to anesthetics (Carlson et al. Arch Opthal 1985).
• Use Pax7CreERT2:R26tdTom:PdgfraH2BGFP reporter mice to determine whether EOM MuSCs can give rise to muscle connective tissue postnatally. Minor comments :

On p7, the 3rd line: "marker" is redundant.

This has been corrected.

On p9: what is meant by "force-directed environment"? Is this the aggregation of regulons and targets based on interaction strength determined by the algorithmic arrangement used by pySCENIC?

A force-directed graph is a type of visualization technique where nodes are positioned based on the principles of physics that assign forces among the set of edges and the set of nodes. Spring like attractive forces are used to attract pairs of edges towards each other (connected nodes) while repulsive forces, like those of electrically charged particles, are used to separate all pairs of nodes. In the equilibrium state for this system, the edges tend to have uniform length (because of the spring forces), and nodes that are not connected by an edge tend to be drawn further apart (because of the electrical repulsion). This results in a layout that visually represents the relationships between the nodes, where each node (circle) is an active transcription factor and each edge (distance between nodes) is an inferred regulation between 2 transcription factors.

The text has been changed accordingly.

On p11: add space between (Sambasivan et al., 20009a)and.

Corrected

On p11: 1.7 fold increase → 2.7 fold?

Corrected

On p13: please describe the GRN abbreviation since it is the first used here and not clarified beforehand.

Corrected to gene regulatory network (GRN)

On p15: add space between (Vallejo et al., 2018)Other.

Corrected

On p16: add "a" after "Klf4 is" → Klf4 is a pioneer...

Corrected

In Fig1: it would be better to show the quantification of EdU incorporation, especially at D5 for highlighting the difference between EOM and TA

This has been done and now included Figure 1B.

In Fig1: MF20 staining seemingly describes larger myotubes in EOM compared with TA at D5. Is this most likely due to the higher number of cells to start with in EOM rather than having more fusion ability?

Indeed, as discussed in the Main Comments (question 1), the fusogenic ability of EOM an TA MuSCs will be addressed by plating the same number of cells at high density.

In Fig 2E,F: some font is very faint in color and hard to read in printed format e.g. "TP53 regulates transcription of". May want to change color. In addition, the bottom edge of the Figure is slightly cut off.

We have enhanced the color of some words so all terms are properly seen. The figure has been adjusted in order for the bottom edge to be seen.

In Fig 4D: COLVI should be changed to COLIV.

Corrected

In Fig 5B: Myod1 is redundant.

Actually Myod as regulon (Myod1_(+)) in Fig 5B is not redundant. It is written twice as it is a regulon of both EOM Diff and TA Diff.

In Fig 6D; please specify "Amp". Is Hey1 a myogenic marker?

Amp stands for Activated/Amplified cells. We have changed this to Act to keep consistency.

Hey1 is a bHLH transcription factor that is required in a cell-autonomous manner for maintenance of MuSCs (Noguchi et al. Development 2019). This information has now been added to the text.

In Fig 7F; there are Ctrl and control- please unify them.

Corrected

In Fig7C,D: When does Foxc1 start to be expressed in EOM progenitors in the embryo? If the authors tested, please mention it.

Foxc1 is a DEG and top regulon of EOM progenitors in the early embryo (E11.5, Grimaldi et al. elife 2022). We will formally address this point by immunostaining on tissue sections of E10.5, E12.5 and E14.5 embryos.

In Supp Fig 7A: graphs are lacking color-coded legends.

Corrected

In Supp Fig 7C: Font is very small and illegible in a paper format.

Corrected. For networks it is sometimes difficult to get bigger font size.

In Supp Fig 7F: what are the dynamics of PDGFβ+ cell populations in successive passages in culture? If the authors tested please mention it.

We have been that Pdgfrb expression increases upon passages (Fig 6D). However, this experiment does not tell us whether there is a higher fraction of PDGFRβ+ cells or a similar fraction compared to Day 3 but expressing higher levels of the protein. To distinguish these possibilities, we propose to assess the PDGFRβ+ fraction by FACS upon passages in culture.

In Supp Fig 8 A: Are the colors reversed for EOM? In Fig 8 E, EOM progenitor and differentiation stream are light blue and yellow respectively but in Supp 8A the colors are flipped and don't seem to match the Map laid out in Fig 8E.

The scvelo pipeline will be re-run to correct this error on the graphical output.

Some references are listed as redundant.

Corrected

Reviewer #1 (Significance (Required)):

Skeletal muscle stem cells (MuSCs) play an indispensable role in muscle regeneration in adults. MuSCs are distributed in all muscles throughout the body and their function and molecular properties are diverse among muscles. Extraocular muscles (EOMs) are known to be preferentially spared in muscular dystrophies and during aging. In addition, EOM-derived MuSCs are highly transplantable compared to those of limb muscles. However, intrinsic regulators of EOM MuSCs have not been fully characterized yet. This study by Girolamo et al. shows the differences in molecular signature and biological features of MuSC populations between EOM and limb (Tibialis anterior, TA) muscles. Comprehensive approaches including scRNA-seq, bioinformatics, and live-cell imaging revealed that a subset of the EOM-derived MuSC population is highly proliferative and expresses extracellular matrix components at high levels. The analysis also shows that EOM-derived MuSCs have non-myogenic signatures such as Foxc1 and Pdgfrb. A transcriptional factor Foxc1 is described as a pro-mitogenic factor in the cancer field and is known as a driver of endothelial/smooth muscle fate. In this study, the authors find that Foxc1 is expressed in EOM MuSCs but not TA MuSCs. A siRNA-mediated gene silencing study shows that Foxc1 is important for the population expansion of EOM MuSCs. Furthermore, the authors demonstrated that the EOM MuSCs contain a PDGFRβ+ve cell population that is more proliferative and less myogenic compared to a PDGFRβ-ve cell population. Altogether, this study provides new insights into the regional differences in MuSCs and will contribute to the development of stem cell-based therapies for muscle-wasting diseases including muscular dystrophies and age-related sarcopenia.

We appreciate the assessment of the Reviewer noting the new insights that our work provides on muscle stem cell heterogeneity.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Benavente-Diaz et al. address a question of why do progenitors isolated from extra ocular muscles have higher proliferative and regenerative capacity compared to progenitors from limb muscles. They perform transcriptomic profiling of the two progenitor populations and report which genes and functional groups are differentially expressed. They perform multiple bioinformatic analyses aimed at providing insights into which differentially expressed genes may be master regulators of these differences.

Major comments:

Many conclusions in this paper are based on bioinformatic analyses with little experimental data provided as a confirmation. Overall, to increase significance of the manuscript I would suggest expanding the experimental validation part of the study. By following up on the findings from the bioinformatic analyses and confirming them in vitro this manuscript could move from beyond preliminary and only potentially interesting.

The previous version of our manuscript relied on bioinformatics analysis of single cell transcriptomics and some experimental validations to investigate muscle stem cell heterogeneity. Now, we performed loss of function experiments in EOM cells and gain of function experiments in TA cells using lentiviruses to validate those points mechanistically (Figure 7E-L).

Authors suggest a number of TFs and ECM components as master regulators of progenitor identity. An experiment of a rather limited scope was provided in Figure 7E-F, where effects of silencing TF Foxc1 on EOM progenitor proliferation was assessed. It would be highly beneficial to expand these experiments to include other TFs found in their dataset. Importantly, by overexpressing the proposed master regulators in TA progenitors authors should investigate whether these TFs indeed confer higher proliferative and regenerative capacity. Otherwise, the authors should make it clear that their conclusions about TFs regulating or maintaining EOM progenitors are preliminary and based on bioinformatic analyses.

Indeed, these experiments are necessary to consolidate the bioinformatic analysis and provide further mechanistic insights on this point. We have obtained lentiviruses and optimized gain of function assays in TA cells. Gain of function experiments with Creb3l1 and Dmrta2, two other top regulon transcription factors have been planned besides the experiments already included with Foxc1.

Minor comments:

In Figure 2, authors describe single-cell RNAseq analysis of EOM and TA progenitors. They report a number of markers differentially expressed between these two populations. It would be good to perform higher-resolution subclustering of each these populations to understand whether markers are expressed in all EOM progenitors or whether there is a specific subpopulation that is characterized by Mgp/Bgn/... expression. A paper by Yartseva et al. (Cell Reports 2020) did describe a population of activated satellite cells that express extracellular matrix components. In addition, from the data presented it is not clear whether proposed EOM markers are uniquely expressed or only enriched in EOM progenitors.

Actually, In Figure 2 we are showing what the reviewer is requesting. The heatmap highlights the presence of subpopulations (Progenitor/Differentiating) in both EOM and TA. The 4-way heatmap in Figure 2D is showing the distinctly upregulated genes of each subcluster. Matrix related genes are indeed expressed by a subpopulation of EOM cells, that we identified as "Progenitors". Two of those, Bgn and Mgp, can be seen in Figure 3H. Moreover, in Figure 4B we show the Average Expression and Percentage of cells expressing certain ECM component.

Actinomycin D is commonly used in single cell preparations for RNAseq to mitigate stress gene activation due to isolation procedure (for example see Wu YE et al. Neuron 2017). It is possible that EOM progenitors are particularly responsive to the isolation procedure, which would imply that stress genes are not involved in EOM progenitor maintenance, but that their expression is an artifact of isolation. These experiments should be repeated with actinomycin D to exclude potential artifacts.

While this is a possibility, the likelihood of this is relatively low as activated cells were obtained by quick trypsinization of cells. To formally exclude the problem mentioned by the reviewer we will perform qRT-PCR for EOM markers on activated cells at Day 3 that were fixed in PFA or treated with Actinomycin D prior to trypsinization. Moreover, in Suppl Figure 5G-E, we already used the stress index calculation defined by Machado et al. 2020 and this does not seem to affect our activated dataset.

It is unclear why authors chose to focus on PdgfrB+ population in Figure 7. Was it chosen as a target of Foxc1 or as a marker of proliferative cells? Any other reason? This should be explained as well as significance of this part in connection to the rest of the article.

We decided to focus on Pdgfrb for several reasons stated in the text: 1) it is a component of the matrisome we have validated; 2) it stands out in the Reactome pathways/Molecular function analysis; 3) it is a target of Foxc1; 4) it is a marker of cells with mesenchymal characteristics. We also chose this marker, for which antibodies for FACs exist, as proof of principle validation of the EOM mesenchymal phenotype. Similarly, sc-RNAseq analysis of human muscle, used Cav1 antibodies to isolate a functionally different subpopulation of MuSCs (Barruet elife 2020). To make the flow of the manuscript more consistent this data is now compiled on Figure 4.

Please explain the significance and relevance of the results presented in Figure 8A-C.

These figures highlight the potential of EOM progenitors to specifically regulate matrisome genes with respect to the TA. The 90 top active regulons of the EOM potentially regulate more matrisome genes than the TA, and the ratio (Number of EOM presumptive regulations/ Number of TA presumptive regulations) peaks when looking at the top 5 regulons (a 3-fold difference), and progressively reduces.

Prior studies are (not) referenced appropriately

We have corrected reference duplications.

Figures contain small fonts that are not legible. In particular, networks such as the one in Fig 5C are difficult to read.

The font size, font color and/or size of networks has been changed for Fig 2E-F, 5C-D, 8G-J and Suppl Fig 2A, 7C.

General assessment: Functional differences between EOM and TA progenitors have been previously described, but a deep mechanistic understanding of the underlying molecular pathways is lacking. This manuscript takes a step towards elucidating these molecular pathways.

We now provide more mechanistic data regarding the differential role that Foxc1 plays in extraocular compared to limb myogenic cells. Our revised plan will consolidate and extend these observations.

Advance: Tajbakhsh group recently published a paper Evano et al. Plos Genetics 2020, that also explored the differences between EOM and TA stem cells. Among other things this paper showed that EOM stem cells have intrinsic molecular mechanisms/programs that differentiate them from TA stem cells. In that context, the experimental insights that Benavente-Diaz et al. provide are not novel. Benavente-Diaz et al. would extend the knowledge in the field if they experimentally confirmed that the proposed master regulators indeed determine progenitor proliferation and regeneration capacity.

We respectfully disagree regarding the novelty of our work. In our previous study cited above, we showed that EOM stem cells have in vivo transcriptional differences with those in the limb (bulk RNAseq) and they can adopt the fate of limb cells when transplanted into the limb. Interestingly, full “reprogramming” was not achieved in those experiments pointing to limited plasticity.

Here, we show by scRNAseq and bioinformatic analysis of regulons that Foxc1 and extracellular matrix signature are features that are unique to EOM stem cells. Also, our overall single cell transcriptome analysis and comparative studies show that EOM muscle stem cells have adopted a signature that overlaps with mesenchymal stem cells – a property that has to date not been reported.

Muscle is arguably the best system to investigate stem cell heterogeneity, and our study provides mechanistic insights into the extend of this diversity.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Benaverte-Diaz et al. address a question of why do progenitors isolated from extra ocular muscles have higher proliferative and regenerative capacity compared to progenitors from limb muscles. They perform transcriptomic profiling of the two progenitor populations and report which genes and functional groups are differentially expressed. They perform multiple bioinformatic analyses aimed at providing insights into which differentially expressed genes may be master regulators of these differences.

Major comments:

• Many conclusions in this paper are based on bioinformatic analyses with little experimental data provided as a confirmation. Overall, to increase significance of the manuscript I would suggest expanding the experimental validation part of the study. By following up on the findings from the bioinformatic analyses and confirming them in vitro this manuscript could move from beyond preliminary and only potentially interesting.
• Authors suggest a number of TFs and ECM components as master regulators of progenitor identity. An experiment of a rather limited scope was provided in Figure 7E-F, where effects of silencing TF Foxc1 on EOM progenitor proliferation was assessed. It would be highly beneficial to expand these experiments to include other TFs found in their dataset. Importantly, by overexpressing the proposed master regulators in TA progenitors authors should investigate whether these TFs indeed confer higher proliferative and regenerative capacity. Otherwise, the authors should make it clear that their conclusions about TFs regulating or maintaining EOM progenitors are preliminary and based on bioinformatic analyses.

Minor comments:

• In Figure 2, authors describe single-cell RNAseq analysis of EOM and TA progenitors. They report a number of markers differentially expressed between these two populations. It would be good to perform higher-resolution subclustering of each these populations to understand whether markers are expressed in all EOM progenitors or whether there is a specific subpopulation that is characterized by Mgp/Bgn/... expression. A paper by Yartseva et al. (Cell Reports 2020) did describe a population of activated satellite cells that express extracellular matrix components. In addition, from the data presented it is not clear whether proposed EOM markers are uniquely expressed or only enriched in EOM progenitors.
• Actinomycin D is commonly used in single cell preparations for RNAseq to mitigate stress gene activation due to isolation procedure (for example see Wu YE et al. Neuron 2017). It is possible that EOM progenitors are particularly responsive to the isolation procedure, which would imply that stress genes are not involved in EOM progenitor maintenance, but that their expression is an artifact of isolation. These experiments should be repeated with actinomycin D to exclude potential artifacts.
• It is unclear why authors chose to focus on PdgfrB+ population in Figure 7. Was it chosen as a target of Foxc1 or as a marker of proliferative cells? Any other reason? This should be explained as well as significance of this part in connection to the rest of the article.
• Please explain the significance and relevance of the results presented in Figure 8A-C.
• Prior studies are referenced appropriately
• Figures contain small fonts that are not legible. In particular, networks such as the one in Fig 5C are difficult to read.

Significance

• General assessment: Functional differences between EOM and TA progenitors have been previously described, but a deep mechanistic understanding of the underlying molecular pathways is lacking. This manuscript takes a step towards elucidating these molecular pathways.
• Advance: Tajbakhsh group recently published a paper Evano et al. Plos Genetics 2020, that also explored the differences between EOM and TA stem cells. Among other things this paper showed that EOM stem cells have intrinsic molecular mechanisms/programs that differentiate them from TA stem cells. In that context, the experimental insights that Benaverte-Diaz et al. provide are not novel. Benaverte-Diaz et al. would extend the knowledge in the field if they experimentally confirmed that the proposed master regulators indeed determine progenitor proliferation and regeneration capacity.
• Audience: basic research, translational. This research would be of interest to regenerative therapy field.

My field of expertise: molecular and cellular biology, muscle regeneration. I am not a bioinformatician and I am not able to technically evaluate in silico approaches used in this study.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Girolamo et al., describe the differences in molecular signature and biological features of MuSC populations between extraocular (EOM) and limb (Tibialis anterior, TA) muscles. Comprehensive approaches including scRNA-seq, bioinformatics, and live-cell imaging reveal that EOM MuSCs is more proliferative in vitro and express ECM components at high levels as well as non-myogenic markers such as Foxc1 and Pdgfrb. The transcription factor network described in this study will characterize the identity of EOM MuSCs, providing insights into stem cell-based therapies for muscle diseases.

Major comments

1. In Figure 1A, EOM-MuSCs appear to form myotubes as efficiently as TA-MuSCs. If so, why myotube formation is not affected in EOM-MuSCs even with lower Myog expression compared to TA-MuSCs? The authors should discuss about this point.
2. In Figure 2, activated EOM-MuSCs express Myod1e at lower levels compared to TA-MuSCs. Are MyoD protein levels are also lower in EOM-MuSCs?
3. In Figure 7E-G: Does the Foxc1 knockdown change the myogenic potential, especially on myotube formation? In addition to FOXC1 and Myog, the mRNA levels of Pax7 and Myod1 would be better to be provided.
4. The authors mention that Foxc1 maintains EOM MuSCs in a progenitor-like state through matrix remodeling and cooperation with other TFs. However, such functional analysis does not seem to be provided sufficiently. For example: does Foxc1 siRNA lower matrisome and Pdgfrb genes in EOM-MuSCs; does forced expression of Foxc1in TA-MuSCs acquire the EOM-like state? Although the authors can predict the role and function of Foxc1 in the MuSC population based on the pySCENIC and previous studies, the experimental approach by the authors would be more convincing. The reviewer would like to emphasize that these experiments are not entirely necessary in this manuscript.
5. Please state a reasonable explanation for the physiological role of high amounts of ECM produced by EOM-MuSCs.

Minor comments

On p7, the 3rd line: "marker" is redundant.

On p9: what is meant by "force-directed environment"? Is this the aggregation of regulons and targets based on interaction strength determined by the algorithmic arrangement used by pySCENIC?

On p11: add space between (Sambasivan et al., 20009a)and.

On p11: 1.7 fold increase → 2.7 fold?

On p13: please describe the GRN abbreviation since it is the first used here and not clarified beforehand.

On p15: add space between (Vallejo et al., 2018)Other.

On p16: add "a" after "Klf4 is" → Klf4 is a pioneer...

In Fig1: it would be better to show the quantification of EdU incorporation, especially at D5 for highlighting the difference between EOM and TA.

In Fig1: MF20 staining seemingly describes larger myotubes in EOM compared with TA at D5. Is this most likely due to the higher number of cells to start with in EOM rather than having more fusion ability?

In Fig 2E,F: some font is very faint in color and hard to read in printed format e.g. "TP53 regulates transcription of". May want to change color. In addition, the bottom edge of the Figure is slightly cut off.

In Fig 4D: COLVI should be changed to COLIV.

In Fig 5B: Myod1 is redundant.

In Fig 6D; please specify "Amp". Is Hey1 a myogenic marker?

In Fig 7F; there are Ctrl and control- please unify them.

In Fig7C,D: When does Foxc1 start to be expressed in EOM progenitors in the embryo? If the authors tested, please mention it.

In Supp Fig 7A: graphs are lacking color-coded legends.

In Supp Fig 7C: Font is very small and illegible in a paper format.

In Supp Fig 7F: what are the dynamics of PDGFβ+ cell populations in successive passages in culture? If the authors tested please mention it.

In Supp Fig 8 A: Are the colors reversed for EOM? In Fig 8 E, EOM progenitor and differentiation stream are light blue and yellow respectively but in Supp 8A the colors are flipped and don't seem to match the Map laid out in Fig 8E.

Some references are listed as redundant.

Significance

Skeletal muscle stem cells (MuSCs) play an indispensable role in muscle regeneration in adults. MuSCs are distributed in all muscles throughout the body and their function and molecular properties are diverse among muscles. Extraocular muscles (EOMs) are known to be preferentially spared in muscular dystrophies and during aging. In addition, EOM-derived MuSCs are highly transplantable compared to those of limb muscles. However, intrinsic regulators of EOM MuSCs have not been fully characterized yet. This study by Girolamo et al. shows the differences in molecular signature and biological features of MuSC populations between EOM and limb (Tibialis anterior, TA) muscles. Comprehensive approaches including scRNA-seq, bioinformatics, and live-cell imaging revealed that a subset of the EOM-derived MuSC population is highly proliferative and expresses extracellular matrix components at high levels. The analysis also shows that EOM-derived MuSCs have non-myogenic signatures such as Foxc1 and Pdgfrb. A transcriptional factor Foxc1 is described as a pro-mitogenic factor in the cancer field and is known as a driver of endothelial/smooth muscle fate. In this study, the authors find that Foxc1 is expressed in EOM MuSCs but not TA MuSCs. A siRNA-mediated gene silencing study shows that Foxc1 is important for the population expansion of EOM MuSCs. Furthermore, the authors demonstrated that the EOM MuSCs contain a PDGFRβ+ve cell population that is more proliferative and less myogenic compared to a PDGFRβ-ve cell population. Altogether, this study provides new insights into the regional differences in MuSCs and will contribute to the development of stem cell-based therapies for muscle-wasting diseases including muscular dystrophies and age-related sarcopenia.

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Reply to the reviewers

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

Major points:

1. Although the role of mitofusin on mitochondrial morphology has been established by others and comprehensively assessed in the present study, the authors should determine the functional outcome from the genetic manipulations on Mfn2 and Mfn1. As observed by increased glucose uptake, one could hypothesize an impairment in mitochondrial oxidative phosphorylation, leading the cells to rely uniquely or heavily on glycolysis as a fuel. Also, as mentioned by the authors in the discussion, ROS play a fundamental role in adipogenesis, and, therefore, mitochondrial ROS emission and/or cellular redox balance should also be assessed. I believe these two experiments will add insightful information to the current dataset.

__Thank you for these suggestions. Whilst we agree with the general premise of this point, unfortunately quantifying oxidative phosphorylation and ROS production with sufficient precision to detect relatively subtle changes remains very challenging. We have attempted these experiments but they require considerable optimisation (particularly using adipocytes). Preliminary studies done in MEFs (Cover letter figure 1) suggest that under some stimuli there may be higher ROS in Mfn1 and Mfn2 knock-out lines. However this preliminary data would require further optimisation and repetition in adipocytes, which is more challenging. __

For now, we have amended the Discussion to specify that these experiments are of particular interest.

Cover letter figure 1. Levels of reactive oxygen species (ROS) in mouse embryonic fibroblasts measured by flow cytometry for fluorometric dyes CellROX (total cellular ROS), D2-HDCFA (total cellular ROS), and MitoSOX (mitochondrial ROS). Levels are expressed relative to wild-type. MEFs were treated with antimycin A (or media only) for 20minutes prior to incubation with the ROS dyes, then washed three times before assayed. AntA, Antimycin; CR, CellROX; M1, Mfn1-/- MEFs; M2, Mfn2-/- MEFs; MS, MitoSOX; WT, wild-type.

The insulin effect on glucose uptake does not allow to conclude any impairment in insulin responsivity. The fold change of glucose uptake mediated by insulin was roughly 1.2 in undifferentiated adipocytes, 2.3 in differentiated WT, and 2.5 in Mfn1KO differentiated adipocytes. The absolute increase in glucose uptake could be a compensatory mechanism due to impairment in mitochondrial bioenergetics (see point #1), given that the cells can still respond to insulin. Measuring Akt phosphorylation levels following insulin treatment would help solve this issue.

__As requested, we have assessed the effect of insulin treatment on Ser 473 phosphorylation of Akt2 (Pkb) in wild-type and knock-out MEFs differentiated into adipocytes (Fig 2D). Mfn1_-/-_ MEFs show an increase in Akt phosphorylation relative to the other cell lines. They also have higher expression of insulin receptor and Glut4, consistent with their degree of adipogenic differentiation. __

We agree that impaired mitochondrial bioenergetics could account for the observations in perturbed glucose uptake in the knockout cell lines (especially Mfn2-null) and have therefore amended the text throughout to reflect this.

Usually, working with clonal transgenic cells lines has the limitations that the cells might behave differently in terms of adipogenic potential over passages. A transient loss of function in the same cells would solve this concern. Also, introducing the patient mutations might be closer to the human situation than working with KO mouse fibroblasts.

__We agree with this potential concern, which is why we conducted knock-down studies in 3T3-L1 cells in addition to the work in knockout MEFs. These data were concordant with what we observed in the KO MEFs so we don’t think it is necessary to conduct repeat KD experiments in WT MEFs. __

In our previous study we observed that human fibroblasts with biallelic MFN2-R707W mutations did not have any obvious phenotype (____https://elifesciences.org/articles/23813____). We have separate work studying these mutations in vivo where we provide further characterisation of murine adipocytes harbouring Mfn2-R707W; this work is now published here: https://elifesciences.org/articles/82283

Minor points:

1. Although the authors mention in the introduction that the differentiation of adipocytes is followed by an increase in mitochondrial mass, it would be interesting the determine the expression profile of mfn1 and mfn2 during the differentiation process.

We have found that there is an increase in markers of mitochondrial fusion (Mfn1 & Mfn2) as well as fission (Fis1) throughout differentiation of 3T3-L1s. ____We have included this data in the manuscript (Supplementary Figure ____6A ).

The authors should discuss other models, even though pre-clinical, of mitochondrial dysfunction that results in lipodystrophy but with different metabolic outcomes. To cite a few but not only PMID: 29588285; PMID: 21368114; PMID: 31925461.

Thank you for this suggestion. We have added a section on this in the introduction.

It would be interesting to discuss the role of Mfn1/2 in the context of cold-induced adipogenesis, given the prominent role of mitochondrial dynamics, as mentioned by the authors in the reference list, on cold-induced adaptative thermogenesis (Mahdaviane et al. 2017; Boutant et al. 2017).

Thank you for this suggestion. We have added a section on this in the introduction.

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

• In Fig.2A, the authors report "increased lipid accumulation in Mfn1-/- MEFs, but not in Mfn2-/- MEFs". While the overall content might be similar, the pattern of lipid accumulation seems to be different. Indeed, differences in lipid droplet morphology have been observed in Mfn2 KO MEFs upon oleate treatment (McFie et al., 2016). The manuscript would benefit from having quantifications of lipid droplet size and number.

Thank you for highlighting this. We have quantified lipid droplet size and, consistent with McFie et al have found increased size in Mfn2 knock-down. This data is now included in Supplementary Figure 6B.

• Following the above point, McFie et al. also reported that Mfn1/Mfn2 double KO MEFs could differentiate into adipocytes. The authors should discuss these opposing observations. The contrasting observation may be due to acquired clonal differences in MEF lines. We have attempted ‘double’ knock down (of both Mfn1 and Mfn2 concurrently) in 3T3-L1 cells however this was essentially lethal and also did not generate any cells capable of differentiation. We have added a section in the Discussion regarding this point.

• In relation to the effects of Mitofusin deletions on glucose uptake, the authors mention that Mfn2 KO MEFs show impaired insulin stimulated glucose uptake. The interpretation of the result is not straight forward, as basal glucose uptake is highly increased in Mfn2 KO MEFs. Maybe there is simply a treshold for maximal glucose uptake capacity in MEF-derived adipocytes. In any of these cases, the authors might want to check GLUT1 levels, in line of their suggestion that the increased basal glucose uptake might be related to higher GLUT1. Alternatively, the authors might also want to check elements of the insulin signaling path, in case there are alterations that could explain the phenomenon.

As mentioned above in response to reviewer 1, we have now ____performed immunoblots to quantify some components of the insulin signalling cascade (Fig 2D). We observed lower expression of both Glut1 and Glut4 in the Mfn2-/- cells. Mfn2-/- cells did demonstrate some Akt phosphorylation but considerably less than Mfn1-/- cells. These results are now included in the revised manuscript (Figure 2D).

• In line with the above point, one would have wished that mitochondrial biology was better characterized in the different MEF models. While mitochondrial shape analyses are provided, some information on, at least, mitochondrial respiratory capacity, glucose oxidation and/or fatty acid oxidation rates, would be important. This would allow for a more solid discussion on why Mfn2 KO MEFs display such high basal glucose uptake rates.

We have responded to a similar suggestion from Reviewer 1, above.

• In relation to the experiments in MEFs, one should never forget that WT, Mfn1 and Mfn2 KO MEFs derive from different mice. Hence, the phenotypes could be related to trait variabilities in the origin mice themselves, and not just the gene deletion. To control for this aspect, the authors could simply re-introduced Mfn1 or Mfn2 in their respective MEFs and evaluate if their alterations are normalized.

__Yes one could try this but we have addressed this general concern by replicating the impact of Mfn1/2 KD in 3T3L1 cells so are not inclined to pursue this at this time. __

• Transcriptomic analyses reveals a decrease in adipogenic gene expression in Mfn2 KO MEFs. However, lipid accumulation is comparable to WT MEFs is normal. This could be due to defects in lipolytic capacity, leading to similar lipid accumulation despite lower adipogenic capacity. This could be tested by evaluating the adrenergic response of these cells (e.g.: glycerol release).

Thank you for this suggestion. We have commented in the Discussion to explain that we have not fully characterised this mechanism.

• The experiments in 3T3-L1 would also benefit from some gene expression analyses to evaluate if Mfn1 depletion leads to acceleration and/or magnification of the differentiation stages. In relation to this, 3T3-L1 cells could be used to monitor Mfn1 and Mfn2 through differentiation, which in itself would be valuable information.

We have performed a protein-level time course for markers of mitochondrial fusion (Mfn1 & Mfn2) as well as fission (Fis1) throughout differentiation of 3T3-L1s. We have included this data in the manuscript (Supplementary Figure 6A). We think that changes in protein expression are more relevant than changes in mRNA so have not included gene expression changes at this time.

CROSS-CONSULTATION COMMENTS The comments from the three independent reviewers are extremely well aligned and agree that improving the following aspects could largely benefit the manuscript:

• A better metabolic characterisation of the models used
• Provide measurements in relation to mitochondrial bioenergetics and ROS production – we have attempted this but the data is not very clear in our view and warrants further optimisation which we are not inclined to pursue currently. - Explorations of insulin signaling - done thank-you.
• Improve the validation and significance of the cellular models used, following the different suggestions from the three reviewers. Most notably, considering the introduction of human Mfn2 mutation forms – we have published a separate manuscript on follow up work on the human MFN2 variant as mentioned above.

A number of additional comments are raised, all of which are very reasonable and, in my opinion, should not be difficult to address. I think we can all agree that a mechanistic underpinning of the observations would give a larger degree of novelty to the work. Also, none of us would like the revision's quality to be constraint by a tight deadline. I would therefore be totally OK to extend the timeframe for the revision beyond the original 3 months proposed.

Reviewer #2 (Significance (Required)):

This is an interesting and well-crafted manuscript. Mice deficient for Mfn2 or Mfn1 have been reported by different laboratories, yet most of them fail to explore the effects on early adipogenesis. The study is limited to cultured cells, but this is well acknowledged by the authors Given the existence of human mutations in the mitofusin-2 gene that largely alter fat mass distribution, this work provides new clues on how these mutations might impact adipose tissue.

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

Mann et al. The objective of this study is to determine the extent to which mitofusins (Mfn1 and Mfn2) have redundant functions and assess their contributions to adipocyte differentiation. While a point mutation in the Mfn2 gene has been associated with severe adipose tissue dysfunction and lipodystrophy, no disease phenotypes have been linked to mutations in Mfn1. To address these objectives, the authors sought to characterize how adipocyte differentiation and function is affected in Mfn1, Mfn2 or double knockout adipocytes in two distinct in vitro models. Their findings indicate divergent effects of Mfn1 and Mfn2 on adipocyte differentiation and function despite similar alterations to mitochondrial morphology. Loss of Mfn1 promotes adipogenesis while Mfn2 decreases it. The authors conclude that these findings are indicative of non-redundant functions in Mfn1 and Mfn2.

Major comments: The observation that Mfn1 KO/KD leads to increased adipogenesis in vitro is somehow novel and, perhaps, surprising, as the author say. However, the molecular understanding underlying this phenotype remains unexplored. The analyses performed are mainly descriptive and don't dig deeper into the identification of the molecular mechanism. They do hypothesize that ROS production may be responsible for the observed effects, but that's how far they go.

The authors do highlight the limitations of this work, but these limitations need careful consideration, for not addressing them seriously limits the novelty of this study, especially not testing these conditions in human cells. The current version of this work seems too preliminary to suggest useful experiments that could strengthen the study, since future analyses could take many different directions.

Yes, we accept that the findings are rather preliminary but our initial efforts suggest that precisely elucidating the underlying mechanism/s is likely to be more difficult and complicated than alluded to by the reviewers. We would therefor prefer to share our initial observations so that others can also attempt to clarify the underlying mechanisms.

A few unanswered questions that the authors might consider are: What is the difference between the Arg707Trp mutation and the KO/KD? Mfn1 and 2 deletions lead to fragmented mitochondria, but opposite adipogenic potentials. What other mitochondrial defects can explain it? Are organelle contact site disrupted only with Mfn2? How does Mfn1 and 2 KO/KD affect mitochondrial proteome? What does mitochondrial bioenergetics look like? How is ROS production affected? Is the increased glucose uptake (basal) a compensatory mechanism for mitochondrial dysfunction? Thank you for these suggestions. We acknowledge that this work is largely descriptive in nature. These are all questions that should be addressed to improve mechanistic understanding of our observations.

__The difference between p.Arg707Trp and KO/KD is challenging to address because in the non-adipose cell lines studied so far (human and mouse fibroblasts) there has been no evidence of perturbation of the mitochondrial network. __

As discussed above, we have done preliminary studies into ROS production but are unable to provide a complete characterisation at this time. Similarly, we have not been able to perform bioenergetic studies (e.g. Seahorse, Oxyboros) that would provide more insight into differences between Mfn1 and Mfn2 KO cell lines.

CROSS-CONSULTATION COMMENTS I agree the work is interesting, but is too preliminary and merely descriptive. the experiments suggested will significantly improve the manuscript. However, I don't think they will take only three months to be completed. This work needs a significant amount of work including the study of the mechanism, at least an idea of what the mechanism could be, to be considered novel.

We accept this limitation and have responded to this general point above.

Reviewer #3 (Significance (Required)):

Understanding how mitochondrial dynamics affect adipogenic differentiation is critical to better understand how metabolism impact cell signaling, cell fate and function.

Strengths: this work reveals an interesting phenotype for Mfn1 and Mfn2 mutant preadipocytes. Weaknesses: this work is merely descriptive and preliminary to provide a clear understanding of the observed phenotypes

Advance: Although the performed experiments are accurate, well designed, and well controlled, the fact that Mfn1 and 2 have distinct functions and cannot compensate for one another was already clear based on the embryonic lethality of either Mfn1 and Mfn2 KO mice as well as the Mfn2 mutation in humans that leads to a pathological condition.In the current verison, this work minimally contributes to advancing the field.

Audience: an extensively revised version of this work including deeper phenotyping of thier models and human cell work would be of interest for sceintists studying mitchondrial biology, adipose tissue, metabolic diseases, and human genetic diseases.

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Referee #3

Evidence, reproducibility and clarity

Mann et al. The objective of this study is to determine the extent to which mitofusins (Mfn1 and Mfn2) have redundant functions and assess their contributions to adipocyte differentiation. While a point mutation in the Mfn2 gene has been associated with severe adipose tissue dysfunction and lipodystrophy, no disease phenotypes have been linked to mutations in Mfn1. To address these objectives, the authors sought to characterize how adipocyte differentiation and function is affected in Mfn1, Mfn2 or double knockout adipocytes in two distinct in vitro models. Their findings indicate divergent effects of Mfn1 and Mfn2 on adipocyte differentiation and function despite similar alterations to mitochondrial morphology. Loss of Mfn1 promotes adipogenesis while Mfn2 decreases it. The authors conclude that these findings are indicative of non-redundant functions in Mfn1 and Mfn2.

Major comments:

The observation that Mfn1 KO/KD leads to increased adipogenesis in vitro is somehow novel and, perhaps, surprising, as the author say. However, the molecular understanding underlying this phenotype remains unexplored. The analyses performed are mainly descriptive and don't dig deeper into the identification of the molecular mechanism. They do hypothesize that ROS production may be responsible for the observed effects, but that's how far they go.

The authors do highlight the limitations of this work, but these limitations need careful consideration, for not addressing them seriously limits the novelty of this study, especially not testing these conditions in human cells.<br /> The current version of this work seems too preliminary to suggest useful experiments that could strengthen the study, since future analyses could take many different directions. A few unanswered questions that the authors might consider are: What is the difference between the Arg707Trp mutation and the KO/KD? Mfn1 and 2 deletions lead to fragmented mitochondria, but opposite adipogenic potentials. What other mitochondrial defects can explain it? Are organelle contact site disrupted only with Mfn2? How does Mfn1 and 2 KO/KD affect mitochondrial proteome? What does mitochondrial bioenergetics look like? How is ROS production affected? Is the increased glucose uptake (basal) a compensatory mechanism for mitochondrial dysfunction?

Referees cross-commenting

I agree the work is interesting, but is too preliminary and merely descriptive. the experiments suggested will significantly improve the manuscript. However, I don't think they will take only three months to be completed. This work needs a significant amount of work including the study of the mechanism, at least an idea of what the mechanism could be, to be considered novel.

Significance

Understanding how mitochondrial dynamics affect adipogenic differentiation is critical to better understand how metabolism impact cell signaling, cell fate and function.

Strenghts: this work reveals an interesting phenotype for Mfn1 and Mfn2 mutant preadipocytes. Weaknesses: this work is merely descriptive and preliminary to provide a clear understanding of the observed phenotypes

Advance: Although the performed experiments are accurate, well designed, and well controlled, the fact that Mfn1 and 2 have distinct functions and cannot compensate for one another was already clear based on the embryonic lethality of either Mfn1 and Mfn2 KO mice as well as the Mfn2 mutation in humans that leads to a pathological condition.In the current verison, this work minimally contributes to advancing the field.

Audience: an extensively revised version of this work including deeper phenotyping of thier models and human cell work would be of interest for sceintists studying mitchondrial biology, adipose tissue, metabolic diseases, and human genetic diseases.

Reviewer expertise: adipose tissue function, metabolic disorders, mitochondrial bioenergetics.

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Referee #2

Evidence, reproducibility and clarity

The work by Mann and colleagues explores the adipogenic potential of MEF cells derived from Mfn1, Mfn2, Mfn1/Mfn2 and OPA1 KO mice. Two of these cell lines (Mfn1/Mfn2 KO MEFs and OPA1 MEFs) failed to differentiate, so only Mfn1 and Mfn2 were considered for most of the work. The experiments revealed that Mfn1 deletion lead to a faster and more prominent differentation of MEFs into adipocytes, which did not occur on Mfn2 KO MEFs. In contrast Mfn2 KO MEFs showed some signs of impaired adipogenesis, including lower GLUT4 gene expression and reduced insulin-stimulated glucose transport. Most of these observations were verified using a second cell model, in which Mfn1 or Mfn2 were knocked-down in 3T3-L1 adipocytes. This led the authors to conclude that Mfn1, but not Mfn2, enhances adipogenesis.

The manuscript is very well written and the experiments are proficiently designed. One might have wished confirmation of these findings in primary adipocyte cultures or in model organisms, but this limitation is duly acknowledged by the authors. The methods are well described and should allow other labs to easily reproduce the experiment. A few suggestions that could improve the manuscript can be found below.

• In Fig.2A, the authors report "increased lipid accumulation in Mfn1-/- MEFs, but not in Mfn2-/- MEFs". While the overall content might be similar, the pattern of lipid accumulation seems to be different. Indeed, differences in lipid droplet morphology have been observed in Mfn2 KO MEFs upon oleate treatment (McFie et al., 2016). The manuscript would benefit from having quantifications of lipid droplet size and number.
• Following the above point, McFie et al. also reported that Mfn1/Mfn2 double KO MEFs could differentiate into adipocytes. The authors should discuss these opposing observations.
• In relation to the effects of Mitofusin deletions on glucose uptake, the authors mention that Mfn2 KO MEFs show impaired insulin stimulated glucose uptake. The interpretation of the result is not straight forward, as basal glucose uptake is highly increased in Mfn2 KO MEFs. Maybe there is simply a treshold for maximal glucose uptake capacity in MEF-derived adipocytes. In any of these cases, the authors might want to check GLUT1 levels, in line of their suggestion that the increased basal glucose uptake might be related to higher GLUT1. Alternatively, the authors might also want to check elements of the insulin signaling path, in case there are alterations that could explain the phenomenon.
• In line with the above point, one would have wished that mitochondrial biology was better characterized in the different MEF models. While mitochondrial shape analyses are provided, some information on, at least, mitochondrial respiratory capacity, glucose oxidation and/or fatty acid oxidation rates, would be important. This would allow for a more solid discussion on why Mfn2 KO MEFs display such high basal glucose uptake rates.
• In relation to the experiments in MEFs, one should never forget that WT, Mfn1 and Mfn2 KO MEFs derive from different mice. Hence, the phenotypes could be related to trait variabilities in the origin mice themselves, and not just the gene deletion. To control for this aspect, the authors could simply re-introduced Mfn1 or Mfn2 in their respective MEFs and evaluate if their alterations are normalized.
• Transcriptomic analyses reveals a decrease in adipogenic gene expression in Mfn2 KO MEFs. However, lipid accumulation is comparable to WT MEFs is normal. This could be due to defects in lipolytic capacity, leading to similar lipid accumulation despite lower adipogenic capacity. This could be tested by evaluating the adrenergic response of these cells (e.g.: glycerol release).
• The experiments in 3T3-L1 would also benefit from some gene expression analyses to evaluate if Mfn1 depletion leads to acceleration and/or magnification of the differentiation stages. In relation to this, 3T3-L1 cells could be used to monitor Mfn1 and Mfn2 through differentiation, which in itself would be valuable information.

Referees cross-commenting

The comments from the three independent reviewers are extremely well aligned and agree that improving the following aspects could largely benefit the manuscript:

• A better metabolic characterisation of the models used
• Provide measurements in relation to mitochondrial bioenergetics and ROS production
• Explorations of insulin signaling
• Improve the validation and significance of the cellular models used, following the different suggestions from the three reviewers. Most notably, considering the introduction of human Mfn2 mutation forms

A number of additional comments are raised, all of which are very reasonable and, in my opinion, should not be difficult to address. I think we can all agree that a mechanistic underpinning of the observations would give a larger degree of novelty to the work. Also, none of us would like the revision's quality to be constraint by a tight deadline. I would therefore be totally OK to extend the timeframe for the revision beyond the original 3 months proposed.

Significance

This is an interesting and well-crafted manuscript. Mice deficient for Mfn2 or Mfn1 have been reported by different laboratories, yet most of them fail to explore the effects on early adipogenesis. The study is limited to cultured cells, but this is well acknowledged by the authors Given the existence of human mutations in the mitofusin-2 gene that largely alter fat mass distribution, this work provides new clues on how these mutations might impact adipose tissue.

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Referee #1

Evidence, reproducibility and clarity

Mann et al. described the effects of Mfn1 and Mfn2 deletion on adipogenesis. The authors describe a surprisingly pro-adipogenic effect of Mfn1 deletion despite massive mitochondrial fragmentation whilst conversely, loss of Mfn2 led to mitochondria fragmentation and impairment of adipogenesis. Overall, the research is well-designed and properly presented. Besides the lack of in vivo data (which is difficult due to the lack of a specific preadipocyte Cre), as acknowledged by the authors as a limitation, the study would benefit from a few experimental data in order to make the conclusions more robust. Please, find my comments in a point-by-point manner, which I hope will be useful for the authors.

Major points:

1. Although the role of mitofusin on mitochondrial morphology has been established by others and comprehensively assessed in the present study, the authors should determine the functional outcome from the genetic manipulations on Mfn2 and Mfn1. As observed by increased glucose uptake, one could hypothesize an impairment in mitochondrial oxidative phosphorylation, leading the cells to rely uniquely or heavily on glycolysis as a fuel. Also, as mentioned by the authors in the discussion, ROS play a fundamental role in adipogenesis, and, therefore, mitochondrial ROS emission and/or cellular redox balance should also be assessed. I believe these two experiments will add insightful information to the current dataset.
2. The insulin effect on glucose uptake does not allow to conclude any impairment in insulin responsivity. The fold change of glucose uptake mediated by insulin was roughly 1.2 in undifferentiated adipocytes, 2.3 in differentiated WT, and 2.5 in Mfn1KO differentiated adipocytes. The absolute increase in glucose uptake could be a compensatory mechanism due to impairment in mitochondrial bioenergetics (see point #1), given that the cells can still respond to insulin. Measuring Akt phosphorylation levels following insulin treatment would help solve this issue.
3. Usually, working with clonal transgenic cells lines has the limitations that the cells might behave differently in terms of adipogenic potential over passages. A transient loss of function in the same cells would solve this concern. Also, introducing the patient mutations might be closer to the human situation than working with KO mouse fibroblasts.

Minor points:

1. Although the authors mention in the introduction that the differentiation of adipocytes is followed by an increase in mitochondrial mass, it would be interesting the determine the expression profile of mfn1 and mfn2 during the differentiation process.
2. The authors should discuss other models, even though pre-clinical, of mitochondrial dysfunction that results in lipodystrophy but with different metabolic outcomes. To cite a few but not only PMID: 29588285; PMID: 21368114; PMID: 31925461.
3. It would be interesting to discuss the role of Mfn1/2 in the context of cold-induced adipogenesis, given the prominent role of mitochondrial dynamics, as mentioned by the authors in the reference list, on cold-induced adaptative thermogenesis (Mahdaviane et al. 2017; Boutant et al. 2017).

Referees cross-commenting

I agree with the statement of reviewer #2. I agree with reviewer #3, this is not the first paper on Mfns in adipocytes, so the novelty is limited but TMO sufficient for publication. Also, I tend to first look at what is there, not what is not there, and to my opinion, based on quality control measures, this work has merit.

Significance

See above

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Reply to the reviewers

Reply to reviewers.

We deeply thank the reviewers for the time spent on evaluating our manuscript as well as providing comments and suggestions to improve our study.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

*In this manuscript Lebdy et al. describe a new role of GNL3 in DNA replication. They show that GNL3 controls replication fork stability in response to replication stress and they propose this is due to the regulation of ORC2 and the licensing of origins of replication. Their data suggest that GNL3 regulates the sub nuclear localization of ORC2 to limit the number of licensed origins of replication and to prevent resection of DNA at stalled forks in the presence of replication stress.

While many of the points of the manuscript are proven and well supported by the results, there are some experiments that could improve the quality and impact of the manuscript. The main issue is that the connection between the role of GNL3 in controlling ORC2, the firing of new origins and the protection of replication forks is not clearly established. At the moment the model relies on mainly correlative data. In order to further substantiate the model, we propose to address some of the following issues:*

1. *The authors indicate that RPA and RAD51 accumulation at stalled forks is not affected by GNL3 depletion. These data should be included and other proteins should be analysed. In addition, the role of helicases could be explored through the depletion of the main helicases involved in the remodelling of the forks. * Response: As asked by the reviewer we will add the fractionation experiments that show that the level of RAD51 and RPA on chromatin is not affected by GNL3 depletion. So far, the other proteins we checked (RIF1 and BRCA1), both involved in nascent strand protection, did not show clear differences. Therefore, we concluded that depletion of GNL3 does not seem to affect the recruitment of major proteins required for protection of nascent DNA. Of course, we cannot exclude that other proteins may be affected by GNL3 depletion, but testing all the possible candidates would be time consuming with a very low chance of success. In addition, fractionation experiments are possibly not quantitative enough to uncover small differences and may be not that informative. Thus it remains possible that RPA exhaustion may be the cause of resection in absence of GNL3 as suggested by the work conducted in Lukas’ lab (Toledo et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24267891/). To test this hypothesis, we will analyze if resection in absence of GNL3 is still occurring in a well-characterized cell line that overexpress the three RPA subunits that we obtained from Lukas’ lab.

To our knowledge not many helicases have been shown to be involved in remodeling of stalled forks. The best example is RECQ1, however we feel that testing RECQ1 involvement in resection upon GNL3 depletion will complicate our story without adding much regarding the mechanism. We hope the reviewer understands our concern.

• The proposed model implies that GNL3 depletion leads to increased origin licensing. FThe authors should address if the primary effect of GNL3 depletion is on origin firing by using CDC7 inhibition in the absence of stress (Rodríguez-Acebes et al., JBC 2018). *

__Response: __This is an excellent point raised by the reviewer. To test if the primary effect of GNL3 depletion in on origin firing we will test if the defect in replication fork progression is dependent on CDC7 using DNA fibers experiments and CDC7 inhibitor.

• A way to prove that origin firing mediates the effect of GNL3 on fork protection would be to reduce the number of available origins. The depletion of MCM complexes has been shown to limit the number of back-up origins that are licensed and leads to sensitivity to replication stress (Ibarra et al., PNAS 2008). If GNL3 depletion results in increased number of origins, this effect should be prevented by the partial depletion of MCM complexes. *

__Response: __This is also an excellent point. We will test if MCM depletion decreases resection upon GNL3 depletion and treatment with HU. In addition, we will integrate in the manuscript experiments that we have done recently that show that treatment with roscovitine, a CDK inhibitor that impairs origin firing, decreases the level of resection observed in absence of GNL3. We think this experiment strengthens the results obtained with CDC7 inhibitors.

*Alternatively, the authors could try to modulate the depletion of GNL3. Origin licensing takes place in the G1 phase and thus the depletion of GNL3 by siRNA could affect the following S phase. Using an inducible degron for GNL3 depletion would allow to deplete GNL3 in G1 or S phase specifically. If the model is correct, the removal of GNL3 in S phase should not affect fork protection but removing GNL3 in the previous G2/M phase should reduce the number of licensed origins and lead to impaired fork protection. *

__Response: __This is obviously a good point given the fact that GNL3 deletion is not viable (see responses to reviewer 2). We tried to develop an auxin induced degron of GNL3, but we could not obtain homozygous clones, meaning that our clones had always an untagged GNL3 allele. Since GNL3 is essential its tagging may impair its function, explaining why we could not obtain homozygous clones. However, we are planning to optimize the design using other degrons system (for instance Halo-tag) to address the role of GNL3 specifically during S-phase. But we think this is above the scope of the present study.

*In addition to the connection GNL3-origin firing-fork protection, it is unclear how the lack of GNL3 in the nucleolus and the change in the sub nuclear localization of ORC2 controls origin firing and resection. The strong interaction observed between GNL3-dB and ORC2, and the subsequent change in ORC2 localization does not explain how origin licensing can be affected. In this sense, the authors could address: *

1. *Does the depletion of GNL3 and the expression of GNL3-dB affect the formation of the ORC complex, its subnuclear localization or its binding to chromatin? The authors have not explored if the interaction of GNL3 with ORC2 is established in the context of the ORC complex. An IF showing NOP1 with PLA data from GNL3-dB and ORC2 is needed to analyse how the expression of increasing amounts of GNL3-dB affects ORC2. * __Response: __We tested if GNL3 depletion impacts ORC2 and ORC1 recruitment on chromatin, but we could not observe significant differences. No clear differences were observed upon GNL3-dB expression either. One reason for this may be due to the excess of ORC complex on the chromatin, in addition chromatin fractionation is likely not sensitive enough to observe small differences. We think that quantitative ChIP-seq of ORC2 or other ORC subunits upon GNL3 depletion is required to visualize such differences, but this is above the scope of the study, and this constitutes the following of this project. We also tried to look at subnuclear localization of ORC2 using immunofluorescence, but the signal was not specific enough to observe differences. We think that the increased interaction (PLA) of ORC2 with GNL3-dB (Figure 5E) demonstrates a change in ORC2 subnuclear localization. To confirm this, we will perform the excellent experiment proposed by the reviewer to test if increasing level of GNL3-dB affects its interaction with ORC2 using PLA.

We do not think that the interaction between ORC2 and GNL3 is established in the context of the ORC complex since only ORC2 (and not the other ORC) was significantly enriched in the GNL3 Bio-ID experiment. The full list of proteins from the Bio-ID experiment (Figure 4A) will be provided in the revised version. Therefore, we think that either GNL3 regulates ORC2 subnuclear localization that in turns impact the ORC complex or GNL3 regulates ORC2-specific functions. More and more evidences show that ORC2 plays roles possibly independently of the ORC complex (see Huang et al. 2016 https://doi.org/10.1016/j.celrep.2016.02.091 or Richards et al. 2022 https://doi.org/10.1016/j.celrep.2022.111590 for instance). Future work should uncover how these ORC2 functions may regulate origins activity.

*In order to confirm if the mislocalization of ORC2 by the expression of GNL3-dB increases origin firing and mediates the effects on fork protection the authors could check DNA resection levels inhibiting CDC7 in high GNL3-dB conditions. Also, the levels of MCM2, phosphor-MCM2, CDC45, have not been analysed upon expression of GNL3-dB. *

__Response: __This is a good point; we will test if the resection observed upon expression of GNL3-dB is dependent on origin firing using CDC7 inhibitor. We have not measured the level of the cited proteins but instead we performed DNA combing to measure Global Instant Fork Density. We now show that expression of GNL3-WT suppresses the increased origin firing observed upon GNL3 depletion, in contrast expression of GNL3-dB does not suppress it. This important result indicates that origin firing is increased upon GNL3-dB expression, providing a link between aberrant localization and increased firing. These data will be part of the revised version of the manuscript.

The data in the paper suggest that GNL3 may affect the role of ORC2 in centromeres. Since depletion of GNL3 leads to increased levels of gH2AX, it would be interesting to address if this damage is due to incomplete replication in centromeres by analysing the co-localization of g*H2AX and centromeric markers both in unstressed conditions and upon the induction of replication stress. *

__Response: __This is indeed and interesting comment, however since it has been previously shown that gH2AX signal is rather strong upon GNL3 depletion (see Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/) we do not think that co-localization experiments with CENP-A for instance will be informative given the high number of gH2AX foci.

*Minor points: *

1. In the initial esiRNA screen the basal levels of g*H2AX should also be shown. * Response: Our negative control is the transfection of an esiRNAs that targets EGFP (a gene that is not expressed in the tested cell line). This esiRNAs is ranked at the end of the list and therefore constitutes the basal level of gH2AX signal. In any case it is well-established that GNL3 depletion increases gH2AX signal (see Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/).

*Figure EV1B: I think the rank needs another RS mark to see better the effect of each esiRNA on DNA lesions (high variability in all the conditions showed). *

__Response: __We understand this issue, but we cannot repeat this set of experiments for technical reasons (reagents and cost mainly). Anyway, we believe that the role of GNL3 is response to replication stress is extensively addressed by other experiments of this manuscript.

*Figure 1C and Figure EV1D/E: the quantification of the pCHK1/CHK1 levels could be included to show that there are no changes in phosphorylation upon GNL3 depletion. *

Response: it is a good point; we will put quantification in the revised version.

*In the first section of the results, at the end Figure 4B is incorrectly called for. *

__Response: __Thanks for the comment, we will modify accordingly.

The levels of GLN3 expression in 293 cells should be already included in section GNL3 interacts with ORC2.

__Response: __We will add a figure that shows the level of expression in 293 cells.

The full MS data needs to be included for both GNL3 and ORC2.

__Response: __This will be integrated in the revised version.

Figure 4B should be improved, since there is a faint band in the IgG mouse control.

__Response: __it is true that the figure is not perfect, but we believed that our Bio-ID and PLA experiments fully demonstrate the interaction between GNL3 and ORC2.

__Reviewer #1 (Significance (Required)): __

*The work is nicely written, the figures are well presented and the experiments have the necessary controls. It provides relevant information to understand how replication stress is controlled and linked to replication fork protection through origin firing. These results are relevant to the field, linking GNL3 to origin firing and with potential to help understand the role of GNL3 in cancer. They provide new information and can give rise to new studies in the future. Many of the conclusions of the manuscript are well supported. Additional support for some of the main claims would strengthen the results and also increase the impact providing a bigger conceptual advance by performing some of the suggested experiments. *

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

*This manuscript explores the role of GNL3/nucleostemin in DNA replication and specifically in the response of DNA replication to DNA damage. GNL3 is a predominantly nucleolar protein, previously characterised as a GTP-binding protein and shown to be necessary for effective recruitment of the RAD51 recombinase to DNA breaks. The entry point for this report is a mini screen, based on proteins identified previously by the authors to associate with replication forks by iPOND, for factors that increase gamma-H2Ax (an indicator of DNA damage) after treatment with the Top1 inhibitor camptothecin (CPT). In this mini-screen GNL3 emerged as the top hit.

The authors put forward the hypothesis that GNL3 is able to sequester the replication licensing factor ORC2 in the nucleolus and that failure of this mechanism leads to excessive origin firing and DNA resection following CPT treatment.*

• The model put forward is interesting, but currently rather confusing. However, for the reasons upon which I expand below, I do not believe that the data provide a compelling mechanistic explanation for the effects that are reported and I am left not being certain about some of the links that are made between the various parts of the study, even though individual observations appear to be of good quality. *

*Specific points: *

*The knockdown of GNL3 is very incomplete. In this regard, the complementation experiments are welcome and important. However, is it an essential protein? Can it be simply deleted with CRISPR-Cas9?

*__Response: __There are obviously variations between experiments but overall, the depletion of GNL3 using siRNA seems good in our opinion. Deletion of GNL3/nucleostemin leads to embryonic lethality in mouse (Beekman et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000755/ ; Zhu et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000763/). ES cells deleted for GNL3 can be obtain but do not proliferate probably because of their inability to enter in S-phase (Beekman et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000755/). We wanted to test if it was the case in our cellular model and we tried to delete it using CRISPR-Cas9. We managed to obtain few clones deleted for GNL3, but they grow really poorly prevented us to do experiments. To bypass this, and as suggested by the reviewer 1, we tried to make an auxin-induced degron of GNL3. Unfortunately, we did not manage to obtain homozygous clones, only heterozygous. One possibility could be that the tagging induced a partial loss of function of GNL3, and since GNL3 is essential, it may explain why we did not obtain homozygous clones. We may also want to use alternative degron systems such as Halo-Tag, but we believe this is out of the scope of the study.

__ __*Global instant fork density is not quite the same as actually measuring origin firing. Ideally, it would be good to see some more direct evidence of addition origin firing e.g. by EdU-seq (Macheret & Halazonetis Nature 2018) but this would be quite a significant additional undertaking. However, given the authors have performed DNA combing with DNA counterstain, they should be able to provide accurate measurements of origin density and inter-origin distance. *

__Response: __As indicated by the reviewer EdU-seq would need a lot of development since we are not using this approach in our team. In addition, this method can detect replication origins only if performed in the beginning of S-phase, meaning that only the early firing origins will be detected and not the others. GIFD measurement is actually directly linked with origin firing since it is counting the forks to duplicate the genome. The measurements of IODs have at least two main limitations: (1) there is a bias for short IODs due to the length of analyzed fibers and (2) it focuses only on origins within a cluster not globally. Overall, we believe that GIFD is the method of choice to measures origins firing. In addition, these experiments have been done by the lab of Etienne Schwob (see acknowledgments), a leader in the field.

*'Replication stress' is induced with CPT. This term is frequently used to describe events that lead to helicase-polymerase uncoupling (e.g. O'Connor Mol Cell 2015) but that is not the case with CPT, which causes fork collapse and breaks. Are similar effects seen with e.g. UV or cisplatin? Additionally, a clear statement of the authors definition of replication stress would be welcome. *

__Response: __We will better define the term ‘replication stress’ in the revised version of the manuscript. It should be understood, in our case, that any impediment that leads to replication fork stalling and measurable by DNA combing or Chk1 phosphorylation. We have not performed experiments using UV and cisplatin.

*It is really not clear how the authors explain the link between potential changes in origin firing and resection. i.e. What is the relationship between global origin firing and resection at a particular fork, presumably broken by encounter with a CPT-arrested TOP1 complex. What is the link mechanistically? This link needs elaborating experimentally or clearly explaining based on prior literature. *

• *__Response: __Most of our results on resection has been performed with hydroxyurea, but it is true that we saw resection in absence of GNL3 in response to CPT. Treatment with HU or CPT reduces fork speed and activates additional replication origins (see Ge et al. 2007 https://pubmed.ncbi.nlm.nih.gov/18079179/ for HU or Hayakawa et al. 2021 https://pubmed.ncbi.nlm.nih.gov/34818230/ for CPT ). When GNL3 is depleted, more forks are active, meaning more targets for HU and CPT. In addition, it is likely that the firing of additional origins in response to HU and CPT is stronger in absence of GNL3. Because of this we believe that factors required to protect stalled forks may be exhausted explaining why resection is observed. This is inspired by the work of Lukas’ lab (Toledo et al. 2013 https://pubmed.ncbi.nlm.nih.gov/24267891/) and is described in the figure 6. One obvious candidate that may be exhausted is RPA, to test this we will check if resection upon GNL3 depletion and treatment with HU is still occurring in cell lines provided by Lukas’ lab that overexpress RPA complex (described in Toledo et al.). We will explain our model more carefully in the revised version.

*Related to this, I remain unconvinced that the experiments in Figure 3 show that the effects of ATRi and Wee1i on origin firing and on resection are contingent on each other. I do not believe that the authors have adequately supported the statement (end of pg 9) 'We conclude that the enhanced resection observed upon GNL3 depletion is a consequence of increased origin firing.' The link between origin firing and resection needs really needs further substantiation and / or explanation.

*__Response: __Our rational was the following. Inhibition of ATR or WEE1 increase replication origin firing, a situation that may be like the one observed for GNL3 depletion. In Toledo et al, they show that inhibition of WEE1 or ATR induces exhaustion of RPA. This exhaustion is reduced in presence of CDC7 inhibitor, roscovitine (a CDK inhibitor that inhibits origin firing) or depletion of CDC45, indicating that this is due to excessive origin activation. In our case we show that the resection observed upon WEE1 or ATR inhibition is reduced upon treatment with CDC7 inhibitor. We conclude that excessive replication origin firing induces DNA resection. Since we observed the same thing upon GNL3 depletion (but not upon BRCA1 depletion) we conclude that excessive origin firing favors DNA resection likely through exhaustion of RPA. As indicated above we will test this hypothesis by overexpressing RPA. In addition, we now show that treatment with roscovitine decreases resection upon GNL3 depletion (this will be part of the revised manuscript), an experiment that we believe confirms that excessive replication origins firing is responsible for resection upon GNL3 depletion. As suggested by reviewer 1, we will also test if depletion of MCM also reduces resection observed in absence of GNL3.

*It is not clear whether the binding of ORC2 to GNL3 also sequesters other components of the origin recognition complex? Does loss of the ability of GNL3 to bind ORC2 actually lead to more ORC bound to chromatin? How does GNL3 contribute to regulation of origin firing under normal conditions? Is it a quantitatively significant sink for ORC2 and what regulates ORC2 release? *

Response: The results of GNL3 Bio-ID were extremely clear, we could not significantly detect any other ORC subunits than ORC2 (these data were not present in the manuscript but will be added in the revised version), therefore we believe that GNL3 may sequester/regulate only ORC2. We tried to see if GNL3 depletion was changing the binding of ORC1 and ORC2 to the chromatin, but we could not see any difference, one possibility may be that small differences are not detectable by chromatin fractionation. We believe that ChIP-seq or ORC2 or other ORC subunits in absence of GNL3 is required but this it out of the scope of the study. GNL3 may regulates the stability of the ORC complex on chromatin via ORC2 but GNL3 may also regulates other ORC2 functions, at centromeres for instance. It has been shown indeed that ORC2 plays roles possibly independently of the ORC complex (see Huang et al. 2016 https://doi.org/10.1016/j.celrep.2016.02.091 or Richards et al. 2022 https://doi.org/10.1016/j.celrep.2022.111590 for instance). How exactly this is affecting origin firing is still mysterious. This is something we are planning to address in the future.

We do not know if it is a quantitatively sink for ORC2 or how this is regulated, however we believe that the ability of GNL3 to accumulate in the nucleolus may sequester ORC2. Consistent with this, we show that a mutant of GNL3 (GNL3-dB) that diffuses in the nucleoplasm interacts more with ORC2 in the nucleoplasm suggesting a release. As suggested by reviewer 1 we will now test if the interaction between ORC2 and GNL3-dB is dependent on the level of expression of GNL3-dB. In addition, we now show that expression of GNL3-dB increases replication origin firing like GNL3 depletion (data that will be added in the revised version), suggesting that regulation of ORC2 is the major cause of increased firing upon GNL3 depletion.

*Minor points: *

*All blots should include size markers *

__Response: __We will add them

*Some use of language is not sufficiently precise. For instance: ** - the meaning of 'DNA lesions' at the end of the first paragraph of the introduction needs to be more explicit. *

* - the approach to measurement of these 'lesions' (monitoring gamma-H2Ax) needs to be spelled out explicitly, e.g. line 4 of the last paragraph of the introduction. *

*

• 'we observed that the interaction between GNL3-dB and ORC2 was stronger' ... I do not see how number of foci indicates necessarily the strength of an interaction. *

* - in many places throughout 'replication origins firing' should be 'replication origin firing' (or 'firing of replication origins'). *

__Response: __We will correct these language mistakes.

__Reviewer #2 (Significance (Required)): __

The model put forward here has the potential to shed light on an important facet of the cellular response to DNA damage, namely the control of origin firing in response to replication stress that will certainly be of interest to the DNA repair / replication community and possibly more widely. The roles of GNL3 are poorly understood and this study could improve this state of affairs. However, the gaps in the mechanism outlined above and somewhat confusing conclusions do limit the ability of the paper to achieve this at present.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

*In this study, Lebdy et al propose a new mechanism to regulate the resection of nascent DNA at stalled replication forks. The central element of this mechanism is nucleolar protein GNL3, whose downregulation with siRNA stimulates DNA resection in the presence of stress induced by HU (Figure 1). Resection depends on the activity of nucleases MRE11 and CtIP, and can be rescued by reintroducing exogenous GNL3 protein in the cells (Figure 1G). GNL3 downregulation decreases fork speed and increases origin activity, without any strong effect on replication timing (Figure 2). Inhibition of Dbf4-dependent kinase CDC7 (a known origin-activating factor) also restricts fork resection (Figure 3). GNL3 interacts with ORC2, one of the subunits of the origin recognition complex, preferentially in nucleolar structures (Figure 4). A mutant version of GNL3 (GNL3-dB) that is not sufficiently retained in the nucleoli fails to prevent fork resection as the WT protein (Figure 5). In the final model, the authors propose that GNL3 controls the levels of origin activity (and indirectly, stalled fork resection) by maintaining a fraction of ORC2 in the nucleoli (Figure 6). *

This model is interesting and provocative, but it also relies on a significant degree of speculation. The authors are not trying to "oversell" their observations, because the Discussion section entertains different interpretations and possibilities, and the model itself contains several interrogative statements (e.g. "ORC2-dependent?"; "exhaustion of factors?").

• While the article is honest about its own limitations, the major concern remains about its highly speculative nature. I have some questions and suggestions for the authors to consider that could contribute to test (and hopefully support) their model. *

• *If GNL3 downregulation induces an excess of licensed origins and mild replicative stress resulting in some G2/M accumulation (Figure 2), what is the consequence of longer-term GNL3 ablation? Do the cells adapt, or do they accumulate signs of chromosomal instability? (micronuclei, chromosome breaks and fusions, etc) * __Response: __This is an important point also raised by Reviewer 2: deletion of GNL3 leads to embryonic lethality in mouse and ES cells deleted for GNL3 do not proliferate and fail to enter into S-phase. Consistent with this, the clones deleted for GNL3 that we obtained using CRISPR-Cas9 grow poorly, thus preventing us to do experiments. To our knowledge micronuclei and chromosome breaks have never been analyzed upon transient depletion of GNL3 using siRNA. However, it is well established that depletion of GNL3 induces phosphorylation of H2A.X) and the formation of ATR, RPA32 and 53BP1 foci due to S-phase arrest (Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/). DNA lesions have also been visualized by comet assay (Lin et al. 2019. https://pubmed.ncbi.nlm.nih.gov/30692636/). Consistent with this we observed a weak increased of DNA double-strand breaks upon GNL3 depletion using pulse-field gel electrophoresis as well as mitotic DNA synthesis (MiDAS). We can integrate this data in the revised version of the manuscript if required. To sum up, it is clear that GNL3 depletion is inducing problems during S-phase that may lead to possible genomic rearrangements.

• The model relies on the link between origin activity and stalled fork resection that is almost exclusively based on the results obtained with CDC7i (Figure 3). But CDC7 has other targets besides pre-RC components at the origins, such as Exo1 (from the Weinreich lab, cited in the study), MERIT40 and PDS5B (from the Jallepalli lab, also cited). The effect of CDC7i could be exerted through these factors, which are linked to fork stability and DNA resection. The loss of BRCA1 (Figure 3F) could somehow entail the loss of control over these factors. Could the authors check the possible participation of these proteins?*

__Response: __It is true that CDC7 has other targets than pre-RC components. We therefore decided to inhibit origin firing using roscovitine, a broad CDK inhibitor, a strategy previously used in Lukas lab (Toledo et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24267891/). We observed that treatment with roscovitine decreased significantly resection observed upon GNL3 depletion, confirming the link between origin activity and stalled fork resection. This will be integrated in the revised version of the manuscript. As asked by Reviewer 1, we will also perform depletion of MCM to strength our model.

Exo1 is indeed a target of CDC7 as shown by the Weinreich lab (Sasi et al. 2018. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6111017/) however the authors do not formally demonstrate that Exo1 phosphorylation is required for its activity. We observed that depletion of Exo1 significantly reduced resection upon GNL3 depletion (data that will be added in the revised version), indicating that the effect of CDC7 inhibitor could be exerted via the control of Exo1. This is why our BRCA1 control is important, it is well stablished that Exo1 is required for nascent strand degradation upon BRCA1 depletion (Lemaçon et al. 2017. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5643552/) but CDC7 inhibition has no effect on resection upon BRCA1 depletion suggesting that resection by Exo1 may not be regulated by CDC7 in our context.

As stated by the reviewer MERIT40 and PDS5B are targets of DDK kinases (Jones et al. 2021 https://doi-org.insb.bib.cnrs.fr/10.1016/j.molcel.2021.01.004) and seem to be required for protection of nascent DNA and in response to HU. However, little is known about the role(s) of these proteins and we think that adding them will complicate message. We hope the reviewer understands this.

The model also relies on the fact that GNL3-dB mutant (not retained in the nucleoli) is not sufficient to counteract fork resection induced by HU (Figure 5G). The authors should test directly whether GNL3-dB induces extra origin activation, using their available DNA fibers-based technique.

__Response: __This is an excellent point. We have now GIFD (Global Instant Fork Density) data that shows that the number of active forks is increased upon dB GNL3-dB expression. It demonstrates that when GNL3 is no longer retained in the nucleolus more origins are active. These data will be integrated in the revised version of the manuscript, and we believe further support the regulation of ORC2 by GNL3.

*Finally, the model implies an exquisite regulation of the amount of ORC2 protein, which could influence the number of active origins and the extent of fork resection in case of stress. In this scenario, one could predict that ORC2 ectopic expression would have similar, or even stronger effects, than GNL3 downregulation. Is this the case? *

__Response: __We completely agree with this prediction. However, we are afraid that overexpression of ORC2 may have indirect effects due to the many described functions of ORC2, therefore it may be difficult to interpret the data. We will give a try anyway.

*Even if the connection between origins and fork resection could be firmly established, the molecular link between them remains enigmatic. The authors hint (as "data not shown") that it is neither mediated by RPA nor RAD51. Unfortunately, the reader is left without a clear hypothesis about this point. *

__Response: __We will add data that show that RPA and RAD51 recruitment is not affected by GNL3 depletion. However, the sensitivity of chromatin fractionation approach may be too weak to detect low differences. Based on the work of Lukas Lab (Toledo et al. 2013 https://pubmed.ncbi.nlm.nih.gov/24267891/) one possible mechanism may be exhaustion of the pool of RPA. This may link the excessive activation of origins observed upon GNL3 depletion and resection. To test this, we will check if resection upon GNL3 depletion and treatment with HU is still occurring in cell lines that overexpress RPA complex (described in Toledo et al.) that we obtained from Lukas’ lab.

__ __ **Referees cross-commenting**

__ __In addition to each reviewer's more specific comments, the three reviews share a main criticism: the lack of mechanistic information about the proposed link between origin activity and resection of nascent DNA at stalled forks.

__Reviewer #3 (Significance (Required)): __

In principle, this study would appeal to the readership interested in fundamental mechanisms of DNA replication and the cellular responses to replicative stress.

For the reasons outlined in the previous section, I believe that in its current version the study is not strong enough to provide a new paradigm about origins being regulated by partial ORC2 sequestering at nucleoli. The other potentially interesting advance is the connection between frequency of origin activity and the extent of nascent DNA resection at stalled forks, but the molecular link between both remains unknown.

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Referee #3

Evidence, reproducibility and clarity

In this study, Lebdy et al propose a new mechanism to regulate the resection of nascent DNA at stalled replication forks. The central element of this mechanism is nucleolar protein GNL3, whose downregulation with siRNA stimulates DNA resection in the presence of stress induced by HU (Figure 1). Resection depends on the activity of nucleases MRE11 and CtIP, and can be rescued by reintroducing exogenous GNL3 protein in the cells (Figure 1G). GNL3 downregulation decreases fork speed and increases origin activity, without any strong effect on replication timing (Figure 2). Inhibition of Dbf4-dependent kinase CDC7 (a known origin-activating factor) also restricts fork resection (Figure 3). GNL3 interacts with ORC2, one of the subunits of the origin recognition complex, preferentially in nucleolar structures (Figure 4). A mutant version of GNL3 (GNL3-dB) that is not sufficiently retained in the nucleoli fails to prevent fork resection as the WT protein (Figure 5). In the final model, the authors propose that GNL3 controls the levels of origin activity (and indirectly, stalled fork resection) by maintaining a fraction of ORC2 in the nucleoli (Figure 6).

This model is interesting and provocative, but it also relies on a significant degree of speculation. The authors are not trying to "oversell" their observations, because the Discussion section entertains different interpretations and possibilities, and the model itself contains several interrogative statements (e.g. "ORC2-dependent?"; "exhaustion of factors?").

While the article is honest about its own limitations, the major concern remains about its highly speculative nature. I have some questions and suggestions for the authors to consider that could contribute to test (and hopefully support) their model.

1. If GNL3 downregulation induces an excess of licensed origins and mild replicative stress resulting in some G2/M accumulation (Figure 2), what is the consequence of longer-term GNL3 ablation? Do the cells adapt, or do they accumulate signs of chromosomal instability? (micronuclei, chromosome breaks and fusions, etc)
2. The model relies on the link between origin activity and stalled fork resection that is almost exclusively based on the results obtained with CDC7i (Figure 3). But CDC7 has other targets besides pre-RC components at the origins, such as Exo1 (from the Weinreich lab, cited in the study), MERIT40 and PDS5B (from the Jallepalli lab, also cited). The effect of CDC7i could be exerted through these factors, which are linked to fork stability and DNA resection. The loss of BRCA1 (Figure 3F) could somehow entail the loss of control over these factors. Could the authors check the possible participation of these proteins?
3. The model also relies on the fact that GNL3-dB mutant (not retained in the nucleoli) is not sufficient to counteract fork resection induced by HU (Figure 5G). The authors should test directly whether GNL3-dB induces extra origin activation, using their available DNA fibers-based technique.
4. Finally, the model implies an exquisite regulation of the amount of ORC2 protein, which could influence the number of active origins and the extent of fork resection in case of stress. In this scenario, one could predict that ORC2 ectopic expression would have similar, or even stronger effects, than GNL3 downregulation. Is this the case?
5. Even if the connection between origins and fork resection could be firmly established, the molecular link between them remains enigmatic. The authors hint (as "data not shown") that it is neither mediated by RPA nor RAD51. Unfortunately, the reader is left without a clear hypothesis about this point.

Referees cross-commenting

In addition to each reviewer's more specific comments, the three reviews share a main criticism: the lack of mechanistic information about the proposed link between origin activity and resection of nascent DNA at stalled forks.

Significance

In principle, this study would appeal to the readership interested in fundamental mechanisms of DNA replication and the cellular responses to replicative stress.

For the reasons outlined in the previous section, I believe that in its current version the study is not strong enough to provide a new paradigm about origins being regulated by partial ORC2 sequestering at nucleoli. The other potentially interesting advance is the connection between frequency of origin activity and the extent of nascent DNA resection at stalled forks, but the molecular link between both remains unknown.

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Referee #2

Evidence, reproducibility and clarity

This manuscript explores the role of GNL3/nucleostemin in DNA replication and specifically in the response of DNA replication to DNA damage. GNL3 is a predominantly nucleolar protein, previously characterised as a GTP-binding protein and shown to be necessary for effective recruitment of the RAD51 recombinase to DNA breaks. The entry point for this report is a mini screen, based on proteins identified previously by the authors to associate with replication forks by iPOND, for factors that increase gamma-H2Ax (an indicator of DNA damage) after treatment with the Top1 inhibitor camptothecin (CPT). In this mini-screen GNL3 emerged as the top hit.

The authors put forward the hypothesis that GNL3 is able to sequester the replication licensing factor ORC2 in the nucleolus and that failure of this mechanism leads to excessive origin firing and DNA resection following CPT treatment.

The model put forward is interesting, but currently rather confusing. However, for the reasons upon which I expand below, I do not believe that the data provide a compelling mechanistic explanation for the effects that are reported and I am left not being certain about some of the links that are made between the various parts of the study, even though individual observations appear to be of good quality.

Specific points:

The knockdown of GNL3 is very incomplete. In this regard, the complementation experiments are welcome and important. However, is it an essential protein? Can it be simply deleted with CRISPR-Cas9?

Global instant fork density is not quite the same as actually measuring origin firing. Ideally, it would be good to see some more direct evidence of addition origin firing e.g. by EdU-seq (Macheret & Halazonetis Nature 2018) but this would be quite a significant additional undertaking. However, given the authors have performed DNA combing with DNA counterstain, they should be able to provide accurate measurements of origin density and inter-origin distance.

'Replication stress' is induced with CPT. This term is frequently used to describe events that lead to helicase-polymerase uncoupling (e.g. O'Connor Mol Cell 2015) but that is not the case with CPT, which causes fork collapse and breaks. Are similar effects seen with e.g. UV or cisplatin? Additionally, a clear statement of the authors definition of replication stress would be welcome.

It is really not clear how the authors explain the link between potential changes in origin firing and resection. i.e. What is the relationship between global origin firing and resection at a particular fork, presumably broken by encounter with a CPT-arrested TOP1 complex. What is the link mechanistically? This link needs elaborating experimentally or clearly explaining based on prior literature.

Related to this, I remain unconvinced that the experiments in Figure 3 show that the effects of ATRi and Wee1i on origin firing and on resection are contingent on each other. I do not believe that the authors have adequately supported the statement (end of pg 9) 'We conclude that the enhanced resection observed upon GNL3 depletion is a consequence of increased origin firing.' The link between origin firing and resection needs really needs further substantiation and / or explanation.

It is not clear whether the binding of ORC2 to GNL3 also sequesters other components of the origin recognition complex? Does loss of the ability of GNL3 to bind ORC2 actually lead to more ORC bound to chromatin? How does GNL3 contribute to regulation of origin firing under normal conditions? Is it a quantitatively significant sink for ORC2 and what regulates ORC2 release?

Minor points:

All blots should include size markers

Some use of language is not sufficiently precise. For instance:

• the meaning of 'DNA lesions' at the end of the first paragraph of the introduction needs to be more explicit.
• the approach to measurement of these 'lesions' (monitoring gamma-H2Ax) needs to be spelled out explicitly, e.g. line 4 of the last paragraph of the introduction.
• 'we observed that the interaction between GNL3-dB and ORC2 was stronger' ... I do not see how number of foci indicates necessarily the strength of an interaction.
• in many places throughout 'replication origins firing' should be 'replication origin firing' (or 'firing of replication origins').

Significance

The model put forward here has the potential to shed light on an important facet of the cellular response to DNA damage, namely the control of origin firing in response to replication stress that will certainly be of interest to the DNA repair / replication community and possibly more widely. The roles of GNL3 are poorly understood and this study could improve this state of affairs. However, the gaps in the mechanism outlined above and somewhat confusing conclusions do limit the ability of the paper to achieve this at present.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript Lebdy et al. describe a new role of GNL3 in DNA replication. They show that GNL3 controls replication fork stability in response to replication stress and they propose this is due to the regulation of ORC2 and the licensing of origins of replication. Their data suggest that GNL3 regulates the sub nuclear localization of ORC2 to limit the number of licensed origins of replication and to prevent resection of DNA at stalled forks in the presence of replication stress.

While many of the points of the manuscript are proven and well supported by the results, there are some experiments that could improve the quality and impact of the manuscript. The main issue is that the connection between the role of GNL3 in controlling ORC2, the firing of new origins and the protection of replication forks is not clearly established. At the moment the model relies on mainly correlative data. In order to further substantiate the model, we propose to address some of the following issues:

1. The authors indicate that RPA and RAD51 accumulation at stalled forks is not affected by GNL3 depletion. These data should be included and other proteins should be analysed. In addition, the role of helicases could be explored through the depletion of the main helicases involved in the remodelling of the forks.
2. The proposed model implies that GNL3 depletion leads to increased origin licensing. FThe authors should address if the primary effect of GNL3 depletion is on origin firing by using CDC7 inhibition in the absence of stress (Rodríguez-Acebes et al., JBC 2018).
3. A way to prove that origin firing mediates the effect of GNL3 on fork protection would be to reduce the number of available origins. The depletion of MCM complexes has been shown to limit the number of back-up origins that are licensed and leads to sensitivity to replication stress (Ibarra et al., PNAS 2008). If GNL3 depletion results in increased number of origins, this effect should be prevented by the partial depletion of MCM complexes.
4. Alternatively, the authors could try to modulate the depletion of GNL3. Origin licensing takes place in the G1 phase and thus the depletion of GNL3 by siRNA could affect the following S phase. Using an inducible degron for GNL3 depletion would allow to deplete GNL3 in G1 or S phase specifically. If the model is correct, the removal of GNL3 in S phase should not affect fork protection but removing GNL3 in the previous G2/M phase should reduce the number of licensed origins and lead to impaired fork protection. In addition to the connection GNL3-origin firing-fork protection, it is unclear how the lack of GNL3 in the nucleolus and the change in the sub nuclear localization of ORC2 controls origin firing and resection. The strong interaction observed between GNL3-dB and ORC2, and the subsequent change in ORC2 localization does not explain how origin licensing can be affected. In this sense, the authors could address:
   1. Does the depletion of GNL3 and the expression of GNL3-dB affect the formation of the ORC complex, its subnuclear localization or its binding to chromatin? The authors have not explored if the interaction of GNL3 with ORC2 is established in the context of the ORC complex. An IF showing NOP1 with PLA data from GNL3-dB and ORC2 is needed to analyse how the expression of increasing amounts of GNL3-dB affects ORC2.
   2. In order to confirm if the mislocalization of ORC2 by the expression of GNL3-dB increases origin firing and mediates the effects on fork protection the authors could check DNA resection levels inhibiting CDC7 in high GNL3-dB conditions. Also, the levels of MCM2, phosphor-MCM2, CDC45, have not been analysed upon expression of GNL3-dB.
   3. The data in the paper suggest that GNL3 may affect the role of ORC2 in centromeres. Since depletion of GNL3 leads to increased levels of H2AX, it would be interesting to address if this damage is due to incomplete replication in centromeres by analysing the co-localization of H2AX and centromeric markers both in unstressed conditions and upon the induction of replication stress.

Minor points:

1. In the initial esiRNA screen the basal levels of H2AX should also be shown.
2. Figure EV1B: I think the rank needs another RS mark to see better the effect of each esiRNA on DNA lesions (high variability in all the conditions showed).
3. Figure 1C and Figure EV1D/E: the quantification of the pCHK1/CHK1 levels could be included to show that there are no changes in phosphorylation upon GNL3 depletion.
4. In the first section of the results, at the end Figure 4B is incorrectly called for.
5. The levels of GLN3 expression in 293 cells should be already included in section GNL3 interacts with ORC2.
6. The full MS data needs to be included for both GNL3 and ORC2.
7. Figure 4B should be improved, since there is a faint band in the IgG mouse control.

Significance

The work is nicely written, the figures are well presented and the experiments have the necessary controls. It provides relevant information to understand how replication stress is controlled and linked to replication fork protection through origin firing. These results are relevant to the field, linking GNL3 to origin firing and with potential to help understand the role of GNL3 in cancer. They provide new information and can give rise to new studies in the future. Many of the conclusions of the manuscript are well supported. Additional support for some of the main claims would strengthen the results and also increase the impact providing a bigger conceptual advance by performing some of the suggested experiments.

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Reply to the reviewers

1. General Statements [optional]

We are grateful for the thoughtful comments and suggestions from the reviewers which we feel have resulted in a manuscript that is both clearer to the reader and more rigorous. We have addressed the suggested revisions point by point below:

2. Point-by-point description of the revisions

Reviewer #1 Major comments:

Figure 2E. This shows the residence time of Cse4 without Ndc10 association. How does this compare to the residence time on mutant CEN3 (Supplemental Figure 1). It looks like Cse4 still binds to CEN3 with some specificity even in the absence of Ndc10. Does this suggest that Cse4 has some intrinsic ability to recognize CEN3? Alternatively, Ndc10 is still required for Cse4 binding but is below detection in the Cse4-alone residence lifetimes. Ideally, the authors would compare this with Cse4 binding in an Ndc10 mutant.

We thank the reviewer for this interesting question. As suggested, we analyzed Cse4 behavior on the mutant CDEIIImut CEN3 DNA, which does not stably recruit Ndc10 (Figure 1C), using the real-time colocalization assay. Although overall Cse4 associations were reduced, we still observed transient interactions, consistent with the possibility that Cse4 has some intrinsic ability to recognize CEN3. Kaplan-Meier analysis of the lifetimes of Cse4 colocalizations on CDEIIImut CEN3 DNA were significantly reduced when compared to CEN DNA (Figure EV1G, H). We have added these points to the text (p. 10, lines 29-31 and p. 11, lines 1-8).

Figure 3 explores the very interesting relationship between Scm3 dynamics and Cse4 binding but I feel that the data is not fully flushed out. A key finding is that Cse4 can potentially bind to CEN DNA prior to engaging with Scm3 to be incorporated. This predicts that Cse4 should bind first and then colocalize with Scm3. Can this be detected in the timing of the traces? How often does Scm3 bind to already prebound Cse4 and does this correlate with Cse4 residing longer?

We performed new and more rigorous analyses of the data to address these questions in the revised manuscript. After our analysis to calculate ternaryScm3 off-rates, we analyzed the relative timing of these ternary residences and found that indeed Cse4 can bind to CEN DNA prior to Scm3 and these events do correlate with Cse4 residing longer. Complete analysis of the binding order of Cse4 and Scm3 ternary residences revealed that Scm3 bound to CEN3 DNA prior to Cse4 more often than Cse4 preceding Scm3 (46% vs 34% of ternary residences) with the remaining 20% arriving simultaneously (Figure EV2E). Despite a difference in prevalence, the median lifetimes of both Scm3-Firstand Scm3-Last contexts were similar to each other (Figure EV2F) and both were significantly stabilized when compared to non-ternary residences. These results highlight a potential mechanism where Scm3 catalyzes stable Cse4 incorporation at centromeric DNA instead of delivering it to the centromere regardless of the order of arrival. These data are now reported and discussed in the revision (p. 12, line 11-p.13, line 10).

A related and perhaps even more interesting point is whether Scm3 is involved in "loading" of Cse4. If so, then one would expect that once Cse4 is assembled into nucleosomes it should be stable, even if Scm3 leaves. Can the authors extract this from the data? Alternatively, it is possible that Scm3 remains associated to Cse4 to maintain the nucleosome which would imply a more extended role for Scm3 apart from assembly alone. It would be interesting if information on this can be extracted from the data.

Using our updated analysis of ternaryScm3 Cse4 residences, feel we have addressed this possibility indirectly in a couple of ways. First, we found that in instances where ternary Scm3/Cse4 complexes are formed, Scm3 co-occupied the CEN DNA an average of 56.0% of the total Cse4 residence time, which is distinctly shorter than the 84% of the total Cse4 residence that was occupied by Ndc10 in Cse4/Ndc10 ternary residences. These findings are consistent with a Scm3-turnover mechanism that occurs post ternary complex formation with Cse4 as we found that Cse4 off-rates were significantly reduced after Scm3 association (Figure 3D).

Second, further analysis of Scm3 residence behavior revealed that there was no significant stabilization of Scm3 after ternary Cse4/Scm3 complex formation vs non-ternary Scm3 residences found in either off-rates (33 hr-1 vs 32 hr-1, Figure EV2C) or median lifetimes (45 s vs 52 s, Figure EV2D). These results indicate that Scm3 association is not stabilized like Cse4 after ternary complex formation and points to a potential catalytic role in Cse4 nucleosome formation, leaving a stable Cse4 nucleosome after turnover. We reported these findings in the revision results section (p. 12, lines 11-16) as well as briefly within the discussion.

Even in the presence of Scm3 and CCAN components, Cse4 appears to have a limited lifetime in the in vitro assay compared to in vivo stability. The authors should speculate on whether activities exist in their extract that actively disassembles nucleosomes. Perhaps ATP could be depleted to inactivate remodellers?

This is an excellent suggestion that we addressed with a new experiment. We performed an endpoint localization experiment with lysate containing fluorescently labeled Ndc10 and Cse4 and then removed the lysate and incubated the slide for 24hr in imaging buffer at RT. Strikingly, the proteins were maintained at the CEN DNA with a high protein total colocalization (~75% retention) (shown in Figure EV1B, C). These data suggest that the lysates may contain negative regulatory factors and we have added this point in the revised text (p. 9 lines 6-25).

We were not able to address whether the removal of ATP stabilized the proteins because we previously found that ATP depletion of the lysates completely abrogates kinetochore assembly in extracts. We will need to eventually dissect the role of remodelers in future work using a different approach.

For Figure 6, it is not clear why AT-track mutants of CDEII are labeled as genetically stable and genetically unstable. This is confusing as the "genetically stable" show a more than 10-fold increase in chromosome loss rates. Perhaps these can be renamed into "unstable" and "very unstable" or "weak" and "strong" mutants, just to make clear that these classes are both poorer than wild type.

We had deferred to the nomenclature used in the previous study (Baker and Rogers, 2005) which initially characterized these mutants. To avoid this confusion, we have renamed these mutants “unstable” and “very unstable” as suggested to make it clearer that none of these synthetic mutants fully recapitulate WT CEN3 behavior.

Finally, it would be wonderful to include data to assess whether a full Cse4 nucleosome is assembled or a partial nucleosome e.g. just Cse4/H4 tetrasomes. This could be done by tracking the accumulation of H2A or H2B at the CEN3. This would give further insight into what step Scm3 catalyses.

This is a very interesting suggestion that we were not able to directly address. Epitope tagging of these histone proteins in Saccharomyces cerevisiae with endogenous fluorophores has proved challenging due to gene duplication, overall sensitivity to histone levels within the cells and disruption of histone function by epitope tagging. We hope to find a workable method to address this in the future to address this question directly.

Minor comments:

Typo on page 5, line 1 "nucleosom" missing an e.

We have corrected this in the revised text.

Kaplan-Meyer should be spelled Kaplan-Meier

We have corrected this in the revised text.

The term "censored" is mentioned across many figures but comes up just ones in the methods where it is not clearly explained. Perhaps this could be clarified in the legend.

We have now provided a clear explanation of the term “censored” in the text on p. 28, lines 25-27. It has also been added to the figure legends and reported in the Statistical tests section of the methods section to address this point.

The abstract states that Cse4 can arrive at the centromere without its chaperone. More likely, Cse4 is in complex with other chaperones that may allow it to bind. Perhaps the abstract can be modified to read "Cse4 can arrive at the centromere without its dedicated centromere-specific chaperone Scm3..."

We updated the abstract to reflect this point in the revised text.

Related to this point, the discussion states the possibility that Cse4 can initially bind to CEN3 via other more general chaperones. However, it should be acknowledged that transient Cse4 binding in their assay may simply occur through mass action due to high concentrations of CEN3 DNA. In vivo, this transient binding may not be that relevant.

We acknowledge this potential caveat in the discussion section (p. 20 lines 15-18), although we feel this is somewhat unlikely due to our observation of significantly reduced Cse4 binding on CDEIIImut DNA despite DNA concentrations being similar to previous assays (Figure EV3A). We speculate that some of this transient behavior is at least in part driven by two major factors: negative regulatory factors within our cellular extracts that counter nucleosome formation (as explored in Figure EV1B-C) and photostability of the endogenous fluorophores used within the study (Figure EV1D-E). These points were highlighted within the second paragraph of page 9.

Reviewer #2 Major comments:

1. Figure S1A-D seem like some of the most compelling data in the paper to bolster the rigor of their experimental setup. There appears to be plenty of space to include these data in the main figure set in Figure 1 after panel D. The authors would be well served to consider moving S1A-D somewhere in the main figure set.

We appreciate the helpful feedback on the importance of the date found in Supplemental Figure 1 and have now incorporated it into Figure 1 within the main text as suggested.

The authors conclude that Ndc10 recruits HJURP(Smc3) to the yeast point centromeres. If this is the case, can the TIRFM assay measure ternary residence lifetimes complexes between Ndc10/HJURP(Smc3)/CenDNA?

We made the conclusion that Ndc10 recruits Scm3 based on previous publications showing this requirement in vivo. We have now attempted to address this in our assay indirectly by monitoring Scm3 behavior on the CDEIIImut CEN3 DNA that lacks Ndc10. Surprisingly, we found that Scm3 interacted similarly with CDEIIImut CEN3 DNA and actually showed an increase in median lifetimes vs. CEN3 DNA (Figure EV2B), suggesting its intrinsic DNA-binding activity may be the primary driver of its CEN DNA binding and that stable Cse4 association is required for its turnover. These data suggest that Ndc10 is not driving Scm3 interaction (or targeting) to CEN3. We are grateful to the reviewer for pointing this out and have adjusted our conclusions in the revised manuscript (p. 12, line 26-p.13 line 10).

Throughout the manuscript short- and long- term residence lifespans are mentioned, referencing the figures containing lines with lengths depicting residence times. This is a qualitative reference to short and long residences. Can the authors provide a graph for short-term ( 300 s) residence life-spans for, CENPA alone, CENPA/Ndc10, and CENPA/HJURP on CEN3 DNA? Or some figure similar to Figure 3C, but reporting the proportion of short-term vs long-term residence?

We typically used Kaplan-Meier survival function estimates to compare binding behavior but agree that quantification of residences within these contexts may be easier for the reader to follow. We have therefore quantified short-term ( 300 s) as suggested and added them as a panel (F) to Figure EV1 and as panel (E) in Figure 3.

The choice of CCAN components for analysis in Fig. 5 is interesting, but many readers may be curious why Mif2 wasn't selected for disruption, since it has such a cozy placement with CENP-A and CEN DNA. Can choice to not include Mif2 mutants/degrons be mentioned/justified in the text (unless, even better yet, they choose to address Mif2 role directly in new experimentation)?

We relied on structural models to choose CCAN proteins that are in close proximity to the DNA. Because Mif2 is not in these structures, we did not include it in our studies. We have explained this in the revised text (p. 16 lines 14-17) and agree it is an interesting future area of study.

Minor comments:

1. Are these whole cell extracts (WCE) DNA-free? I'm curious if there is any competition from endogenous DNA from the yeast cellular extract.

The extracts are not DNA-free so it is likely there is some competition from endogenous DNA. We have avoided enzymatically removing the DNA since the TIRF assay depends on the integrity of DNA.

In relation to Mif2 and comment #4 above, do the authors make any connection to their results with synthetic nucleosome sequences not being conducive to yeast centromere formation with the prior observation (Allu et al 2019) using recombinant components that the human version of Mif2 more easily saturates its binding sites on CENP-A nucleosomes when they are assembled with natural centromere DNA rather than the Widom 601 sequence?

We did not speculate on the role of Mif2 and stability of synthetic nucleosome sequences. This is an interesting point but the differences between the yeast and human systems combined with the fact we have not yet started to study Mif2 made it seem too premature to include in this manuscript.

Providing a gel (or other measure) of the DNA templates (750, 250, and 80 bp) used in TIRFM assay would be nice to show to confirm the designed size of the pre-tethered DNA.

We agree this is a helpful control and we have now included it as a panel in Figure EV5B.

1. Some of the references to figures/figure panels in the main text do not match the figures. (discussion, pg 16, paragraph 1 & 2;pg 18, paragraph 1).

We have updated references mentioned to reflect to the correct figure in both sections of the discussion.

Reviewer #3 Major comments: -->Statistics are highly recommended for all the data in the ms.

We have included log-rank analysis to instances where two survival functions were plotted together where appropriate. P-values for all these analyses were reported in the appropriate figure legends.

• At what rate is data collected in the TIRFM setup. For clarity for the reader, it is important to provide imaging details for time-lapse. What is the impact of photobleaching on the stability of the fluorophore signal? Please clarify.

This is a helpful suggestion and we have now included imaging details (like time intervals for each channel) when the real-time assay is introduced in the results section (p. 8, lines 10-12). We have also provided additional details for the photobleaching estimates and how these might censor data in turn (p. 9, lines 14-25). Although photobleaching is a primary limitation of the time-lapse assays, we point out that it is appropriate to compare protein behavior under identical imaging parameters within differing contexts. We also noted that we typically compared time-lapse behavior (which is affected by photobleaching) with endpoint assays to ensure consistent behavior.

• The power of single-molecule technique is precisely that such data can be made quantitative. Indeed, the Kaplan-Meyer graphs do show nice quantitative results. Unfortunately, in the text few quantitative measurements are reported. In fact, the Kaplan-Meyer graphs can be interpreted in a quantitative manner such as probability of residency time. Although in most cases the statistical significance between two conditions can be expected, this is not formally calculated and shown. What is the 50% survival time of Cse4 alone or with Ndc10, for instance? This manuscript would greatly benefit from a quantitative approach to the data, including a summary table of the results of the various conditions tested. Please add this important table.

We initially put the quantitative data in the figure legends but omitted it from the main text for simplicity but appreciate the Reviewer’s point. We note that we performed log-rank tests on all Kaplan-Meier analyses that are plotted on the same graph to provide statistical differences where applicable and have included all P-values in the figure legends. In response to the suggestion, we have now also included a table (Table 1) that contains the median survival time for all proteins tested as well as the median survival times for the differing contexts tested for quick reference and easier comparison for the reader.

• This reviewer would expect that the endpoint (90 min) would roughly reflect the occupancy results from time-lapse (45 min) experiments. Based on the data presented in Figures 1, 2, S1-3, this does not appear to be the case. 50% of Cse4-GFP and 70% Ndc10-mCherry colocalized with CEN3 DNA in the endpoint experiment, whereas in Fig 2C, ~30 and ~52 traces were positive for Cse4-GFP and Ndc10-mCherry, resp. with the former having drastically lower residency survival compared to Ndc10-mCherry. If indeed, 50% of Cse4-GFP makes it to the endpoint, about 50% of all traces should reach the end of the 45 minutes time-lapse window. Only about 1/3 of all positive Cse4-GFP traces can be seen at the end of the 45 min window. Could this be due to technical issues of photostability of GFP? Why does the colocalization of Cse4 signal with the DNA signal disappear so readily? Are Cse4 so unstable? Is the same true for canonical H3 nucleosomes? This unlikely true for nucleosomes in cells.

This is a valid concern, and we appreciate the thoughtful critique. The inconsistency noted between the initial endpoint colocalization and those reported later in the paper is mainly due to the difference between yeast strains carrying Cse4 tagged alone in comparison to multiple kinetochore proteins with tags that exhibit mild genetic interactions. This point is now explained in the revised text (p. 8, line 29-p. 9. line 3).

Photostability is also a factor in the live imaging experiments compared to the endpoint localization assays. However, our photobleaching estimates suggest that the Cse4 lifetimes are not limited by photobleaching (Figure EV1D, E) so we do not believe that accounts for the differences between experiments and it is mainly the presence of multiple epitope tags.

In regard to why Cse4 is not more stable, Reviewer 1 had the same question so we performed an experiment to address whether the lysate contains negative regulatory factors. We found that Cse4 is stable once the lysate is removed (Figure EV1B, C), consistent with the idea that there are factors that disrupt it in the lysate. We discuss these potential reasons for transient association in the revised text (p. 9, lines 4-25).

It should also be noted that there are clear differences in nucleosome formation in reconstitutions and within our extracts, as evident by the Widom-601 DNA data (Figure 6D). This was not necessarily unexpected, as extracts are a much more complex medium, but we are encouraged by the fact that at least once formed, these Cse4-containing particles on CEN DNA are perhaps more stable than their reconstituted counterparts that seem to be so far unsuitable for structural studies.

Along the same lines, in Suppl Fig 3 there is a disconnect between residency survival and endpoint colocalization on either CEN3, CEN7, or CEN9. What could be the underlying mechanism between the discordance of endpoint results and time-lapse results? Could this be the result of experimental differences?

We are grateful that this discrepancy was highlighted to us, as upon closer examination we discovered that endpoint colocalization analysis had not been correctly updated in the figure to include data from equivalent genetic backgrounds as the CEN3 and CEN9 assays. Updating the figure in Appendix Figure S2 to include this data remedied this discrepancy.

• What fraction of particles show colocalization between Cse4-GFP and Ndc10-mCherry? What fraction of occupancy time show colocalization between Cse4-GFP and Ndc10-mCherry? Altogether, understanding the limitation and benefits of endpoint analysis and time-lapse analysis in this particular experimental set-up is important to be able to interpret the results. Please clarify these points.

We have now added particle numbers to all survival estimate plots which makes it much easier for the reader to interpret the proportion of Cse4 residences that are ternary vs. non-ternary in instances where off-rates were quantified and Kaplan-Meier analysis was performed on the resulting lifetimes. We determined that for ternary Cse4-Ndc10 residences, Cse4 and Ndc10 co-occupied the CEN DNA an average of ~84% of the total Cse4 residence.

• Page 9, third sentence of third paragraph it is stated that the "results suggests that Scm3 helps promote more stable binding of Cse4 ...". This is indeed one possible explanation of the results, and this possibility is tested by overexpressing Psh1 or Scm3 by endpoint colocalization analysis. 1) Taking the concerns regarding the endpoint vs time-lapse results into account, wouldn't it be more accurate to compare either time-lapse results against each other or endpoint results? 2) Alternatively, more stable Cse4 particles are able to recruit Scm3, simply because of the increased binding opportunity of a more stable particle. In this scenario, just the residency time of Cse4 alone is the predicting factor in likelihood to associate with Scm3. To test the latter possibility, Cse4 stability would need to be altered. Please consider this experiment- should be relatively easy with the right mutant of either CSE4 or CDEII (see Luger or Wu papers).

We appreciate the points raised here and addressed both as follows. For point (1) we altered the text in the third paragraph of the section, The conserved chaperone Scm3HJURP is a limiting cofactor that promotes stable association Cse4CENP-A with the centromere, to make it more clear to the reader that in the experiments presented in Figure EV4, endpoint analysis results were only compared to each other, and likewise time-lapse experiments were only compared to each other for each genetic background. While the results were consistent between experiments, we did not directly compare results from one to the results of another, but instead we used both assays to characterize Cse4CENP-A behavior more completely in differing contexts.

To test the alternative hypothesis proposed in point (2), we sought to avoid potential selection bias by utilizing off-rate analysis, which enabled us to separate the portions of Cse4 residences that occurred prior to ternary association with either Ndc10 or Scm3. This unbiased approach allowed us to compare Cse4 residence lifetimes pre and post ternary association and we found that there were still significant differences in off-rates and median lifetimes of the associated ternary and non-ternary residences using this updated analysis. We thank the reviewer for helping to guide us towards this more robust analysis.

Based on the recommendation in point (2), we also sought to directly compare the behavior of Cse4 and Scm3 on the “Very Unstable” CDEII mutants described in the section, DNA-composition of centromeres contributes to genetic stability through Cse4CENP-A recruitment. In this case, equivalent extracts were used and Cse4 stability was altered directly via the DNA template. When the off rates of ternaryScm3 Cse4 residences were compared, we found a significant increase in off-rates of Cse4 on the “Very Unstable” CDEII mutant CEN DNA (Appendix Figure S3B) compared to WT CEN DNA. If the alternative hypothesis proposed in point (2) were true, we would expect this reduction in median lifetime to correlate with a lower proportion of Cse4-Scm3 ternary association but quantification yielded proportions that, while varied, were not on average lower than the proportion of Cse4-Scm4 association on CEN3 DNA (.23 vs .31, Appendix Figure S3A). This finding, taken together with the fact that it would be difficult for us to propose an alternative hypothesis that explains the results outlined in Figure EV4, supports our hypothesis that Scm3 helps promote more stable binding of Cse4 and that this stabilization is directly influenced by DNA sequence composition.

• In Figure 1C and Supplemental Figure 5B, there appears to be foci that CEN3-ATTO-647 positive, but Cse4-GFP negative and visa verse. It seems logical that there are DNA molecules that didn't reconstitute Cse4 nucleosomes. But how can there be Cse4-GFP positive foci without a positive DNA signal? Is it possible that unlabeled DNA make it onto the flow chamber? If so, can these unlabeled DNA be visualized by Sytox Orange for instance to confirm that no spurious Cse4 deposition occurred? Please clarify.

Because it is unlikely that random associations will colocalize with the labeled DNA based on control assays (Supp. Figure 1C) that show this occurs rarely (

• On page 10, at the end of the first paragraph, growth phenotype of pGAL-SCM3 and pGAL-PSH1 mutants were tested. On GAL plates, pGAL-PSH1 shows reduced growth, but not pGAL-SCM3. Wouldn't a more accurate conclusion be that Psh1 is limiting stable centromeric nucleosome formation, instead of Scm3?

The growth defects on galactose don’t necessarily mean that a factor is limiting in cells. Instead, they report on whether changing the relative amounts of the complex lead to phenotypes in cells that could be the result of many causes that would require characterization of the phenotypes to understand. In this case, we presume that Psh1 titrates Scm3 away from Cse4 to prevent nucleosome formation in vivo. However, we have not directly tested this so we just concluded that the relative levels of the complexes are important for cell growth.

• In the section where DNA was tethered at either one or both ends, an important control is missing. How does such a set-up impact nucleosome formation in general. Can H3 nucleosomes form on random DNA that is either tethered at one or both ends? Does this potentially affect the unwrapping potential/topology of AT-tract DNA? Please comment.

This is an interesting point and one that we hope to explore further in the future but was beyond the scope of this paper. We suspect that restrictions via tethering would also limit canonical nucleosome formation on random DNA. We envision that unwrapping may be affected as well and hope to explore this via other, potentially better suited techniques like optical tweezers.

Minor comments + Censored data points are not explained in the text.

A brief explanation of censorship was added to the figure legends and we have now provided a clear explanation of the term “censored” in the text on p. 28, lines 25-27. It has also been reported in the Statistical tests section of the methods section to address this point.

• Number of particles tested should be reported in the main and supplemental figures, not just the legends for those readers who first skim the manuscript before deciding to read it.

We add these values to all Kaplan-Meier plots in all figures (Main, Expanded View, and Appendix)

• Typo on page 5, first line: "nucleosom" should be "nucleosome".

We fixed this in the text.

• Typo on page 9, second line: sentence is missing something "... is required for Scm3-dependent ..."

We fixed this in the text.

• It is unclear how the difference in Supplemental figure 5D was calculated.

We included log-rank test generated P-values as well as description in the figure legend of EV4.

• Figure 4C: why are there more Ndc10-mCherry foci observed in double tethered constructs vs single tethered constructs?

There can be variances in DNA density between slides, particularly with non-dye labeled DNA template. We updated figure panel C to include a representative image with similar Ndc10 density.

• For the display of individual traces as shown in Fig 2B, 3A, 4E, and 5E, it might be more informative if the z-normalized signal and the binary read-out are shown in separate windows to better appreciate how the z-normalized signal was interpretated.

Due to spacing limits within figures we attempted to accommodate this by reducing the thickness of the binary read-out and ensured that the raw data traces were overlaid for easier interpretation by the reader.

• Page 17, fifth line of the second paragraph, it is stated that a conserved feature of centromeres is their AT-richness. This is most certainly true for the majority of species studied thus far, but bovine centromeres for instance are about 54% GC rich. Indeed, Melters et al 2013 Genome Biol showed that in certain clades centromeres can be comprised of GC-rich sequences. It might be worthwhile to nuance this statement.

We have updated the text to reflect that AT-rich DNA is widely conserved but not a universal feature of centromeres.

• Page 17, last paragraph. Work by Karolin Luger and Carl Wu is cited in relationship to AT-rich DNA being unfavorable for canonical nucleosome deposition. A citation is missing here: Stormberg & Lyubchenko 2022 IJMS 23(19): 11385. Also, the first person to show that AT-tracts affect nucleosome positioning are Andrew Travers and Drew. This landmark work should be cited.

We thank the Reviewer for noticing this and have added the appropriate citations.

• Page 18, 9th line from the top, it is stated that yeast centromeres are sensitive to negative genetic drift. This reviewer is of the understanding that genetic drift is a statistical fluctuation of allele frequency, which can result in either gain or loss of specific alleles. Population size is a major factor in the potential power of genetic drift. The smaller a population, the greater the effect. Budding yeast is found large numbers, which would mean that drift only has limited predicted impact. Maybe the authors meant to use the term purifying selection?

We appreciate this clarification and agree with the reviewer, we have updated the manuscript to cite purifying selection and not genetic drift as at centromeres.

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Referee #3

Evidence, reproducibility and clarity

The manuscript "Single molecule visualization of native centromeric nucleosome formation reveals coordinated deposition by kinetochore proteins and centromere DNA sequence" by Popchock and colleagues describes a new high-throughput single-molecule technique that combines both in vitro and in vivo sample sources. Budding yeast centromeres are genetically defined centromeres, which makes them ideal for studying short DNA segments at the single-molecule level. By flowing in whole cell lysates, Cse4 nucleosomes can form under near physiological conditions. Two analytical experiments were performed: endpoint and time-lapse. In the former case, nucleosomes were allowed to form within 90 minutes and the latter case, nucleosome formation was tracked for up to 45 minutes. In addition, well described genetic mutants were used to assess the stability of Cse4 nucleosomes, as well as different DNA sequences (this we particularly liked- well done). Overall, this is a very interesting technique with potential to be useful for studying any DNA-based effect, ranging from DNA repair to kinetochore assembly. This is strong and impactful work, and the potential this kind of microscopy has for solving kinetic problems in the field. We think it's worthy of publication after revising technical and experimental concerns that would elevate the ms significantly.

Major comments:

Statistics are highly recommended for all the data in the ms.

• At what rate is data collected in the TIRFM setup. For clarity for the reader, it is important to provide imaging details for time-lapse. What is the impact of photobleaching on the stability of the fluorophore signal? Please clarify.
• The power of single-molecule technique is precisely that such data can be made quantitative. Indeed, the Kaplan-Meyer graphs do show nice quantitative results. Unfortunately, in the text few quantitative measurements are reported. In fact, the Kaplan-Meyer graphs can be interpreted in a quantitative manner such as probability of residency time. Although in most cases the statistical significance between two conditions can be expected, this is not formally calculated and shown. What is the 50% survival time of Cse4 alone or with Ndc10, for instance? This manuscript would greatly benefit from a quantitative approach to the data, including a summary table of the results of the various conditions tested. Please add this important table.
• This reviewer would expect that the endpoint (90 min) would roughly reflect the occupancy results from time-lapse (45 min) experiments. Based on the data presented in Figures 1, 2, S1-3, this does not appear to be the case. 50% of Cse4-GFP and 70% Ndc10-mCherry colocalized with CEN3 DNA in the endpoint experiment, whereas in Fig 2C, ~30 and ~52 traces were positive for Cse4-GFP and Ndc10-mCherry, resp. with the former having drastically lower residency survival compared to Ndc10-mCherry. If indeed, 50% of Cse4-GFP makes it to the endpoint, about 50% of all traces should reach the end of the 45 minutes time-lapse window. Only about 1/3 of all positive Cse4-GFP traces can be seen at the end of the 45 min window. Could this be due to technical issues of photostability of GFP? Why does the colocalization of Cse4 signal with the DNA signal disappear so readily? Are Cse4 so unstable? Is the same true for canonical H3 nucleosomes? This unlikely true for nucleosomes in cells. Along the same lines, in Suppl Fig 3 there is a disconnect between residency survival and endpoint colocalization on either CEN3, CEN7, or CEN9. What could be the underlying mechanism between the discordance of endpoint results and time-lapse results? Could this be the result of experimental differences?
• What fraction of particles show colocalization between Cse4-GFP and Ndc10-mCherry? What fraction of occupancy time show colocalization between Cse4-GFP and Ndc10-mCherry? Altogether, understanding the limitation and benefits of endpoint analysis and time-lapse analysis in this particular experimental set-up is important to be able to interpret the results. Please clarify these points.
• Page 9, third sentence of third paragraph it is stated that the "results suggests that Scm3 helps promote more stable binding of Cse4 ...". This is indeed one possible explanation of the results, and this possibility is tested by overexpressing Psh1 or Scm3 by endpoint colocalization analysis. 1) Taking the concerns regarding the endpoint vs time-lapse results into account, wouldn't it be more accurate to compare either time-lapse results against each other or endpoint results? 2) Alternatively, more stable Cse4 particles are able to recruit Scm3, simply because of the increased binding opportunity of a more stable particle. In this scenario, just the residency time of Cse4 alone is the predicting factor in likelihood to associate with Scm3. To test the latter possibility, Cse4 stability would need to be altered. Please consider this experiment- should be relatively easy with the right mutant of either CSE4 or CDEII (see Luger or Wu papers).
• In Figure 1C and Supplemental Figure 5B, there appears to be foci that CEN3-ATTO-647 positive, but Cse4-GFP negative and visa verse. It seems logical that there are DNA molecules that didn't reconstitute Cse4 nucleosomes. But how can there be Cse4-GFP positive foci without a positive DNA signal? Is it possible that unlabeled DNA make it onto the flow chamber? If so, can these unlabeled DNA be visualized by Sytox Orange for instance to confirm that no spurious Cse4 deposition occurred? Please clarify.
• On page 10, at the end of the first paragraph, growth phenotype of pGAL-SCM3 and pGAL-PSH1 mutants were tested. On GAL plates, pGAL-PSH1 shows reduced growth, but not pGAL-SCM3. Wouldn't a more accurate conclusion be that Psh1 is limiting stable centromeric nucleosome formation, instead of Scm3?
• In the section where DNA was tethered at either one or both ends, an important control is missing. How does such a set-up impact nucleosome formation in general. Can H3 nucleosomes form on random DNA that is either tethered at one or both ends? Does this potentially affect the unwrapping potential/topology of AT-tract DNA? Please comment.

Minor comments

• Censored data points are not explained in the text.
• Number of particles tested should be reported in the main and supplemental figures, not just the legends for those readers who first skim the manuscript before deciding to read it.
• Typo on page 5, first line: "nucleosom" should be "nucleosome".
• Typo on page 9, second line: sentence is missing something "... is required for Scm3-dependent ..."
• It is unclear how the difference in Supplemental figure 5D was calculated.
• Figure 4C: why are there more Ndc10-mCherry foci observed in double tethered constructs vs single tethered constructs?
• For the display of individual traces as shown in Fig 2B, 3A, 4E, and 5E, it might be more informative if the z-normalized signal and the binary read-out are shown in separate windows to better appreciate how the z-normalized signal was interpretated.
• Page 17, fifth line of the second paragraph, it is stated that a conserved feature of centromeres is their AT-richness. This is most certainly true for the majority of species studied thus far, but bovine centromeres for instance are about 54% GC rich. Indeed, Melters et al 2013 Genome Biol showed that in certain clades centromeres can be comprised of GC-rich sequences. It might be worthwhile to nuance this statement.
• Page 17, last paragraph. Work by Karolin Luger and Carl Wu is cited in relationship to AT-rich DNA being unfavorable for canonical nucleosome deposition. A citation is missing here: Stormberg & Lyubchenko 2022 IJMS 23(19): 11385. Also, the first person to show that AT-tracts affect nucleosome positioning are Andrew Travers and Drew. This landmark work should be cited.
• Page 18, 9th line from the top, it is stated that yeast centromeres are sensitive to negative genetic drift. This reviewer is of the understanding that genetic drift is a statistical fluctuation of allele frequency, which can result in either gain or loss of specific alleles. Population size is a major factor in the potential power of genetic drift. The smaller a population, the greater the effect. Budding yeast is found large numbers, which would mean that drift only has limited predicted impact. Maybe the authors meant to use the term purifying selection?

Significance

This study developed an in vitro imaging technique that allows native proteins from whole cell lysates to associate with a specific DNA sequence that is fixed to a surface. By labeling proteins with specific fluorophore-tags colocalization provides insightful proximity data. By creating mutants, the assembly or disassembly of protein complexes on native or mutated DNAs can therefore be tracked in real time. In a way, this is a huge leap forward from gel shift EMSA assays that have traditionally been used to do comparative kinetics in biochemistry.

This makes this technique ideal for studying DNA binding complexes, and potentially, even RNA-binding complexes. This study shows both the importance of using genetic mutants, as well as testing the effects of the fixed DNA sequence. As many individual fixed DNA molecules can be tracked at one, it allows for high-throughput analysis, similar to powerful DNA curtain work from Eric Greene's lab. Overall, this is a promising new single-molecule technique that combines in vitro and ex vivo sample sources, and will likely appeal to a broad range of molecular and biophysics scientists.

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Referee #2

Evidence, reproducibility and clarity

Centromeres drive chromosome inheritance from one cell generation to the next, so understanding their nature is of utmost importance in biology. The assembly of centromeric chromatin is of outstanding interest since defects in this step impair faithful genetic inheritance. Popchock et al investigate the molecular mechanisms of Cse4(CENPA) deposition and stabilization on a native budding yeast centromeric DNA. Using TIRMF (Total Internal Reflection Fluorescent Microscopy) enabled single molecule visualization of de novo Cse4(CENPA) nucleosome formation from a yeast cellular extract. The centromeric DNA used in this study was derived from PCR amplification of plasmids containing the native yeast point centromere from chromosome 3 (CEN3 DNA) sequences containing the CDEI, CDEII, CDEII, flanking pericentromeric DNA and linker DNA totaling ~750bp. In the PCR preparation, the CEN3 DNA contains a 5'-fluorescent dye and a biotinylated 3'-end, and was tethered to a functionalized (streptavidin) slide for TIRFM. The yeast extract was extracted from cells arrested in mitosis. This system is a novel application of a single molecule to study Cse4(CENPA) formation on centromeric DNA.

Using this system, the authors observed coordinated Cse4(CENPA) deposition on the CEN3 DNA, reporting inherent, transient colocalization of Cse4(CENPA) with CEN3 DNA. Stable Cse4(CENPA) colocalization on the CEN3 DNA is correlated with the Cse4(CENPA) chaperone Smc3(HJURP), and an ability for nucleosome formation on the CEN3 DNA. Further stabilization of Cse4(CENPA) was shown to depend on the DNA binding CCAN protein chl4(CENPN) and okp1(CENPQ) which dimerizes with the DNA/CENPA binding Ame1(CENPU).

Using this single molecule system they also demonstrated a role for the A/T run (>4) content in the CDEII as specifically important for Cse4(CENPA) deposition on CEN3 DNA. Cse4(CENPA) colocalization was preferred on the native CDEII sequence, relative to mutant CDEII sequences with similar A/T content but variable homopolymeric runs.

Major comments:

1. Figure S1A-D seem like some of the most compelling data in the paper to bolster the rigor of their experimental setup. There appears to be plenty of space to include these data in the main figure set in Figure 1 after panel D. The authors would be well served to consider moving S1A-D somewhere in the main figure set.
2. The authors conclude that Ndc10 recruits HJURP(Smc3) to the yeast point centromeres. If this is the case, can the TIRFM assay measure ternary residence lifetimes complexes between Ndc10/HJURP(Smc3)/CenDNA?
3. Throughout the manuscript short- and long- term residence lifespans are mentioned, referencing the figures containing lines with lengths depicting residence times. This is a qualitative reference to short and long residences. Can the authors provide a graph for short-term (<120 s) and long-term (> 300 s) residence life-spans for, CENPA alone, CENPA/Ndc10, and CENPA/HJURP on CEN3 DNA? Or some figure similar to Figure 3C, but reporting the proportion of short-term vs long-term residence?
4. The choice of CCAN components for analysis in Fig. 5 is interesting, but many readers may be curious why Mif2 wasn't selected for disruption, since it has such a cozy placement with CENP-A and CEN DNA. Can choice to not include Mif2 mutants/degrons be mentioned/justified in the text (unless, even better yet, they choose to address Mif2 role directly in new experimentation)?

Minor comments:

1. Are these whole cell extracts (WCE) DNA-free? I'm curious if there is any competition from endogenous DNA from the yeast cellular extract.
2. In relation to Mif2 and comment #4 above, do the authors make any connection to their results with synthetic nucleosome sequences not being conducive to yeast centromere formation with the prior observation (Allu et al 2019) using recombinant components that the human version of Mif2 more easily saturates its binding sites on CENP-A nucleosomes when they are assembled with natural centromere DNA rather than the Widom 601 sequence?
3. Providing a gel (or other measure) of the DNA templates (750, 250, and 80 bp) used in TIRFM assay would be nice to show to confirm the designed size of the pre-tethered DNA.
4. Some of the references to figures/figure panels in the main text do not match the figures. (discussion, pg 16, paragraph 1 & 2;pg 18, paragraph 1).

Significance

This work demonstrates the dynamics of Cse4(CENPA) coordination with Smc3(HJURP) to form nucleosomes on point centromeric DNA, and the necessity for homopolymeric A/T runs. It is a truly impressive piece of work that makes sense of findings from prior genetics experiments. Then it extends the understanding and clarifies the role of both centromere proteins and DNA sequence. The quantitative and powerful single molecule-based experimentation, the high importance of the subject matter, and its connection to studies using yeast genetics, will make this work, upon modest improvements (see section A of this review), of outstanding interest to an extremely broad audience of biologist.

My relevant expertise keywords: centromeres, nucleosomes, biochemical reconstitution, chromosome engineering

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Referee #1

Evidence, reproducibility and clarity

Summary

This work presents a novel experimental setup to explore native centromeric nucleosome formation at a single molecule level with a high degree of temporal resolution. It combines TIRF microscopy with an immobilized fluorescent yeast CEN3 DNA sequence. Binding of centromere proteins was probed by using whole-cell lysates produced from various mutant yeast strains expressing fluorescently tagged centromere proteins. This system was used to investigate the recruitment of Cse4 (yeast CENP-A), the histone H3 variant which defines centromeres, to the native yeast CDE3 sequence. Consistent with previous studies, the authors identified a requirement for Ndc10, which binds the CDE3 sequence with high efficiency, in Cse4 recruitment. Colocalization of Ndc10 with Cse4 significantly increases the stability of the Cse4-CDE3 interaction, and Ndc10 binding predominantly precedes Cse4 recruitment. Secondly, they investigated the impact of Scm3 (yeast equivalent of HJURP) on Cse4 stability and found that Scm3 is not required for transient short-term associations between the DNA and Cse4 but is needed for longer more stable interactions between Cse4 & the CDE3 sequence. Overexpression of Scm3 & its negative regulator Psh1 also showed that Scm3 availability is the rate-limiting factor in stable Cse4 associations with DNA. However, these interactions were abolished when the CDE3 DNA sequence was topologically restricted by tethering both ends to the streptavidin-coated coverslip suggesting that the formation of a nucleosome is essential for stable binding of Cse4 to CEN3. The sequence-specific DNA binding kinetochore proteins ChI4 & Okp1 were also found to improve the lifetime of Cse4-CDE3 interactions suggesting a stabilizing interaction. Finally, the impact of A/T runs on nucleosome formation was examined using a library of scrambled CDEII sequences, with approximately native levels As & Ts but shorter runs of the 2 nucleotides. Previous studies found a correlation between the length of AT runs and the incidence of chromosome missegregation. They now extend this correlation to a decreased ability of DNA to stably recruit Cse4. Finally, experiments with other sequences including the Wisdom601 sequence suggest that A/T runs along with CBF3 binding inhibit the recruitment of histone H3 to the CDEII sequence which is overcome by the interactions between Cse4 and Scm3.

Assessment

This is an insightful, well-executed study of a high technical standard. While several observations confirm or further validate previous findings in vivo (such as the requirement for Ndc10 and Scm3 for Cse4 assembly), this work adds a better understanding of the dynamics of Cse4 requirement and the role of Scm3 in assembly and the role of CCAN components in stabilizing Cse4. Figures are well laid out and methods are clearly described. In general, the claims are supported by the data. The development of their single-molecule setup to assay Cse4 nucleosome assembly is a promising tool for future work and for this reason work reporting. In short, I believe this paper contains exciting developments in the understanding of the specific mechanism and temporal dynamics of the formation of a Cse4 nucleosome on its native DNA and the interactions which underpin its stability in vitro and in vivo.

Major comments

I have several comments and suggestions for further analysis of the data. I also have suggestions for additional experiments, but I would stress that none of these are essential for publication.

Figure 2E. This shows the residence time of Cse4 without Ndc10 association. How does this compare to the residence time on mutant CEN3 (Supplemental Figure 1). It looks like Cse4 still binds to CEN3 with some specificity even in the absence of Ndc10. Does this suggest that Cse4 has some intrinsic ability to recognize CEN3? Alternatively, Ndc10 is still required for Cse4 binding but is below detection in the Cse4-alone residence lifetimes. Ideally, the authors would compare this with Cse4 binding in an Ndc10 mutant.

Figure 3 explores the very interesting relationship between Scm3 dynamics and Cse4 binding but I feel that the data is not fully flushed out. A key finding is that Cse4 can potentially bind to CEN DNA prior to engaging with Scm3 to be incorporated. This predicts that Cse4 should bind first and then colocalize with Scm3. Can this be detected in the timing of the traces? How often does Scm3 bind to already prebound Cse4 and does this correlate with Cse4 residing longer?

A related and perhaps even more interesting point is whether Scm3 is involved in "loading" of Cse4. If so, then one would expect that once Cse4 is assembled into nucleosomes it should be stable, even if Scm3 leaves. Can the authors extract this from the data? Alternatively, it is possible that Scm3 remains associated to Cse4 to maintain the nucleosome which would imply a more extended role for Scm3 apart from assembly alone. It would be interesting if information on this can be extracted from the data.

Even in the presence of Scm3 and CCAN components, Cse4 appears to have a limited lifetime in the in vitro assay compared to in vivo stability. The authors should speculate on whether activities exist in their extract that actively disassembles nucleosomes. Perhaps ATP could be depleted to inactivate remodellers?

For Figure 6, it is not clear why AT-track mutants of CDEII are labeled as genetically stable and genetically unstable. This is confusing as the "genetically stable" show a more than 10-fold increase in chromosome loss rates. Perhaps these can be renamed into "unstable" and "very unstable" or "weak" and "strong" mutants, just to make clear that these classes are both poorer than wild type.

Finally, it would be wonderful to include data to assess whether a full Cse4 nucleosome is assembled or a partial nucleosome e.g. just Cse4/H4 tetrasomes. This could be done by tracking the accumulation of H2A or H2B at the CEN3. This would give further insight into what step Scm3 catalyses.

Minor comments:

Typo on page 5, line 1 "nucleosom" missing an e.

Kaplan-Meyer should be spelled Kaplan-Meier

The term "censored" is mentioned across many figures but comes up just ones in the methods where it is not clearly explained. Perhaps this could be clarified in the legend.

The abstract states that Cse4 can arrive at the centromere without its chaperone. More likely, Cse4 is in complex with other chaperones that may allow it to bind. Perhaps the abstract can be modified to read "Cse4 can arrive at the centromere without its dedicated centromere-specific chaperone Scm3..."

Related to this point, the discussion states the possibility that Cse4 can initially bind to CEN3 via other more general chaperones. However, it should be acknowledged that transient Cse4 binding in their assay may simply occur through mass action due to high concentrations of CEN3 DNA. In vivo, this transient binding may not be that relevant.

Significance

This paper offers new insight into the assembly of yeast centromeres with a focus on the role of the Chaperone Scm3 in the assembly of the centromere-specific histone Cse4. This is still a poorly understood process and the authors offer an elegant in vitro system to study this and have presented new insights. For this reason, this is study is of interest to a broad readership in the area of mitosis and chromosome structure. The advance is strong at the technical level but also new insight is provided particularly in the role of Scm3 and the nature of centromeric DNA in centromeric chromatin assembly. Overall a strong, high-quality paper.

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Reply to the reviewers

The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, Wang and colleagues demonstrate that a single systemic injection of a high dose of Akkermansia muciniphila (A.m.) lysate drives a rapid pancytopenia followed by prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis (EMH). The latter, as well as the splenomegaly, were likely mediated through activation of pattern recognition receptors and IL-1R signalling pathways. This was demonstrated through the partial and full phenotype reversal in Tlr2;4-/- and MyD88;Trif-/- mice, respectively. Moreover, the phenotype was partially reversed following IL-1R antagonism. After performing multiplex protein assays and flow cytometry, the authors conclude that EMH, in this model, is mediated by IL-1a produced within the spleen by local monocytes and DC.

Overall, the manuscript by Wang et al. is quite well presented, the experiments are mostly well controlled, the methods are well reported, and the data fit a clearly defined story with clinical relevance. Nevertheless, there are several major concerns that if addressed would greatly increase the strength of the authors conclusions.

Major comments

1. The "two wave" hypothesis of hematopoiesis - first in the bone marrow (BM) and then in the spleen - is interesting. However, although an early wave of BM hematopoiesis would make sense, under these circumstances, I don't think the data are strong enough to support this hypothesis as they stand. For example, although the frequency of LSK cells increase, the numbers of most LSK subsets decrease. Given the decrease in the absolute number of BM cells 1d after A.m. injection, isn't it possible that the LSK cells are only proportionally increased relative to the remaining Lin- cells? What happens to the absolute number of LSK cells following A.m. injection?

Also, describing "two distinct waves of HSPC increase in the A.m.-injected spleen" (Fig 2 & S2 titles) and describing a "first wave" of HSPC expansion in the BM (lines 396, 399, 402 etc.) is misleading for the following reasons: (i) the data strongly support a single wave of increasing HSPC in the spleen, peaking at d14, and (ii) there is no evidence HSPC are increased in the BM until d56, although there does appear to be an early increase in MPP. The language should be changed accordingly. 2. The flow cytometry panel is not comprehensive enough to fully characterize the mature hematopoietic cell populations to the levels that are claimed here. For example, it is a stretch to assume that all B220- CD3- CD11c- cells are DC (splenic NK cells, eosinophils, monocytes and red pulp macrophages, for example, can express CD11c, particularly following inflammatory insult), or that CD11b+ F4/80+ SSC-hi cells are eosinophils, especially when eosinophils should be F4/80-lo are not known to express Ly6C in the spleen (For reference, see Immgen). These gating issues may explain the conspicuous absence of macrophages (should be F4/80+CD11b+Ly6C- and would also have a higher SSC than monocytes) in the plots. The B cell gate will also contain PDC, which express B220 (but can be easily excluded using Ly6C and CD11c). With respect to assessing the mature leukocyte populations in the spleen, relabelling the gates (CD11c+ cells instead of DC, F4/80+ myeloid cells instead of eosinophils) would suffice, however, these issues become a problem when trying to identify which cell populations express IL-1a.

Due to the limited antibody panel used here, there is not enough evidence to suggest that DC and monocytes are producing IL-1a. Moreover, the histograms showing the changes in expression of IL-1a on the "DC" and "Mo" are not very convincing. How does the IL-1a staining look on a dot plot? Is there good separation between positive and negative? These plots need to be included. What happens if you gate on the IL-1a+ cells first, then phenotype them?

Macrophages and splenic stromal cells are also likely candidates for IL-1a production. To assess which cell types are the true source of IL-1a, the authors need to repeat these experiments (namely, injecting A.m. and assessing IL-1a expression by leukocytes (and ideally also mesenchymal cells)) at d1 and d14, using a more comprehensive panel. Consider adding MHCII, CD64, Siglec F and CD24 to help differentiate between DC, MF, eosinophils and monocytes. CD45+ vs CD45- could be used as a minimum to assess the expression of IL-1a on leukocytes vs. stroma.

OPTIONAL: The mechanism could be better defined using bone marrow chimeras to assess the different contribution of TLR2/4 signalling and IL-1R signalling on the hematopoietic vs. mesenchymal cell compartments. 3. From these experiments, it is difficult to fully rule out a contribution from the adaptive immune system to the splenomegaly phenotype due to the marked difference in the size of BALB/c and MSTRG spleens at steady state. The authors should show the differences in spleen weight and total cell number as a % increase from control. The no of HSPC should also be normalized per gram of tissue weight or represented as a fold change compared to the relevant control groups. 4. When using fluorescent imaging to compare the abundance of HSPC and other cell populations in the spleen, the authors should provide absolute quantification from multiple FOV and multiple mice. 5. Finally, although the experiments are adequately replicated, the stats are not always appropriate. For example, a t-test shouldn't be used when there are >2 groups, or for a time course. This needs to be amended.

Minor comments

• Line 82-83: I'm fairly certain monocytes and inflammatory Ly6Chi cells are the same thing.
• Line 83-84: "IL-1a is crucial for sustaining inflammatory responses, recruiting myeloid cells to infected tissue and inducing hematopoietic stem and progenitor cell (HSPC) mobilization and expansion both in vitro and in vivo" - I don't believe IL-1a has been shown to be crucial for either, even if it has been shown to play a role. If I am mistaken, please reference with a manuscript showing relevant phenotypes using KO mice.
• Line 214: "Thus, we decided to use 200ug of lysate for the rest of all experiments." - is this what was usen for Figures 1A-C? This is not mentioned anywhere.
• Line 227: "containing both non-hematopoietic cells and immature HSPCs" Please reference Fig. 1H here. Otherwise, it is unclear how you identified the "HSPC and other cell types" in Fig. 1G.
• Figure S2A is described in text before Supp 1I-O and Fig S1H is not referenced in text at all.
• It would be interesting to include what happens to hepatomegaly in MSTRG, Tlr2;4-/- and MyD88;Trif-/- mice.
• Please define WBM. Presumably whole bone marrow?
• Notably, CCL2 is increased in spleen lysate, BM lysate and serum. Given is role in myeloid cell mobilization from the BM, I would expect its role in the phenotype described here to at least be discussed.
• HSPC LT gate includes MPP1, and should be labelled as such.

Significance

General assessment: The manuscript provided by Wang et al. describes, for the first time, a prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis following a single systemic injection of A.m. lysate. The EMH phenotype appears robust and the data implicating TLR-signalling and IL-1a production are compelling. The work has clinical relevance as it increases our understanding of the factors driving EMH.

There are two key limitations that let this study down. Firstly, the lack of depth in the flow cytometry panel used for immunophenotyping means it is not at all clear which cell types are producing IL-1a. Secondly, the authors use an enormous dose of bacterial lysate that is well above physiological levels, even following a loss of barrier integrity (e.g., in patients with IBD). This makes me question the biological relevance of the study, particularly with respect to Akkermansia translocation.

Advance: With some improvement, this study will advance the field, in general. Previous work has looked at EMH following LPS injection, or live E. coli infection, however; the authors are able to demonstrate a distinct Akkermansia-specific effect that differs to that of LPS, membrane components of a different gram-negative bacteria, B. theta. The advancements implicate IL-1a in the modulation of EMH, for the first time, providing some mechanistic insight into this phenomenon.

Audience: This work will likely be of interest to basic researchers interested in EMH. It may also be of interest to clinical researchers of pathologies where EMH is a known complication, such as rheumatoid arthritis and cancer. The impact of the work will depend on whether or not EMH contributes to pathogenesis, or is an epiphenomenon. To my knowledge, this has not been fully established, although this is not my area of research.

I am a basic researcher with expertise in immunology focused on host-microbe interactions, both within the intestine and at distal tissues. I have knowledge of BM hematopoiesis and the microbial factors that influence if although my knowledge on extramedullary hematopoiesis is limited.

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Referee #2

Evidence, reproducibility and clarity

In this study, Wang et al reported single injection of Akkermansia muciniphila (A.m.) induces two waves of extramedullary hematopoiesis (EMH), and demonstrated the mechanism of "second wave" was contributed by IL-1α secretion in spleen DCs and Ly6C+ monocytes. It is an important work on understanding infection-induced EMH. However, several major concerns about claims in this manuscript need to be addressed.

1. The authors demonstrated that A.m.-induced EMH were alleviated by knockout of Tlr2;4 or Myd88-Trif, or even IL-1R inhibition. EMH in the spleen is a mechanism by which the hematopoietic system responds to stresses. Therefore, whether inhibition of EMH by these ways can affect normal hematopoiesis in mice? Do mice have pancytopenia? Will the function of HSC in bone marrow be affected?
2. In Fig.S1E, why did the WBC and PLT recover quickly after the first day, while the RBC took 14 days to recover? Are WBC and RBC regulated by two waves of EMH, respectively?
3. The authors should show absolute numbers of each cell type, not just the percentage of immunophenotypically defined cells. For example, in Fig.1G, I, 2B.
4. In transplantation assays, whole BM cells or splenocytes was use. However, the proportion of HSCs in BM and spleen were all changed post A.m injection, which could affect the outcome of chimerism rate after transplantation. Transplantations should be done on by transplanting sorted fresh immunophenotypic HSCs.
5. The concentration of IFN-γ in both spleen and serum were increased continuously from D1 to 14. Would IFN-γ cause the second wave of EMH? Relevant assays for exclusion are necessary.

Significance

It is an important work on understanding infection-induced EMH.

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Referee #1

Evidence, reproducibility and clarity

Wang et al. examined the mechanisms of splenic extramedullary hematopoiesis upon systemic injection of Akkermansia muciniphila in mice. They showed that components of this mucin-degrading bacterium mobilize bone marrow hematopoietic cells and induce splenomegaly by MYD88/TRIF-dependent innate immune signaling pathways. Activation of TLRs and release of interleukin 1-alpha from splenic cells were then responsible for the expansion and differentiation of functional hematopoietic progenitors in the spleen. Genetic deletion of TLR2 and 4 restrained splenomegaly, while, pharmacological inhibition of IL1 receptor abrogated splenomegaly and extramedullary hematopoiesis suggesting their cooperation in the observed phenotype. It has been widely accepted that splenomegaly arises as a consequence of inflammation and that TLRs are major drivers of this process in the context of bacterial or viral infections. Here, the novelty relies on the potential circuit with the IL1alpha-IL1R axis as an additional driver of splenic extramedullary hematopoiesis. Although the results summarized above indicate that both TLRs and IL1 individually participate to some extent in splenomegaly after Akkermansia muciniphila administration, they fail to demonstrate that they concertedly do so in the spleen. In fact, the blockade of IL1R has a more profound impact.

Significance

My concerns are the following: - The authors mentioned that a specific lipid from Akkermansia muciniphila is able to trigger a non-canonical TLR2-TLR1 heterodimer to release inflammatory cytokines and regulate human immune response. Why TLR1 was not considered in the experimental strategy? - IL1alpha is up-regulated in several splenic cells (in particular in macrophages, Fig. S4F). To demonstrate a critical involvement of dendritic cells or monocytes, depletion studies or conditional mice models should be evaluated. What about megakaryocytes? Why were excluded from the analyses? - Interleukin 1alpha KO mice model should be also evaluated. - The paper is very dense and not easy to read and follow. English editing is required.

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Reply to the reviewers

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

The manuscript presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.

The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.

We thank the reviewer for the advice on the general writing standard and data organization. We have reanalyzed experiment data and interpreted the findings more conservatively for application into the simulation models. As a result, some conclusions to the results sections have changed. Accordingly, we have done a major revision of the entire Results, Discussion and Models and Methods sections in the paper to articulate these reinterpretations while removing superfluous details that may obfuscate the data.

It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ?

We thank the reviewer for the question. Only WT and Marcksl1 KO have been matched for peak velocities in the CA, CV and ISVs between experiments and simulations. WT results were compared to both the experimental reference of 27 embryos in Table 3 and also to the current experiment pool of WT (5 embryos) in Table 6. Marcksl1 KO simulation models 1, 2 and 3 were compared against the average level seen in the low and moderate perfusion Marcksl1 KO phenotypes (8 embryos) from the experiment (Table 5 and Table 6). Additionally, we also have represented the similar level of RBC hematocrit in the CA for WT model to WT experiment data from the reference cited in Table 3.

In addition to the velocity comparisons, we now use the experimentally observed trend of decreased flow rate in the CA of Marcksl1 KO experiment data to assess the model boundary conditions amongst Marcksl1 KO models 1, 2 and 3 that best reflect the experimental observations:

Page 11, lines 1 to 20

The Marcksl1 OE cannot be matched because we do not have the experiment data for that, the same goes for PlxnD1 where we have no experiment flow data. These two networks represent more conceptual discussions, particularly in PlxnD1 case where we have explicitly stated in the new discussion section:

Page 15, lines 24 to 34

There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem?

Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?

We thank the reviewer on this insightful concern. Indeed, the uniqueness of flow and pressure field can be a problem without careful consideration. We have tried to address this to some extent, because CA, CV are connected by the ISV and DLAV network, to match flow velocity in all regions, the pressure distribution ought to be unique to the particular setting we employed.

As shown in table 3, average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain is matched between the simulation and the population-averaged experimental data from the experimental reference (27 fish sampled in the cited reference) for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.

Additionally, we also compared the flow velocities to the experiment conducted within this study (5 WT, and embryos). This comparison data is shown in Table 6. Admittedly the discrepancy was large for CV and ISVs regions likely due to a smaller data set sampled in this study and biological variations that happen from one experiment to another. We have acknowledged this deficiency in the revised discussion section:

Page 15, lines 3 to 9

The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.

We thank the reviewer for this insight. In accordance with the reviewer’s suspicion, we have estimated the flow rates in the CA of gata1 MO injected embryos and found the level to be similar to WT. This supports the reviewer’s opinion that the heart rate similarity indicates cardiac output similarity and not arterial pressure similarity as we previously put forward. Furthermore, we have checked that the gata1 morphants do in fact present reduced ISV diameters. In light of this reinterpretation, we performed an additional zero hematocrit model (model 3 in section 2.1). We have consequently rewritten the entire section on how RBC hematocrit modulates hemodynamics in a microvascular network:

Page 6, line 18 to page 8 line 10.

Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.

We have followed the reviewer’s advice and have analyzed for vessel hydraulic impedance and effective viscosity in all the network models presented. This is included in the main figures and discussion. The vessel impedances are discussed for the various models in these following parts of the manuscript:

Page 9, lines 20 to 29

Page 11, lines 28 to 30

Page 12, line 1 to page 13 line 10

Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification

The SGM diameters have been determined based on geometric averages and not impedance equivalency. The reason why we did this is because the impedance will not be known until the CFD is performed for the WT network. This is because without a pressure distribution (which cannot be determined experimentally) we cannot calculate vessel impedance since only flow can be measured and both flow and pressure are requirements to impedance calculation. Our intention with the SGM is to highlight how geometric averaging of morphological characteristics lead to incorrect flow and stress predictions. However, we understand the reviewer’s sensibility and have revised the entire section of the SGM results. We have now discussed three SGM models with varying degrees of geometry simplification. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. The new findings and discussion can be found in the revised manuscript here:

Page 8, line 19 to page 9 line 36.

As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?

We agree that the intuition feedback depends on the expertise of the investigator. The boundary condition selection is intuitive from the experimental findings and key data like pressures in the network cannot be measured. Furthermore, population-averaged flow data does not always match the flow-to-geometry situations that vary from sample to sample, thus demonstrated by the high margin of prediction discrepancy for flow velocities in table 6. We have discussed these challenges and our recommendations for improvement in the Discussion section:

Page 15, lines 3 to 9

Page 15, lines 35 to 40

Page 16, lines 12 to 15

On the topic of RBC model simplification, we agree with the reviewer that our work suggests the methodology would benefit from a further coarse-graining approach to the RBC phase. Accordingly, we discussed the possibility of using a low-dimensional RBC model already published in literature:

Page 14, lines 13 to 17

The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.

Thank you for referring us to other publications that are related to our study. To our knowledge and after performing publication search on these authors, we find that although Dickinson and colleagues performed experiments to examine the effects of perturbed blood flow on vessel remodelling (Udan et al., 2013), they did not perform any numerical modelling to calculate hemodynamic forces such as WSS and luminal pressure. Instead, changes in vessel morphogenetic process were only correlated with blood flow velocity. In our study, we attempt to quantitatively correlate WSS and pressure distributions within a vascular network. Franco and colleagues (Bernabeu et al., 2014) developed PoINet to model haemodynamic forces in mouse retina model of angiogenesis. From what we understand, PoINet is different from our 3D CFD model by 1) not having red blood cells incorporated in their model and as such, the blood viscosity prediction is modelled using shear-rate dependent formulation and not through red blood cell hematocrit, 2) cross sections of blood vessels are assumed to be circular and therefore have no irregularity and 3) live imaging of blood flow is difficult in mouse retina therefore preventing accurate boundary conditions for the model.

We have included the reference to work of Franco and colleagues:

Page 14, line 28 to line 31

Page 9, lines 12 to 14

Freund JB indeed has had extensive work on RBC and cellular flow in microvessels. We have included a reference of his work in:

Page 14, lines 22 to 25.

Reviewer #1 (Significance (Required)):

The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.

We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.

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

Summary: The authors report corroborating numerical-experimental studies on the relationship between morphological alterations (e.g. vessel lumen dilation/constriction, network mispatterning) and hemodynamical changes (e.g. variation in flow rate, pressure, wall shear stress) in the vascular network of zebrafish trunk circulation. Various physiological or pathological adaptation scenarios were proposed and tested, with a range of simulation and experiment models. Where I found it a solid piece of work supported by abundant data, certain aspects need to be clarified/enhanced to improve the scientific rigor and potential impact of the manuscript. Below are my detailed comments in the hope of helping the authors improve the manuscript's quality.

Major comments:

1. Cellular blood flow in vascular networks has been extensively studied in recent years by existing computational models (some of which were published open-source) with similar methods and features to the one proposed by the present work. Can the authors be more explicit about the original contributions of the current model, and provide evidence accordingly (e.g. Github repository or code resources)

The RBC model is essentially the model developed by Fedosov and colleagues (Fedosov, et al., 2010). Likewise, the LBM solver for fluid flow calculation is not. Following the reviewer’s advice, we have removed the details of these non-novel aspects of the methodology and placed them in sections E and F of supplementary material instead. The new Models and methods now show condensed descriptions of the three numerical solvers used and the addition of a grid independence matrix discussion section:

Page 17, line 8 to page 20, line 33.

Crucial details for the simulation setup and model configuration are missing. What were the exact boundary conditions (e.g. inlet and outlet pressures) and initial conditions (e.g. feeding hematocrit of RBCs), and how the numerical-experimental validation process of "to match the velocities of various segments of the network by iteratively altering the pressure inputs ..." as stated on page 13 (lines 1-2) was performed for simulations in this work?

We apologize for the vagueness of our description on how numerical to experimental validations were performed. As replied to reviewer 1 for a similar clarification, we have indicated in Table 3 how average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain were matched between the simulation and the population-averaged experimental data for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.

With regards to what iterative alterations of pressure inputs mean, we monitored the average systolic peak velocities and hematocrit levels in CA, CV and ISVs in intervals of 5 cardiac cycle intervals before manually correcting the pressure input levels to better match average systolic peak velocities in these vessels from the experiment averages. Since we are using population averaged flow data, we do not expect their levels to match the levels in a particular fish-specific geometry, the degree of discrepancy between experiment averages and the model predictions of systolic velocities can be large (Table 6). Admittedly, this is one of the weaknesses of our approach and this limitation is stated in the Discussion section:.

Page 15, lines 3 to 9

As RBC flow typically requires roughly 5 cardiac cycles of flow to reach flow development this process of iterative correction typically takes place over 10 to 20 cardiac cycles. We understand that validation may be a subject of keen interest to readers, hence we have now briefly described the solution initialization and flow development protocol in our modeling approach here:

Page 6, lines 5 to 8

What lattice resolution was used for the flow solver and was the RBC membrane mesh chosen accordingly? Were there any sensitivity analysis (regarding pressure input) or grid-independence study (regarding lattice resolution)

We originally decided on the grid (∆X) and time (∆T) discretization resolutions (0.5 µm and 0.5 µs) based on the acceptable computing turnaround time for each model within our scale of resources. We have now included a section on the grid independence matrix in Models and Methods:

Page 19, line 20 to page 20, line 33

Details of the statistical tests (type of tests used, assessment of data normality, sample size etc.) should be given in the figure caption where applicable (e.g. Fig. 3C, Figs. 7-9).

We apologize for the lack of clarity. All statistical tests used have now been mentioned at least once in each section of results and also in Figure captions wherever significance bars are displayed.

The regression models should also be used with caution, e.g. in Fig. 4B, why should data from two different fish types, namely Gata1 MO and WT, be grouped to fit a linear regression model?

We understand the reviewer’s concern that two population data sets should not be carelessly pooled together for regression analysis without adequate justification. In this case we are utilizing gata1 morpholino injection as a means to alter hematocrit level. There is no reported side-effect as to the best of our knowledge, only hematocrit and possibly hemodynamics and morphological response related to hematocrit level should be affected. Moreover, we have mislabelled the companion set to the gata1 morpholino as WT, the data is in fact data from control morphants and not WT. This change has been applied to Fig. 3 graphs and Table 4 and results section:

Page 7, lines 3 to 16

Finally, as we want to generate a continuum range of varying hematocrit for embryos of the same developmental age. In this regard, we think that within the scope of our intentions and well-accepted usage of gata1 morpholino as a hematocrit reduction protocol it is reasonable to pool the two data sets together for regression analysis.

4.I found the data presented in Fig. 7 insufficient to confidently exclude the numerical models 2, 3 but favor model 1 as the adaptation scenario for the Marcksl1KO case. The first question is, how are the threshold RBC perfusion levels determined to categorize the experimented Marcksl1KO fishes into four groups, i.e. "high", "moderate", "low", "zero"? The authors also need to justify why the "high", "moderate", "low" groups can be mapped to the three modelling scenarios (namely models 1, 2, 3) is it just because "a qualitative match with the experimental trend of ascending CA blood velocity" (Fig. 7F)?

We thank the reviewer for his interpretation of our results. Firstly, we apologize for generating the confusion but we are not trying to map simulation models 1, 2 and 3 to high moderate and low groups respectively in Fig. 7. The high, moderate and low categorizations of experimental Marcksl1 KO phenotypes are based on RBC flux levels observed experimentally. We are trying to ascertain which Marcksl KO phenotype the models 1, 2 and 3 fit, if they do fit the experiment trend at all.

Second, in Fig. 7C, it is shown that no significant difference exists between the "high" group and the WT in their average ISV diameter, then what is defining that group as Marcksl1KO type ?

We apologize for the confusion generated. High flow phenotype is similar to WT flow, the diameter is also similar to WT. In Marcksl1 KO mutants we don’t always see clear phenotyping and often a range is presented from mutant to mutant. Hence the high group is essentially morphometrically and hemodynamically similar to WT, the only reason we know it is a mutant because we have genotyped the zebrafish (marcksl1a-/-;marcksl1b1-/-).

Third, a central assumption here is using heart rate as a measure of the pressure drop in different fish individuals (Fig. 7D). Can't two fishes with similar heart rate have distinct pressure drops in the trunk due to difference in network architecture and topology, vice versa?

We agree with the reviewer’s opinion and now feel that our initial proposition was naïve. After addressing the interpretation of heart rate similarity in the gata1 morphants with more convincing CA flow rate estimations, we now believe that heart rates might not be useful indicators of flow or pressure levels in the network. Instead, cardiac output in the form of CA flow rate as reviewer 1 has suggested might be a better indicator. As the reanalysis has dismantled the earlier interpretation, and found that based on the flow rate estimation for the CA, Marcksl1 KO networks have reduced blood flow rates in the CA.

Page 11, lines 9 to 20

This finding has been incorporated into the consideration of flow adaptation scenarios predicted by the simulation models accordingly in the revised manuscript:

Page 12, line 1 to page 13, line 10

Fourth, the authors should explain why a power-law fit (note that it is not "exponential" as stated on page 10, line 3) should be adopted for the regression analysis in Figs. 7E-v,vi (a useful reference may be Joseph et al. eLife 2019: 10.7554/eLife.45077).

We thank the reviewer for the useful reference and the careless mislabeling of regression curve used. This figure has been redone and a linear regression is instead used that does not attempt to imply any physical law for a power or exponential fitting.

Change made: Fig. 7C

Minor comments:

1. The state of art of cell-resolved blood flow models employed to simulate microcirculatory hemodynamics is not accurately described in the introduction (page 4). More recent works should be cited and critically reviewed to present a fair view on the novelty of the computational model developed herein.

We apologize that the models were mentioned in a passing manner. However ,the need for brevity in introduction somewhat limits their expansion. We have instead gave more direct discussion on similar studies and their relevance to our present work in the Discussion section:

Page 14, lines 13 to 31

It is unclear what "realistic representation of local topologies in the network" (page 7, lines 28-31) means as a claim of novelty. If it means vessel "diameter variation", this geometric feature has been modeled by the works the author referenced (namely Roustaei et al. 2022, Zhou et al. 2021). If it means something else, for example, unsmooth or non-circular vessel surface (or "irregularity of the local endothelium surface" as mentioned on page 5, line 2), then strangely the effects of such features are actually not described in the manuscript.

We apologize for not meeting the expectation of novelty as claimed. We see value in the SGM study matrix have now generated data on three SGM scenarios. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. Essentially the comparison between SGM1 and SGM2 highlights the role of luminal cross-sectional shape skewness while SGM2 to SGM3 highlights the role of axial variation in luminal diameter. With this new SGM data set, we think we can better qualify the aspiration of demonstrating how vessel shape “irregularities” can alter network hemodynamics. The new findings and discussion can be found in the revised manuscript here:

Page 8, line 19 to page 9 line 36.

Why should Fig. 8 contain data from Marcksl1KO model 2? The scenario underlying model 2 was rejected earlier in the manuscript (see point 6 above), and the Marcksl1KO model 2 data are not mentioned in the text when describing the results of Fig. 8, either.

We have reanalyzed the experiment trend and rewritten the outcome of this results section. In summary, both models 1 and model 2 meet the trend of flow rate reduction (with respect to WT levels) in the CA observed in the experiment. Hence, model 2 inclusion is relevant to the WSS analysis. The changes pertaining to this can be found here:

Page 11, line 9 to page 13 line 10.

It is a dense article with loads of data, which is an advantage but only if appropriately streamlined. More subheadings should be considered, especially for section 2.3 (for which the current subsections appear mistaken, 2.3.1 followed by 2.4.2) The manuscript could also benefit from restructuring through optimal combination of simulation visualizations and quantitative analyses. For example, in Fig. 6, not all simulation snapshots are needed here (it is difficult to visually compare the changes between different cases), whereas some quantification in the form of histograms or boxplots will be handy for the readers to note the variation of WSS magnitudes and ranges.

Thank you for the advice, we removed the unnecessary graphical plots and refer to simulation videos in supplementary data instead for such cases. The bad indexing of results subsections has been fixed, while new subsections have been made for better directional narrative to the paper. These changes are colored in red throughout the revised results section:

Page 4, line 37 to page 13 line 39

Related to point 8, the authors could also consider integrating or synthesizing the analyses for individual aISVs and vISVs presented in various figures. Current descriptions for the ISV data appear scattered with frequent exceptions to the summarized trends or relationships. Some minor formatting issues should also be addressed, e.g. the confusing color codes in Figs. 9D-i, E-i.

Thank you for the advice, we have now pooled aISVs together into one group and vISVs into another, instead of discussing data trends on each of the 10 ISVs.

The mispattening case presented in the end of the results section (section "2.4.2") is interesting but appears loosely connected to the preceding contents. Also, it seems not even mentioned in the discussion section.

We agree that the mispatterning case has been only tangentially relevant to the rest of the manuscript. We have linked the topic thematically by network alterations transforming network flows. It is also now included in the discussion section here:

Page 15, lines 30 to 34

Finally, apart from the effect of topological features on local blood flow, the authors should consider the global flow redistribution arising from the network structure (useful refs. Include Chang et al. PLOS Computational Biology 2017: 10.1371/journal.pcbi.1005892; Meigel et al. Physical Review Letters 2019: 10.1103/PhysRevLett.123.228103; Schmid et al. eLife 2021: 10.7554/eLife.60208).

Thank you for the additional references. These are solid pieces of work that have been added to the discussion here:

Page 16, lines 3 to 10

**Referees cross-commenting**

This review report resonates with mine from an experimental perspective and I agree with all points made regarding issues of the current manuscript that the authors need to address with a revised version.

Reviewer #2 (Significance (Required)):

Significance: The particular merit of the work lies in its comprehensiveness of design and abundance of data, which will be of great interest to both the computational and experimental communities in this research field. However, some crucial details (especially with respect to the modelling aspects) are missing, thus hampering the scientific rigor and potential impact of the work. Furthermore, certain justifying statements appear speculative and inconclusive to explain the obtained data, especially regarding the effect of boundary conditions and systemic parameters. The citation of references (some not cited, some cited already but not properly discussed) also needs to be enhanced with engaging discussions to better bridge the findings of the current work (e.g. RBC partitioning in vascular network, effect of WSS on vasculature morphogenesis) with recent works on this research topic.

References

Fedosov DA, Caswell B, Karniadakis GE. 2010. A Multiscale Red Blood Cell Model with Accurate Mechanics, Rheology, and Dynamics. Biophys J 98:2215–2225. doi:10.1016/j.bpj.2010.02.002

Freund JB, Goetz JG, Hill KL, Vermot J. 2012. Fluid flows and forces in development: functions, features and biophysical principles. Dev Camb Engl 139:1229–45. doi:10.1242/dev.073593

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors report corroborating numerical-experimental studies on the relationship between morphological alterations (e.g. vessel lumen dilation/constriction, network mispatterning) and hemodynamical changes (e.g. variation in flow rate, pressure, wall shear stress) in the vascular network of zebrafish trunk circulation. Various physiological or pathological adaptation scenarios were proposed and tested, with a range of simulation and experiment models. Where I found it a solid piece of work supported by abundant data, certain aspects need to be clarified/enhanced to improve the scientific rigor and potential impact of the manuscript. Below are my detailed comments in the hope of helping the authors improve the manuscript's quality.

Major comments:

1. Cellular blood flow in vascular networks has been extensively studied in recent years by existing computational models (some of which were published open-source) with similar methods and features to the one proposed by the present work. Can the authors be more explicit about the original contributions of the current model, and provide evidence accordingly (e.g. Github repository or code resources)?
2. Crucial details for the simulation setup and model configuration are missing. What were the exact boundary conditions (e.g. inlet and outlet pressures) and initial conditions (e.g. feeding hematocrit of RBCs), and how the numerical-experimental validation process of "to match the velocities of various segments of the network by iteratively altering the pressure inputs ..." as stated on page 13 (lines 1-2) was performed for simulations in this work? What lattice resolution was used for the flow solver and was the RBC membrane mesh chosen accordingly? Were there any sensitivity analysis (regarding pressure input) or grid-independence study (regarding lattice resolution)?
3. Details of the statistical tests (type of tests used, assessment of data normality, sample size etc.) should be given in the figure caption where applicable (e.g. Fig. 3C, Figs. 7-9). The regression models should also be used with caution, e.g. in Fig. 4B, why should data from two different fish types, namely Gata1 MO and WT, be grouped to fit a linear regression model? 4.I found the data presented in Fig. 7 insufficient to confidently exclude the numerical models 2, 3 but favor model 1 as the adaptation scenario for the Marcksl1KO case. The first question is, how are the threshold RBC perfusion levels determined to categorize the experimented Marcksl1KO fishes into four groups, i.e. "high", "moderate", "low", "zero"? The authors also need to justify why the "high", "moderate", "low" groups can be mapped to the three modelling scenarios (namely models 1, 2, 3); is it just because "a qualitative match with the experimental trend of ascending CA blood velocity" (Fig. 7F)? Second, in Fig. 7C, it is shown that no significant difference exists between the "high" group and the WT in their average ISV diameter, then what is defining that group as Marcksl1KO type? Third, a central assumption here is using heart rate as a measure of the pressure drop in different fish individuals (Fig. 7D). Can't two fishes with similar heart rate have distinct pressure drops in the trunk due to difference in network architecture and topology, vice versa? Fourth, the authors should explain why a power-law fit (note that it is not "exponential" as stated on page 10, line 3) should be adopted for the regression analysis in Figs. 7E-v,vi (a useful reference may be Joseph et al. eLife 2019: 10.7554/eLife.45077).

Minor comments:

1. The state of art of cell-resolved blood flow models employed to simulate microcirculatory hemodynamics is not accurately described in the introduction (page 4). More recent works should be cited and critically reviewed to present a fair view on the novelty of the computational model developed herein.
2. It is unclear what "realistic representation of local topologies in the network" (page 7, lines 28-31) means as a claim of novelty. If it means vessel "diameter variation", this geometric feature has been modeled by the works the author referenced (namely Roustaei et al. 2022, Zhou et al. 2021). If it means something else, for example, unsmooth or non-circular vessel surface (or "irregularity of the local endothelium surface" as mentioned on page 5, line 2), then strangely the effects of such features are actually not described in the manuscript.
3. Why should Fig. 8 contain data from Marcksl1KO model 2? The scenario underlying model 2 was rejected earlier in the manuscript (see point 6 above), and the Marcksl1KO model 2 data are not mentioned in the text when describing the results of Fig. 8, either.
4. It is a dense article with loads of data, which is an advantage but only if appropriately streamlined. More subheadings should be considered, especially for section 2.3 (for which the current subsections appear mistaken, 2.3.1 followed by 2.4.2). The manuscript could also benefit from restructuring through optimal combination of simulation visualizations and quantitative analyses. For example, in Fig. 6, not all simulation snapshots are needed here (it is difficult to visually compare the changes between different cases), whereas some quantification in the form of histograms or boxplots will be handy for the readers to note the variation of WSS magnitudes and ranges.
5. Related to point 8, the authors could also consider integrating or synthesizing the analyses for individual aISVs and vISVs presented in various figures. Current descriptions for the ISV data appear scattered with frequent exceptions to the summarized trends or relationships. Some minor formatting issues should also be addressed, e.g. the confusing color codes in Figs. 9D-i, E-i.
6. The mispattening case presented in the end of the results section (section "2.4.2") is interesting but appears loosely connected to the preceding contents. Also, it seems not even mentioned in the discussion section.
7. Finally, apart from the effect of topological features on local blood flow, the authors should consider the global flow redistribution arising from the network structure (useful refs. Include Chang et al. PLOS Computational Biology 2017: 10.1371/journal.pcbi.1005892; Meigel et al. Physical Review Letters 2019: 10.1103/PhysRevLett.123.228103; Schmid et al. eLife 2021: 10.7554/eLife.60208).

Referees cross-commenting

This review report resonates with mine from an experimental perspective and I agree with all points made regarding issues of the current manuscript that the authors need to address with a revised version.

Significance

The particular merit of the work lies in its comprehensiveness of design and abundance of data, which will be of great interest to both the computational and experimental communities in this research field. However, some crucial details (especially with respect to the modelling aspects) are missing, thus hampering the scientific rigor and potential impact of the work. Furthermore, certain justifying statements appear speculative and inconclusive to explain the obtained data, especially regarding the effect of boundary conditions and systemic parameters. The citation of references (some not cited, some cited already but not properly discussed) also needs to be enhanced with engaging discussions to better bridge the findings of the current work (e.g. RBC partitioning in vascular network, effect of WSS on vasculature morphogenesis) with recent works on this research topic.

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Referee #1

Evidence, reproducibility and clarity

The manuscript presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.

The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.

It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ? There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem? Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?

The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.

Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.

Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification

As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?

The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.

Significance

The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.

We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.

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Reply to the reviewers

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

The current study uses 3D organotypic rafts to culture primary keratinocytes from Foreskin, Tonsil and Cervix. Further the authors looked at the transcriptomic profiles of each tissue types to study similarities and differences depending on the tissue of origin as well as show the similarity in the tissue specific gene signatures and the ex-vivo samples (data from GTEx). As mentioned by authors Skin and Cervix keratinocytes have been previously cultured on collagen rafts however extending it to Tonsil provides resource and possibility of growing more tissue specific epithelial cells in 3D.

Major comments 1. As the papers focus is to culture epithelial/ epidermal cells on 3D rafts, methods section needs more details about the raft composition, preparation, fibroblast embedding what was the plate size used for raft preparation and culturing of cells on those rafts. What culture media was used for epithelial raft cultures?

We have a detailed published protocol that highlight these details. However, we will expand on some of these details in the manuscript

Results: Figure 1, authors show IF staining's for COL17A1 as marker for basal cells and cornulin for differentiated layers. However, it is important to show how many cells in the basal layer are proliferative? (or how many layers of proliferative cells are present in different epithelia analysed here?) after 14 days majority of cells might already start losing their stemness potential (maybe staining for at least ki67 if staining for basal stem cell marker not possible? Along with loricrin or Involucrin might be good idea).

We will stain for ki67 as suggested. However, based on published data using these raft cultures, we do not expect that many cells will be positive.

This is also important as from supp fig 3 you can see F1 has higher expression of Loricrin, filaggrin etc as compared to all other samples indicating higher diff in this sample. Also, if authors can comment on what was the passage of cells used? And have they observed any difference in the re-epithelization in early passage versus late passage of keratinocytes?

We will expand on this is the updated manuscript. Importantly, we grow these cells in a rho-kinase inhibitor that ‘conditionally’ immortalizes these cells as described (DOI: 10.1172/JCI42297).

It is interesting to see Tonsillar 3D epithelia recapitulate the crypt and surface epithelia and authors also show this with gene expression profile, if possible (Optional), can authors show staining for crypt specific and surface specific markers.

We agree that this is an important control. This will be included.

For all the Supplementary tables where only Ensembl ids are represented, please add gene Id column alongside (it is easier to get biological context from gene id for the reader rather than looking up Ensembl ids). Rename the file names to include the Supplementary file 1, 2, 3?

Since there is 1-to-1 conversion for Ensembl to Gene Id, we elected to not include these. The online app does try tp accommodate this as much as possible. We propose to include two versions of each table. 1 with Ensemble ids only and one with both IDs.

Its excellent to see that in vitro tissue signature matched the in vivo tissue samples (Figure 8) but it will be interesting to show the gene expression differences if found any between the in vitro and in vivo samples that will give insight on the changes as result of in vitro system.

Since the in vivo data will be a mixture of epithelial cells and stroma, these comparisons are not straightforward. However, we are currently examining the use of existing scRNA-Seq data to begin addressing these concerns. This data will be included in the next revision.

Minor comments

1. Abstract: Give sample number (n?) and brief results about the genes that had tissue specific expression pattens.
2. Gene names needs to be in Italics throughout.
3. Introduction: page 5 line 9, authors claim that they based on comparisons they can "identify potential therapeutic targets for various disease" I think this statement either needs experimental evidence or statement / claim needs to be modified.
4. Data submission to GEO???
5. Typo (page 15, line 16 should be "HFK-down", same on page 23 "ectocervix", "endocervix", "uterus", so on, please correct, comma needs to be placed after "
6. Page 24 last line is the heatmap referred here Fig 9B?
7. Fig. 1 legends please indicate what F1, F2, F3, C1--- T1--- represent. Fig 1C Please add axis range/ values for protein atlas data as well.
8. Can authors comment in discussion how was current 3D cervix cells on raft method different from Meyers, C., 1996 3D system?

All these ‘minor’ comments will be addressed.

Reviewer #1 (Significance (Required)):

This article does extend and validate the 3D raft culture method to different epithelial tissues in addition to Skin and cervix. This will be useful for the researchers using co culture systems and interested in understanding epithelial cell and immune cell interactions or host pathogen interacts etc

Describe your expertise: establishing and maintaining primary skin and oral keratinocyte cultures on feeders and 3D cultures on DEDs, Organoid cultures from oral keratinocytes, Oral cancer biology, Histopathology, transcriptomics study, Immuno-oncology.

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

Summary Jackson et al.'s manuscript describes an experiment that directly compares 3D organotypic assays created with primary human epithelial cells from foreskin, cervix and tonsil using histological and bulk RNA sequencing approaches. The authors convincingly show the retention of site-specific histological and transcriptomic differences between the stratified epithelial tissues in culture. Differentially expressed genes are identified and pathway analyses suggest genes that might be involved in the different differentiation processes between these tissue sites and differential regulation of ECM and immune pathways. Differentially expressed genes are used to develop a classifier for tissue identification, which is tested using GTEx data.

Major Comments • The interferon stimulated genes of B cells and macrophages (from Mostafavi et al., 2016) are likely to be very different from those in epithelial cells, so the analysis presented in Figure 9 seems like a stretch to me.

We will include caveats to this interpretation. We are planning stimulation experiments of each tissue to compare IFN responses. However, depending on the outcomes, these may end up being outside of the scope of the current manuscript.

• OPTIONAL: Further data comparing the nature and magnitude of the interferon responses of the three epithelia would improve interest in the manuscript but are not necessary for publication of the current dataset.

See above

Minor Comments • Details of n numbers and what each point represents should be added to Figure 1C. Are these points measurements from 25 um intervals of just one raft per donor? What are 'fields of view' here? Are measurements from one section or from multiple sections per raft? • Page 12 - provide a figure/panel citation for the "micrograph derived from a tonsillectomy" that is suggested for comparison. • In Figure 1 - Figure Supplement 1, how representative of the whole raft are these images? Does the extent of stratification change near to the edge of the collagen gel, for example? How well matched for location within a raft are the images shown? • Page 24 - clarify uses of the phrase "down-regulated in tonsils". Presumably this section refers to tonsil epithelium in 3D organotypic rafts.

Typos • Page 3 - "the cervix is lined with stratified squamous epithelia", should be epithelium. • "J.G. Rheinwald" in in text references. • Page 6 - 'or' not 'and' in first sentence of primary cell culture section.

All these ‘minor’ comments and typos will be addressed.

Reviewer #2 (Significance (Required)):

This highly descriptive study provides a detailed analysis of a bulk RNA sequencing experiment comparing foreskin, cervix and tonsil 3D organotypic rafts. Retained histological and transcriptional differences between epithelial tissues of different origins in organotypic assays are well documented in the literature (e.g., parmoplantar vs non-parmoplantar skin, PMID: 36732947; airway tract, PMID: 32526206) so the observed differences between these three very distinct anatomical tissues are unsurprising overall. The data have been made available via SRA and a shiny web app and are likely to be of interest and use to other researchers working on these tissues in culture. The experiment was performed in matched cell culture conditions so replicates are well-controlled, if limited in number (n=3).

We appreciate this feedback. We agree this is a descriptive study. Nonetheless, we believe there is value in formally demonstrating differences and similarities between these tissues. The provided references will be included to expand our discussion.

I am an epithelial cell biologist specializing in human cell culture models. I do not have sufficient computational background to comment in detail on the RNA sequencing methods or analysis within the manuscript.

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

This is very carefully analysed and written study describing the transcriptional differences between in vitro models of epithelia derived from cervix, foreskin and tonsil tissues. Importantly, they compare the findings to in vivo samples using publicly available data. The findings are significant and will be of interest to the scientific community. I cannot fault the analysis pathways or the conclusions, and the manuscript is a pleasure to read. I recommend it is accepted for publication as is.

Reviewer #3 (Significance (Required)):

This is an important study that is highly significant for researchers interested in epithelia tissue and infection. The data are clearly presented and the analysis is thorough. The authors state that they will make the data publicly available. This will be an important resource for the community.

We appreciate the kind words

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Referee #3

Evidence, reproducibility and clarity

This is very carefully analysed and written study describing the transcriptional differences between in vitro models of epithelia derived from cervix, foreskin and tonsil tissues. Importantly, they compare the findings to in vivo samples using publicly available data. The findings are significant and will be of interest to the scientific community. I cannot fault the analysis pathways or the conclusions, and the manuscript is a pleasure to read. I recommend it is accepted for publication as is.

Significance

This is an important study that is highly significant for researchers interested in epithelia tissue and infection. The data are clearly presented and the analysis is thorough. The authors state that they will make the data publicly available. This will be an important resource for the community.

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

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Referee #2

Evidence, reproducibility and clarity

Summary

Jackson et al.'s manuscript describes an experiment that directly compares 3D organotypic assays created with primary human epithelial cells from foreskin, cervix and tonsil using histological and bulk RNA sequencing approaches. The authors convincingly show the retention of site-specific histological and transcriptomic differences between the stratified epithelial tissues in culture. Differentially expressed genes are identified and pathway analyses suggest genes that might be involved in the different differentiation processes between these tissue sites and differential regulation of ECM and immune pathways. Differentially expressed genes are used to develop a classifier for tissue identification, which is tested using GTEx data.

Major Comments

• The interferon stimulated genes of B cells and macrophages (from Mostafavi et al., 2016) are likely to be very different from those in epithelial cells, so the analysis presented in Figure 9 seems like a stretch to me.
• OPTIONAL: Further data comparing the nature and magnitude of the interferon responses of the three epithelia would improve interest in the manuscript but are not necessary for publication of the current dataset.

Minor Comments

• Details of n numbers and what each point represents should be added to Figure 1C. Are these points measurements from 25 um intervals of just one raft per donor? What are 'fields of view' here? Are measurements from one section or from multiple sections per raft?
• Page 12 - provide a figure/panel citation for the "micrograph derived from a tonsillectomy" that is suggested for comparison.
• In Figure 1 - Figure Supplement 1, how representative of the whole raft are these images? Does the extent of stratification change near to the edge of the collagen gel, for example? How well matched for location within a raft are the images shown?
• Page 24 - clarify uses of the phrase "down-regulated in tonsils". Presumably this section refers to tonsil epithelium in 3D organotypic rafts.

Typos

• Page 3 - "the cervix is lined with stratified squamous epithelia", should be epithelium.
• "J.G. Rheinwald" in in text references.
• Page 6 - 'or' not 'and' in first sentence of primary cell culture section.

Significance

This highly descriptive study provides a detailed analysis of a bulk RNA sequencing experiment comparing foreskin, cervix and tonsil 3D organotypic rafts. Retained histological and transcriptional differences between epithelial tissues of different origins in organotypic assays are well documented in the literature (e.g., parmoplantar vs non-parmoplantar skin, PMID: 36732947; airway tract, PMID: 32526206) so the observed differences between these three very distinct anatomical tissues are unsurprising overall. The data have been made available via SRA and a shiny web app and are likely to be of interest and use to other researchers working on these tissues in culture. The experiment was performed in matched cell culture conditions so replicates are well-controlled, if limited in number (n=3).

I am an epithelial cell biologist specializing in human cell culture models. I do not have sufficient computational background to comment in detail on the RNA sequencing methods or analysis within the manuscript.

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Referee #1

Evidence, reproducibility and clarity

The current study uses 3D organotypic rafts to culture primary keratinocytes from Foreskin, Tonsil and Cervix. Further the authors looked at the transcriptomic profiles of each tissue types to study similarities and differences depending on the tissue of origin as well as show the similarity in the tissue specific gene signatures and the ex-vivo samples (data from GTEx). As mentioned by authors Skin and Cervix keratinocytes have been previously cultured on collagen rafts however extending it to Tonsil provides resource and possibility of growing more tissue specific epithelial cells in 3D.

Major comments

1. As the papers focus is to culture epithelial/ epidermal cells on 3D rafts, methods section needs more details about the raft composition, preparation, fibroblast embedding what was the plate size used for raft preparation and culturing of cells on those rafts. What culture media was used for epithelial raft cultures?
2. Results: Figure 1, authors show IF staining's for COL17A1 as marker for basal cells and cornulin for differentiated layers. However, it is important to show how many cells in the basal layer are proliferative? (or how many layers of proliferative cells are present in different epithelia analysed here?) after 14 days majority of cells might already start losing their stemness potential (maybe staining for at least ki67 if staining for basal stem cell marker not possible? Along with loricrin or Involucrin might be good idea). This is also important as from supp fig 3 you can see F1 has higher expression of Loricrin, filaggrin etc as compared to all other samples indicating higher diff in this sample. Also, if authors can comment on what was the passage of cells used? And have they observed any difference in the re-epithelization in early passage versus late passage of keratinocytes?
3. It is interesting to see Tonsillar 3D epithelia recapitulate the crypt and surface epithelia and authors also show this with gene expression profile, if possible (Optional), can authors show staining for crypt specific and surface specific markers.
4. For all the Supplementary tables where only Ensembl ids are represented, please add gene Id column alongside (it is easier to get biological context from gene id for the reader rather than looking up Ensembl ids). Rename the file names to include the Supplementary file 1, 2, 3?
5. Its excellent to see that in vitro tissue signature matched the in vivo tissue samples (Figure 8) but it will be interesting to show the gene expression differences if found any between the in vitro and in vivo samples that will give insight on the changes as result of in vitro system.

Minor comments

1. Abstract: Give sample number (n?) and brief results about the genes that had tissue specific expression pattens.
2. Gene names needs to be in Italics throughout.
3. Introduction: page 5 line 9, authors claim that they based on comparisons they can "identify potential therapeutic targets for various disease" I think this statement either needs experimental evidence or statement / claim needs to be modified.
4. Data submission to GEO???
5. Typo (page 15, line 16 should be "HFK-down", same on page 23 "ectocervix", "endocervix", "uterus", so on, please correct, comma needs to be placed after "
6. Page 24 last line is the heatmap referred here Fig 9B?
7. Fig. 1 legends please indicate what F1, F2, F3, C1--- T1--- represent. Fig 1C Please add axis range/ values for protein atlas data as well.
8. Can authors comment in discussion how was current 3D cervix cells on raft method different from Meyers, C., 1996 3D system?

Significance

This article does extend and validate the 3D raft culture method to different epithelial tissues in addition to Skin and cervix. This will be useful for the researchers using co culture systems and interested in understanding epithelial cell and immune cell interactions or host pathogen interacts etc

Describe your expertise: establishing and maintaining primary skin and oral keratinocyte cultures on feeders and 3D cultures on DEDs, Organoid cultures from oral keratinocytes, Oral cancer biology, Histopathology, transcriptomics study, Immuno-oncology.

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Reply to the reviewers

We thank the three reviewers for their thorough evaluation of our work and for their positive and constructive feedback. Below we provide an initial response to these comments, including descriptions of several changes incorporated in our preliminary revision. Please note that introductory and significance comments are not repeated here:

Reviewer 1

In my opinion, the main strength of this work is in the development and use of the original assay for adapter identification. As I already indicated, this is a biologically very important problem for cytoplasmic dynein. Another important strength of the paper is the extension of the work to Drosophila. Demonstration of the fact that Heatr5B is an essential gene, and that the product of this gene is involved in dynein-dependent trafficking in fly embryos makes the results significantly more important.I do not think there are many problems with the results in this manuscript. Generally speaking, the data on biochemical interactions are not as strong as I would like them to be. This is explained mainly by the fact that the authors do not have an expressed recombinant Heatr5B that they can use in biochemical experiments, and they limit their biochemistry by pulling down the protein from cell extracts.

Whilst we are very grateful to the reviewer for their thorough evaluation of our work, we do not understand this particular comment. We did include data with recombinant HEATR5B showing binding in vitro to purified dynein and dynactin complexes. The results are shown in Fig. 2B. We have now made it clearer (from line 153 of the preliminarily revised manuscript) that these experiments used recombinant HEATR5B. We hope in the future to determine the biochemical and structural basis of HEATR5B’s interaction with dynein and dynactin but feel that this goes well beyond the scope of this initial study (which already covers a lot of ground), especially as we have not yet found a way to express HEATR5B fragments (line 151).

This creates one of the few experimental problems with the paper. The authors claim that dynein and dynactin do not compete for Heatr5B binding, and therefore they can bind to both components of the complex at the same time. Unfortunately, I do not think that this claim is justified because concentrations of dynein and dynactin in their pull-down assay are much higher than the concentration of GFP-HEATR5B, and likely that HEATR5B does not saturate the binding sites on the motor complex. Therefore, it is unclear whether dynein and dynactin compete for Heatr5B binding. In any case, the conclusion about the competition cannot be seriously made without analysis of saturation curves.

The purified dynein and dynactin were not in excess to recombinant HEATR5B in this assay (80 pmol HEATR5B, 20 pmol dynein tail and 10 pmol dynactin). Nonetheless, the reviewer makes a very good point that we cannot draw strong conclusions about competition unless we generate saturation curves. We have therefore toned down the interpretation of this experiment and included the caveat raised by the reviewer (from line 157):

‘Compatible with this notion, we did not observe competition between the purified dynein tail and dynactin for HEATR5B binding in our in vitro binding assay when both complexes were added simultaneously to the beads (Figure 2B). However, we cannot rule out the possibility that a competitive interaction was masked by binding sites on one of the components not being saturated. Nonetheless, we can conclude from this set of experiments that HEATR5B complexes with endogenous dynactin and dynein in cell extracts and can interact with both complexes directly.’

Please note that this was only a minor point in our manuscript.

My second concern with this paper is the quality of imaging in mammalian cells. Unfortunately, not much can be done with live cell imaging because GFP-HEATR5B is expressed in cells at a low level (see, for example, Fig. 3A). However, in fixed cells GFP-HEATR5B signal could be easily amplified using anti-GFP antibodies.

The fixed cell images of GFP-HEATR5B cells are stained with anti-GFP antibodies and are the result of extensive optimisation of staining and imaging conditions. Due to its low expression and presence in both cytoplasm and membrane-bound pools, the signal for GFP-HEATR5B is not as striking as, for example, RAB11A and AP1γ. Nonetheless, the punctate signals are sufficiently strong to confidently evaluate co-localisation with membrane markers. We have now added to the relevant legends that the GFP signal is obtained via GFP antibody staining. Please note that the association of GFP-HEATR5B with AP1γ (Fig. 3A, B) was also confirmed by immunoprecipitation (Fig. 2A).

A minor problem with movie presentations is that the authors should include both a timer and a scale bar for all their live cell sequences, especially because the movies are looped. The authors did it for Movie 5, and they should do it for the rest of their live cell sequences.

Although information on the duration of movies (including loops) was included in the legends, we agree that it would be helpful to incorporate timers and scale bars in the movies. We have not been able to include this change in the preliminary revision as we have to co-ordinate with our visual aids team to reapply labels and arrows to the edited movies. This change will be made to the full revision.

In my opinion, the main novelty of this paper is in its pull-down assay, I would like to have it discussed more extensively. The authors state that they "were particularly drawn to Heatr5B". Is there an objective reason for this choice? If so, it should be specified.

We included our two reasons for focusing on HEATR5B in the previous submission, namely that it was the only protein to be enriched on the tail by dynactin in both the N- and C-terminal tethering configuration and that a previous study found it was one of a number of proteins present on dynactin-associated vesicles. We have modified the language in this section (which starts on line 120 of the preliminary revision) by using the connective ‘because’. This change makes it clearer that there were objective reasons for focusing on HEATR5B in the first instance.

Furthermore, I would like to see the authors discuss the other hits. Their list of hits includes a large number of ribosomal proteins. Do ribosomes really interact with dynein? Can the authors speculate on the number of true hits? Finally, it is likely that dynein interacts with some of the cargoes only transiently. How can the assay be modified to capture these transient interactions?

This is another very good suggestion. As requested, we have added a comment to the Discussion (from line 441) about how transient interactions might be captured using a variation of our strategy. We have now added a comment in the Discussion (from line 435) about the capture of ribosomes and other RNA-associated proteins in our screen, as well as the potential significance of this observation. We have also highlighted in this section another dynactin-stimulated hit, Wdr91, which we are following up. We also discussed the STRIPAK complex, which warrants further study, in the Results (line 106). We do not have space to discuss other hits but their identities are listed in Tables S1 and S2 together with a summary of their known functions for easy reference.

Reviewer 2:

Major points:

As a view of non-expert of light microscopy cellular imaging, some confocal images are difficult to accept as proofs of their conclusion that mutation to decrease HEAT5B/AP1 interaction results in diffusion from perinucleolar surface. For example, fluorescent signals in Control of Fig.4A seem more diffused than HR5B KO, which have fluorescence clearly localized on the surfaces of nuclei. Can they have explanation how it ends up with their statistical analysis in Fig.4E?

Fig. 4A is representative of what we typically see in mutant cells, with dispersion of the dimmer AP1γ signal in the cytoplasm and less disturbed localisation of the brighter AP1γ signal at the TGN (see Fig. S6B for quantification of AP1γ signal at the TGN in control and mutant cells). We should have made it clear in the Results that the unbiased image analysis pipeline used to produce Fig. 4E detects the total AP1γ signal not just bright signals (this feature of the pipeline is important given the differences in fluorescent intensity of puncta in the two genotypes). We have now clarified this issue in the Results (line 257) and the Fig. 4E legend. We have also added arrowheads to Fig. 4A to highlight the dispersed dim signal in the mutant cells. We thank the reviewer for leading us to improve the description of this experiment__.__

When they mention statistically more distance between target molecules and the perinuleolar surface, are dynein/dynactin connected to AP1 via HEAT5B stalled on the microtubule before reaching the minus end, or dissociate from the microtubule? Clarifying this will improve impact of this work. If the current data is not enough to answer, this reviewer will propose another confocal microscopy with also tubulin labeled. With this, the location of HEAT5B, AP1 etc. with respect to both nuclei and microtubule cytoskeleton will be clarified.

We would love to know the answer to the question of whether HEATR5B disruption reduces the association of AP1γ with microtubules. We have looked into co-localisation of microtubules and dynein’s cargoes previously using advanced light microscopy and found that it is not possible to draw conclusions about meaningful versus coincidental associations because of the density of the microtubule network. In the case of our current study, this approach would be further confounded by the difference in size in fluorescent AP1 puncta in control and HEATR5B mutant cells. We have also in the past attempted to purify recycling endosomal membranes from cells to determine how loss of HEATR5B influences dynein-dynactin association. However, even after extensive efforts we could not reproduce selective purification of recycling endosomes using the published protocol, or indeed variants of it. What is more, we find in general that there is rapid dissociation of motors during purification of membranes from cells, which would confound our results even if we could purify the recycling compartment. We therefore feel that the only way to address the question of how HEATR5B modulates dynein function at the molecular level is to reconstitute the transport machinery with pure proteins (including the as-of-yet unidentified activating adaptor) and microtubules in vitro, which is beyond the scope of this study. We have discussed the future aim of in vitro reconstitution to dissect mechanism in the Discussion (from line 494).

In Line168-169, they concluded AP1gamma associated with TGN rarely overlapped with HEATR5B, based on Fig.3A (where HR5B and AP1 seem overlapped in HeLa cells), Fig.S2A (where AP1gamma and TGN46 seem overlapped in U2OS cells) and Fig.S2B (where HR5B and TGN46 are not overlapped in HeLa cells). Is Fig.3A not contradictory to their conclusion (AP1gamma and HEATR5B not overlapped)? Why did they not directly check the overlap between AP1gamma and HR5B in the same cell in U2OS cells?

We don’t understand why our co-localisation data might be contradictory to our conclusions. Fig. 3A, together with the associated insets and quantification in Fig. 3B, show overlap of HEATR5B with AP1γ puncta in the cytoplasm of HeLa cells but not the AP1γ that is strong enriched in the perinuclear region, as we stated in the results. Absence of enrichment of HEATR5B with the TGN is additionally shown in Fig. S2B. These observations are commented on further in the Discussion (from line 517). We do, however, agree with the reviewer that is was not ideal that we did not show AP1 and TGN association in a HeLa cell (even though it has been documented in the literature). We have now corrected this oversight by showing HeLa cell data in Fig. S2A. We could not check the overlap of AP1 and HEATR5B in U2OS cells as we do not have a GFP-HEATR5B stable U2OS cell line.

Minor points:

Line100-105 and Fig.1EF are not clear. Is it correct that proteins in red bold letters and in blue letters in Fig.1EF are 28 proteins enriched on the dynactin tail?

We should have been clearer here and thank the reviewer for spotting this. We have modified the figure call outs in the text to include the labelling scheme, which we think helps significantly. We have also clarified the labelling system in the legend. To summarise, bold labelling indicates interactors of the dynein tail that are not core components of the dynein-dynactin machinery (such proteins are labelled in non-bold and italics); the blue bold text shows those ‘none core’ interactors that were only enriched on the dynein tail when exogenous dynactin was spiked into the lysates.

Do authors have any idea why the "dynactin-stimulated" ones (in blue) are localized at left end of this group (relatively less significance of dynactin tail binding, if this reviewer understands correctly)?

This question appears to indicate some confusion about whether we are capturing the dynein tail or dynactin. We believe the changes made in response to the previous comment about the labelling scheme should help clear this up. Being positioned to the left of this grouping shows a lower degree on enrichment vs the control (although still greater than 10 fold), rather than a difference in statistical significance. The observation that core dynein-dynactin subunits are more enriched on the dynein tail indicates that these interactions are the most stable or the most frequent.

Fig.S7: More explanation how to conclude that HR5B KO is dimmer than Ctrl based on this plot would be helpful.

We have added a line to the legend to Figure S7C to clarify this matter.

Reviewer 3:

Minor comments

HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane. To which compartment are these vesicles directed and associated, the Golgi apparatus? Could the authors show which compartment it is?

We plan to perform new experiments to address this minor comment in the full revision. However, given their location near the microtubule organising centre, it is likely that the relocalised membranes will be in the vicinity of the Golgi apparatus.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The goal of the authors is to identify dynein regulators which control how dynein and dynactin complexes orchestrate trafficking of diverse cargoes. To do so, the authors have performed a well thought proteomic screen for novel interacting proteins of the dynein tail potentially enhanced by dynactin. These pull-down experiments identified about 50 new dynein tail-interacting proteins, many of which were enhanced by dynactin.

The authors focused on one candidate, HEATR5B, because it was robustly isolated from the screens and its association with the dynein tail was stimulated by exogenous dynactin. HEATR5B is known to interact with AP1 complex, as adaptors that orchestrate cargo loading of clathrin-coated vesicles from intracellular membranes.

The authors further show that HEATR5B complexes with endogenous dynactin and dynein as reveal by immuno precipitation from human cells extracts and can interact with both complexes directly. Then by using Hela cell line stably expressing GFP-HEATR5B, they show that HEATR5B is selectively enriched on the AP1 structure, some of which can be subjected to long-distance transport. They provide evidences that a large proportion of the HEATR5B-positive structures are associated with endosomal recycling membranes, as revealed by colocalization with RAB11A. They further show that the HEATR5B/ AP1 and HEATR5B/ RAB11 membrane structures show similar dynamics, indicating that HEATR5B associate with endosomal membranes that are capable of directed movement. SiRNA depletion of DYNC1H1 reveals that dynein promotes retrograde trafficking of AP-1 associated endosomal membranes.

The authors then investigate the contribution of HEATR5B to AP1-associated membrane trafficking by CRIPR/cas9-mediated mutagenesis in human U2OS cells that disrupt HEATR5B protein expression. They provide evidences that in HEATR5B mutant cells, there is a reduction in the amount of AP1 signal associated with RAB11A-positive structures indicating that disrupting HEATR5B reduces the association of AP1with endosomal membranes. This indicates that HEATR5B promotes AP1 recruitment to endosomal membranes. HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane, suggesting that HEATR5B can stimulate retrograde trafficking of AP1-associated endosomal membranes by dynein- dynactin.

To assess the importance of HEATR5B function at the organismal level, as well as in polarized cell type the authors investigate its function in Drosophila in which there is a single HEATR5B homologue (Heatr5). They generated via crisper an Heatr5 mutant strain. Heatr5 homozygous mutants are zygotic lethal that died in second larval instar stage. They further provide evidence by investigating nos-cas9 gRNA-Hr51+2 mothers, that Heatr5 plays maternal function essential for embryogenesis. They further show that in early embryos from nos-cas9 gRNA-Hr5 females AP1 puncta are strongly reduced and dimmer.

Next, to understand the effect of Heatr5 disruption on AP1-based trafficking in Drosophila, they used the syncytial blastoderm embryo in which the microtubule cytoskeleton is highly polarized with less apically nucleated ends above the nuclei and more basally extended ends. In this system, the activity of minus end-directed motor, such as dynein, and minus end-directed motor, such as kinesin, can be distinguished by the direction of cargo movement.

By injecting AP1 antibodies into wild-type and Heatr5 mutant embryos, they provide evidence that AP1 undergoes net apical transport in the Drosophila embryo and that this process is strongly promoted by Heatr5. They further show that this process is microtubule and dynein dependent and that Heatr5 selectively promotes dynein-mediated transport of AP1 structures in the embryo. They then show that Heatr5-dependent AP1 trafficking pathways in the embryo involves the endosomal and Golgi membranes and that Heatr5 is also required for Golgi organization.

Major Comments

This study is very comprehensive and multi-scale. It ranges from the identification of a dynein motor adaptor for membrane trafficking by a proteomic screen, to its functional characterization in human cells and then during development with Drosophila embryo as model organism. The data are of high quality and are supported by very convincing quantitative analyses. The results are conclusive and the experiments have been carried out and presented in a very constructive way. This combination makes the manuscript very interesting.

Minor comments

HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane. To which compartment are these vesicles directed and associated, the Golgi apparatus? Could the authors show which compartment it is?

Significance

This study is important in two aspects. Firstly, it has identified HEATR5B as a new adaptor of the dynein motor for intracellular membrane trafficking. It is important to mention that this motor is involved in many transport processes and it is still unclear how a single motor orchestrates the traffic of so many cargoes. Second, this work shed new light on the retrograde trafficking from endosomal material to the Golgi apparatus, in particular with HEATR5B, a known interactor of the AP1 clathrin adapter complex. This study highlights a role of HEATR5B in a novel dynein-based process for retrograde trafficking of AP1-associated endosomal vesicle to the Golgi apparatus. It also indicates that HEATR5B promotes association of AP1 with endosomal membrane in a dynein-independent manner.

This work is particularly important for the cell biology field.

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Referee #2

Evidence, reproducibility and clarity

Major points:

As a view of non-expert of light microscopy cellular imaging, some confocal images are difficult to accept as proofs of their conclusion that mutation to decrease HEAT5B/AP1 interaction results in diffusion from perinucleolar surface. For example, fluorescent signals in Control of Fig.4A seem more diffused than HR5B KO, which have fluorescence clearly localized on the surfaces of nuclei. Can they have explanation how it ends up with their statistical analysis in Fig.4E?

When they mention statistically more distance between target molecules and the perinuleolar surface, are dynein/dynactin connected to AP1 via HEAT5B stalled on the microtubule before reaching the minus end, or dissociate from the microtubule? Clarifying this will improve impact of this work. If the current data is not enough to answer, this reviewer will propose another confocal microscopy with also tubulin labeled. With this, the location of HEAT5B, AP1 etc. with respect to both nuclei and microtubule cytoskeleton will be clarified.<br /> In Line168-169, they concluded AP1gamma associated with TGN rarely overlapped with HEATR5B, based on Fig.3A (where HR5B and AP1 seem overlapped in HeLa cells), Fig.S2A (where AP1gamma and TGN46 seem overlapped in U2OS cells) and Fig.S2B (where HR5B and TGN46 are not overlapped in HeLa cells). Is Fig.3A not contradictory to their conclusion (AP1gamma and HEATR5B not overlapped)? Why did they not directly check the overlap between AP1gamma and HR5B in the same cell in U2OS cells?

Minor points:

Line100-105 and Fig.1EF are not clear. Is it correct that proteins in red bold letters and in blue letters in Fig.1EF are 28 proteins enriched on the dynactin tail? Do authors have any idea why the "dynactin-stimulated" ones (in blue) are localized at left end of this group (relatively less significance of dynactin tail binding, if this reviewer understands correctly)?

Fig.S7: More explanation how to conclude that HR5B KO is dimmer than Ctrl based on this plot would be helpful.

Significance

In this work, Madan and colleagues studied dynein adaptor proteins, which are stimulated by dynactin, using proteomics, fluorescent microscopy, live cell imaging techniques for U2OS and fly embryo cells. They especially focused on HEATR5B and proved its role to bind AP1 membrane associate protein for intracellular transport. They first conducted proteomic studies and presented novel lists of dynein-associated proteins and proteins stimulated by dynactin. Among them they decided to prioritize HEATR5B protein (it would be interesting to know their motivation to choose this protein) and carried on fluorescent microscopy studies to characterize roles of HEATR5B in microtubule-based motility. Their approach using U2OS cells is to correlate distribution of HEATR5B and such proteins as AP1gamma, TGN46, RAB11A, which they expect interaction with HEATR5B, between WT and mutants. They remarkably demonstrated distance from perinucleolar membrane is heavily influenced by defect of adaptor function of HEATR5B, by fluorescent microscopy and statistical analysis. Next they made HEATR5B depleted Drosophila embryo by CRSPR-CAS9. They proved its influence on AP1 trafficking to Golgi, which is another novel finding of this study, consistent with the case of U2OS cells.

In general the whole study proved importance of HEATR5 proteins on AP1 trafficking. Many data are presented in convincing way and carefully statistically analyzed. This work will attract attention of wide audience from the field of cytoskeleton, motor proteins and membrane trafficking. After addressing a few points, the manuscript will be ready for publication.

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Referee #1

Evidence, reproducibility and clarity

This work is the first systematic attempt to identify and characterize a diverse set of adapters that attach cytoplasmic dynein to its different cargoes and thus activate the motor. It is an important work because in animal cells dynein is the only efficient motor that can perform processive transport toward the minus ends of microtubules, and therefore the specificity of transport for multiple cargoes along microtubules is determined by these adapters.

The authors use the recombinant tail of dynein for pulling down interacting proteins from the cell extract. This is a straightforward approach, but its main problem is the large number of non-specific proteins that bind to the column. To solve the problem, the authors use a very smart approach. It is based on the fact that in all known cases so far dynein does not transport cargoes without dynactin, and, therefore, potential adaptors are unlikely to bind to the affinity column very efficiently. They compare pull-downs in the presence and absence of dynactin paying specific attention to proteins that bind in the presence of both dynein and dynactin but not dynein alone.

Among the proteins that have been identified by this assay is Heatr5B, the protein known to associate with AP1 clathrin adaptor. Functional characterization of the protein can be divided into two parts, work with mammalian Heatr5B in tissue culture cells and analysis of its function in Drosophila.

In my opinion, the main strength of this work is in the development and use of the original assay for adapter identification. As I already indicated, this is a biologically very important problem for cytoplasmic dynein. Another important strength of the paper is the extension of the work to Drosophila. Demonstration of the fact that Heatr5B is an essential gene, and that the product of this gene is involved in dynein-dependent trafficking in fly embryos makes the results significantly more important.

I do not think there are many problems with the results in this manuscript. Generally speaking, the data on biochemical interactions are not as strong as I would like them to be. This is explained mainly by the fact that the authors do not have an expressed recombinant Heatr5B that they can use in biochemical experiments, and they limit their biochemistry by pulling down the protein from cell extracts. This creates one of the few experimental problems with the paper. The authors claim that dynein and dynactin do not compete for Heatr5B binding, and therefore they can bind to both components of the complex at the same time. Unfortunately, I do not think that this claim is justified because concentrations of dynein and dynactin in their pull-down assay are much higher than the concentration of GFP-HEATR5B, and likely that HEATR5B does not saturate the binding sites on the motor complex. Therefore, it is unclear whether dynein and dynactin compete for Heatr5B binding. In any case, the conclusion about the competition cannot be seriously made without analysis of saturation curves.

My second concern with this paper is the quality of imaging in mammalian cells. Unfortunately, not much can be done with live cell imaging because GFP-HEATR5B is expressed in cells at a low level (see, for example, Fig. 3A). However, in fixed cells GFP-HEATR5B signal could be easily amplified using anti-GFP antibodies.

A minor problem with movie presentations is that the authors should include both a timer and a scale bar for all their live cell sequences, especially because the movies are looped. The authors did it for Movie 5, and they should do it for the rest of their live cell sequences.

In my opinion, the main novelty of this paper is in its pull-down assay, I would like to have it discussed more extensively. The authors state that they "were particularly drawn to Heatr5B". Is there an objective reason for this choice? If so, it should be specified. Furthermore, I would like to see the authors discuss the other hits. Their list of hits includes a large number of ribosomal proteins. Do ribosomes really interact with dynein? Can the authors speculate on the number of true hits? Finally, it is likely that dynein interacts with some of the cargoes only transiently. How can the assay be modified to capture these transient interactions?

Significance

The bottom line is very clear. For me, it is an excellent technical paper with biological results that clearly demonstrate the validity of the technique. As such, it can and should be published.

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Reply to the reviewers

Manuscript number: RC-2023-01861

Corresponding author(s): Manuela, Baccarini

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1. General Statements [optional]

We were delighted to learn that all three reviewers found the paper novel and of interest for a cell biology audience. They especially highlighted the carefully conducted screen, whose results will be integrally published with this paper and will be of use for scientists interested in lysosome biology.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

Reviewer 1

• The claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central finding of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region.

Answer: We have purchased the RAMP system from Addgene and are adapting it to our color setup to use it in HeLa cells expressing GFP-PLEKHG3 and (hopefully) in PLEKHG3 KO cells, adding LiveAct to investigate cortical actin dynamics upon lysosomal repositioning as well as PLEKHG3 KO.

Reviewer 2

5 - It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.

Answer: Currently, we do not have a PLEKHG3 KO. We have, however, redoubled our efforts, so far unsuccessful, to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. In this case, we will be able to easily address this interesting question.

Reviewer 3

• Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.*

Answer: We have redoubled our efforts to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. This cell line will be helpful in answering the Reviewer’s question.

Mutational analysis cannot be performed, because of the lack of binding between LAMTOR3 and PLEKHG3, which leaves us without a read-out.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer 1:

• The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.

Answer: To assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The results of this experiment are shown in the revised Figure S2B-C. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific (Figure only shown in attached revision plan and revised Figure S2B-C). In addition, we have redoubled our efforts, so far unsuccessful, to generate a PLEKHG3 CRISPR-Cas KO in HeLa cells, going up to 10 sg-guides, and hope that we will be successful in the next future.

Extract from revised Figure S2B-C: ____PLEKHG3 KD test in HEK293T cells: B) Western blot of HEK293T cells showing downregulation of PLEKHG3 expression upon siPLEKHG3 treatment compared to siScr. Bar plot shows quantification of PLEKHG3 bands from immunoblot above. Error bars = SEM, n=3. * = p values according to student's t-test. C) Immunofluorescence images of HEK293T cells. siPLEKHG3 shows drop in PLEKHG3 intensity in the periphery of the cell and less colocalization with Phalloidin. Scale bar = 50 µm. Line plots show intensity profiles of Phalloidin (green) and PLEKHG3 (red) along the white lines in the merged inset images. Scale bar = 10 µm.

• *The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. *

And related to this point:

• There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5.

Answer:

We do not claim that the two structures always colocalize. The images in Figure 3C are a schematic representation of the colocalization analysis shown in the plot and were included to explain how we define PLEKHG3 high/low regions or LAMP1 high/low regions, respectively. We agree with the Reviewer and with the previous literature that PLEKHG3 main localization is to cortical actin structures, as shown in Figure 3F of the original version and in Figure S2C (HEK293T cells) and in Figure S3A in HeLa cells in the revised version. The claim is rather that PLEKHG3 has been identified as a vicinal protein of LAMTOR3, seen by a fraction of lysosomes when they traffic into protrusions. We have clarified the text referring to Figure 3F on page 13, line 7-10 as follows:

"Immunofluorescence experiments showed the reported colocalization of endogenous PLEKHG3 (Figure S2C in HEK293T cells, Figure S3A in HeLa cells) and GFP-PLEKHG3 with cortical actin structures and the partial localization of LAMP1-positive vesicles to these structures in correspondence with vinculin-positive focal adhesions."

This specific claim is also based on the observation made in GFP-PLEKHG3-expressing cells (including movie S5, and particularly the stills of the leading edge in Figure 4F). In the text describing Figure 4F, we now clearly state on page 14, line 15-17: “Following a single cell over time, we could observe that __a subset of __lysosomes appears to travel to PLEKHG3 accumulation sites and specifically move into developing protrusions.”

• It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B.

Answer: We stand corrected – the Figure we referred to was actually not in the manuscript. It has been inserted now, as a plot next to Figure 4B on page 16 Figure 4B (schematic representation of colocalization analysis) was designed to explain how we define focal adhesions (paxillin positive) and adjacent control regions (same size and shape, but paxillin-negative). The actual analysis was missing and has now been inserted. We apologize for this mistake.

We do not claim that PLEKHG3 brings lysosomes to FAs. The enrichment of lysosomes in FA regions of cells expressing GFP-PLEKHG3 compared to GFP-expressing cells shown in 4E, as the Reviewer correctly notes, is marginal and is not highlighted anywhere in the text exactly for this reason.

• In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated.

• AND -Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.

Answer: We stand corrected, and the necessary changes have been made in the revised version in Figure 2B on page 11.

Reviewer 2

*1 - Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKHG3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein". *

In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific and is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.

Answer: We apologize for this misunderstanding. The antibody recognizes three bands, all reduced by siRNA treatment. These three bands are only resolved in the gels in Figure S2A and B, and in Figure 2B. The reason for this is the high molecular weight of the isoforms, that are resolved in these 8% gels, but collapse into one band in the 15% gels shown in Figure 2A and C. Therefore, the high molecular weight bands are not resolved under these conditions. 8% gels such as the ones in Figure 2B are needed to resolve the high molecular weight bands.

Figure 2D shows an 8% gel, and therefore all bands are visible. The band marked by an arrow is only present in the streptavidin pulldowns but not in the input or in the supernatant and is therefore considered unspecific. This has been clarified in the revised figure legend on page 11. In addition, to assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The results of this experiment are shown in the Figure S2B-C of the revised manuscript. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific.

2 - In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.

Answer: This is also a misunderstanding. Unfortunately, we mislabeled Figure 2C as “pulldown”, rather than “IP”, as it is characterized in the text. The fact that we cannot co-ip PLEKHG3 by immunoprecipitating L3 using a V5 antibody led us to conclude that the interaction between the proteins is not direct or stable enough to survive a co-ip. Therefore, the most likely conclusion is that PLEKHG3 is a vicinal protein rather than an interactor of L3 – we changed the labeling of Figure 2C to clarify the issue on page 11.

Based on these negative data, we did not proceed to test the possibility of complex formation in vitro.

3 - Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.

Answer: It was our intention to indicate with the arrows the trajectories in the figure along which we measured the MFI of LAMP1 and PLEKHG3. Although this is indicated in the figure legend, it had apparently given the impression that the arrows indicated specific membrane structures. Since we are focusing on different types of membrane protrusions rather than ruffles, we replaced the terms "ruffles" and "protrusions" with the terms "elongated protrusions" (Figure 3D upper panel) and then compared these with "non" elongated protrusions” (Figure 3D lower panel). Indeed, we note that PLEKHG3 accumulation is possible below and along the plasma membrane, but colocalization with lysosomes occurs preferentially in elongated protrusions. We therefore amended the text on page 12, line 24 – page 13, line 5 as follows:

„More specifically, we found that PLEKHG3 colocalized more strongly with LAMP1-positive vesicles in elongated membrane structures (Figure 3D-E). Focal adhesion sites, which anchor the intracellular cortical actin network to the extracellular matrix and are remodeled with the help of late endosomes/lysosomes during protrusion formation and cell motility, can also be found in such elongated membrane protrusions (reviewed in Burridge and Burridge, 2017; Schiefermeier et al., 2014).”

6 - Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.

Answer: in all our experiments we performed two-group comparisons. We have now deleted “unless otherwise stated” from the Materials and Methods section on page 41, lines 1-2.

*Minor comments: *

*1 - In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains? *

Answer: We apologize for this unclarity and have now changed the first sentence in the abstract on page 1 to “Lysosomes are key organelles involved in metabolic signaling pathways through their ability to recruit cytosolic molecules to protein platforms bound to the lysosomal membrane”. We refer to protein platforms as multifunctional protein complexes that can recruit and assemble signaling components (e.g., the recruitment of mTORC1 activating proteins by the LAMTOR complex).

*2 - In the Introduction, there is a period before the reference at the end of the first paragraph. *

Answer: We stand corrected. See changes on page 3, line 8.

3 - In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.

Answer: Figure S1E on page 6 was mislabeled as Figure 1E and Figure S1K on page 9 was mislabeled as Figure 1K. We stand corrected. See changes on page 6, line 20 and page 9, line 4.

4 - All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.

Answer: We appreciate the Reviewer's suggestion, but enlarging all the immunofluorescence images and including zoom-ins would make the manuscript overly crowded and could distract from the main findings. Regarding the expression levels of the baits, as mentioned in the manuscript, we aimed to express them at near-endogenous levels. However, TMEM192 is expressed at higher levels than LAMTOR3 in these cells, which may have resulted in the observed discrepancy. We hope the Reviewer will understand our decision and find the current presentation of the data clear and informative.

5 - In page 9, where it reads "Figure 1K", should read "Figure S1K".

Answer: See answer to minor point 3.

6 - The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.

Answer: While this might seem the case in part of the cells shown in the representative image in Figure S2C, quantification of lysosome distribution did not show a significant difference throughout the population as displayed in the figure below (Figure only shown in attached revision plan).

__Figure 1 for Reviewer 2: __Lysosomal distribution in HeLa cells transfected with either siScr or siPLEKHG3. X-axis is relative distance from the nucleus and Y-axis the normalized intensity of the LAMP1 channel. Results are averages of >30 cells from one experiment.

7 - Fig. 2C is not referred in the legend.

Answer: We stand corrected and have changed the legend of Figure 2 accordingly on page 11.

8 - Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.

Answer: We thank the Reviewer for this comment and have performed this experiment showing the colocalization of endogenous PLEKHG3 with F-actin structures stained by Phalloidin. Even though the endogenous PLEKHG3 staining in HeLa cells is rather weak, sites where membrane protrusions are formed are clearly marked with PLEKHG3 staining below the plasma membrane. These data confirm the specific colocalization of PLEKHG3 with Phalloidin shown in the revised Figure S3A. See also the extract from Figure S3A below (Figure only shown in attached revision plan and revised Figure S3A).

Extract from revised Figure S3A: Immunofluorescence images of HeLa cells. A) HeLa cells stained with PLEKHG3 (red) and Phalloidin (green). The nucleus is indicated by DAPI staining (blue). Scale bar = 50 µm. Insets on the right as indicated by white box in image on the left. Scale bar = 10 µm. Line plot corresponds to white line in merged inset.

*9 - In page 14, authors refer to Fig. 3G, which does not exist. *

Answer: We stand corrected, the sentence on page 14, line 9 refers to Figure S3G.

10 - In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.

Answer: We tried different PLEKHG3 antibodies but ended up using only one. The other antibody has been excluded from the list on page 32, line 18. We have specified which LAMP1 antibodies were used in which Figure in the Material and Methods on page 30, lines 17.20-23.

11 - In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".

Answer: We stand corrected and thank the Reviewer. See changes on page 33, line 17.

Reviewer 3

• A key issue … is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.*

Answer: The Reviewer is likely addressing the images in Figure 3, which have been obtained by staining endogenous PLEKHG3 and do show diffuse staining around the nucleus. This perinuclear staining is resistant to siPLEHG3 (revised Figure S2C) and is not observed with the GFP-PLEKHG3 fusion protein (revised Figure S2E-F; including PLEKHG3 knockdown), which gives a less diffuse signal. This is why we are confident about the colocalization of PLEKHG3 with peripheral lysosomes. This said, we have redoubled our efforts to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. This cell line will be helpful in answering the Reviewer’s question.

Minor point: 1. Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.

Answer: White as a channel color has been substituted for with red (in the 2- and 3-color images) or with blue (in the 4-color images) throughout the images of the revised manuscript, except for the stills from the videos that have not been changed because no colocalization analysis has been performed in this case.

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Reviewer 2

4 - At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.

Answer: We appreciate the Reviewer’s attention to detail and agree that the quantification of these figures is essential to understand the results. We believe that the Reviewer is referring to Figure 3F and Figure 4A, as there is no Figure 2F, and Figure 3A only confirms the localization of endogenous PLEKHG3, as previously reported in (Nguyen et al., PNAS 2016). If our assumption is correct, then the salient aspects of Figure 3F, which is a representative image, are quantified in Figure 3C-E (endogenous PLEKHG3 colocalization colocalization with LAMP1/lysosomes) and Figure 4E and 5F-G (FA with LAMP1/lysosomes). Figure 4A is quantified in Figure 4C-E (GFP-PLEKHG3 colocalization with FAs, this time labeled with paxillin, and LAMP1 colocalization with FAs).

In response to the Reviewer's comment regarding the absence of quantification for cell movement/migration in our study, we apologize for any confusion that may have arisen from our use of the term "cell motility." We did not use this term to describe exclusively directed cell movement, but rather in a broader sense, to encompass the entirety of membrane remodeling processes involved in migration. In this context, our statement that lysosomal subcellular localization plays a role in cell motility remains valid. The relationship between membrane protrusive activity and motility is evident from our observations in cells overexpressing KIF1A-mCherry, where both membrane remodeling/protrusive activity and movement are significantly impaired compared to control cells (refer to Movie S7 vs. S6 and S10 vs. S9).

To address the Reviewer's concern, we have clarified our definition of motility in the introduction by stating on page 5, lines 1-4: "We demonstrate that PLEKHG3 colocalizes with lysosomes at focal adhesion and protrusion sites, and that the localization and function of this protein, as well as cell motility – which we define as the sum of membrane remodeling processes involved in migration – depend on lysosomal dynamics." This revision ensures that our results are accurately described and minimizes any potential confusion. Additionally, we have removed the statement on page 23, line 1 of the original manuscript. We apologize for any confusion our original wording may have caused and appreciate the opportunity to clarify our intentions.

Reviewer 3

1. • The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.*

Answer: We are grateful for the Reviewer's feedback and concur that gaining insight into the mechanistic details of PLEKHG3's interaction with LAMTOR3 would be beneficial. However, our investigation revealed that PLEKHG3 is a transient interactor/proximal protein of LAMTOR3, and due to the absence of direct binding between LAMTOR3 and PLEKHG3 (Figure 2C on page 11), we are unable to perform a mutational analysis of this interaction, as it lacks a direct read-out.

Furthermore, as demonstrated in Figure S3H-L, LAMTOR3 ablation does not affect PLEKHG3 subcellular localization, suggesting that delving deeper into the molecular consequences of their interaction may be highly complex and beyond the scope of this study. We kindly ask the Reviewer to bear with us on this point, considering the novelty of our findings, which illuminate the interplay between lysosomes and actin dynamics as well as the role of PLEKHG3 in regulating cell protrusions—findings not previously reported in the literature.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Ettelt et al describes the identification of PLEKHG3 as a collaborator of the LAMTOR complex on lysosomes using proximity-based biotinylation. The biotinylation screen is well executed and controlled. The authors choose to follow up on PLEKHG3, a protein involved in actin dynamics, which they refer to as understudied (I let the validity of the latter statement to be evaluated by the editor). Generally speaking, the data are of good quality, and the manuscript is clear and well written. However, much of the evidence on the role of PLEKHG3 on lysosomes is suggestive at best and further investigation into its mechanisms of action is warranted. Some important points to address prior to publication are detailed below.

Major Points:

1. The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.
2. A key issue possibly (but not necessarily) related to the point above is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.
3. Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.

Minor point

1. Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.

Significance

In principle, I consider this study to be of interest to the community of cell biologists working on the endolysosomal system and/or the actin cytoskeleton and its relationship to intracellular membranes. However, the authors find themselves in a rather crowded field. I feel that developing the mechanism of action of PLEKHG3 on lysosomes beyond this first submission could help with boosting the impact of the study. There is clearly something interesting going on, but what that is exactly, remains unclear in my view.

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors use proximity-dependent labelling and mass spectrometry to identify cytoplasmic proteins that interact with lysosomes. They show that PLEKHG3 interacts with the LAMTOR complex; that PLEKH3 accumulates in focal adhesion sites, where it colocalizes with peripheral lysosomes; and that the increased translocation of lysosomes to the periphery leads to less "protrusions", as well as rounder cells and less motile cells.

Major comments: While the study is generally carefully performed and thorough, there are major shortcomings that affect the conclusions taken, namely the specificity of the PLEKHG3 antibody, the identification of "protrusions" and ruffles, several quantifications missing, and the data used to conclude about cell motility. There are also conclusions for which there is no concrete or solid evidence.

Specific issues:

1. Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKH3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein". In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific and is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.
2. In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.
3. Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.
4. At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.
5. It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.
6. Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.

Minor comments:

1. In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains?
2. In the Introduction, there is a period before the reference at the end of the first paragraph.
3. In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.
4. All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.
5. In page 9, where it reads "Figure 1K", should read "Figure S1K".
6. The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.
7. Fig. 2C is not referred in the legend.
8. Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.
9. In page 14, authors refer to Fig. 3G, which does not exist.
10. In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.
11. In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".

Significance

The study provides evidence that lysosome positioning can affect cortical actin cytoskeleton dynamics, as well as cell shape and motility. Experiments are in general thorough and data subjected to quantification. However, there are fundamental conclusions that are preliminary at this stage, as some of the data is not yet solid enough. Therefore, it needs to be further strengthened to be considered for publication. In general, it reads well but the amount of abbreviations (e.g. in the case of the constructs) makes it somehow difficult to follow. The study will be interesting for the cell biology, membrane trafficking and cytoskeleton dynamics communities.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Ettelt et al., describes identification of Rho guanine nucleotide exchange factor- PLEKHG3 as one of the positive hits from a TurboID proximity-dependent labeling screen using LAMTOR3 (one of the subunits of the pentameric LAMTOR complex/Ragulator) as a bait protein. The authors find that PLEKHG3 colocalizes with lysosomes at focal adhesions and that peripheral clustering of lysosomes promotes PLEKHG3 localization near the plasma membrane, and also inhibits protrusion formation and cell motility. The experiments, particularly the Turbo ID proximity-dependent labeling screen, are well-executed, and the imaging data is aptly quantified. The manuscript explores an exciting question of how lysosome positioning regulates cortical actin dynamics and thereby cell motility.

Major comments:

• The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.

Moreover, do the authors observe colocalization between GFP-PLEKHG3 and lysotracker in living cells? There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5. - The authors observe that GFP-PLEKHG3 is concentrated at the cell's periphery when KIF1A is overexpressed, whereas RUFY3 overexpression results in more cytosolic staining. To bolster their conclusion that a change in lysosomal positioning alters the subcellular localization of PLEKHG3, it is preferable to employ inducible techniques, such as the recently described "reversible association with motor proteins" (RAMP) (PMID: 31100061). The method is a rapid and reversible method for altering organelle positioning. It is still unknown whether PLEKHG3 is associated with lysosomes and mechanism of how positioning of lysosomes affects PLEKHG3 localization. - Similarly to the preceding point, the claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central findings of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region. - It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B. - In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated. - Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.

Significance

Using a TurboID proximity-dependent labelling screen, the authors identified an interesting subset of actin-remodeling proteins that interact with the lysosomal protein LAMTOR3. The authors further characterized one of these proteins, PLEKGH3, and found that lysosome positioning regulates PLEKGH3 localization, as well as plasma membrane protrusion formation and cell motility. This study suggests that lysosome peripheral accumulation could regulate cortical actin remodelling and consequently cell migration by regulating PLEKGH3 localization (although this is not tested in the manuscript). This study adds to the previous findings that microtubule-based transport of late endosomes regulate delivery of late endosomal LAMTOR proteins to the vicinity of focal adhesions, which in turn, regulate focal adhesion dynamics. The mechanism of how lysosomes can influence actin remodeling will be important in the context of cancer cell migration. My area of expertise is lysosome fusion and motility and I have limited expertise in regulation of actin dynamics and how Rho family members regulate actin remodeling.

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Reply to the reviewers

Manuscript number: RC-2023-01846

Corresponding author(s): Anastassis Perrakis

1. General Statements

We thank the reviewers for the feedback, highlighting the synergy between computational modeling approaches and the experimental techniques we used to study the interaction between JBP1 and J-DNA. We would like to re-iterate that this approach has led to new findings regarding JBP1 and J-DNA interactions, namely:

• We identified and validated an additional interface in DNA binding domain of JBP1 (JDBD), that contributes to J-DNA binding.
• Through analysis of the AlphaFold model of JBP1, we propose how the Thymidine Hydroxylase domain (THD) of JBP1 binds J-DNA, and how the JDBD and THD domains are connected flexibly but explicitly to each other.
• The AlphaFold model allowed to hypothesize that the N-terminus of JBP1 is contributing to J-DNA binding, which we confirmed experimentally. These findings collectively suggest a mechanistic and structural basis on the synergy between the JDBD, the THD and the N-terminus of JBP1, providing a possible explanation to the previously observed conformational changes of JBP1 upon J-DNA binding. Our findings on the conservation of the N-terminus region and the new interface of JDBD, could be offering an explanation on the differences on how essential base-J is for different Trypanosomidaespecies. They also offer a first glimpse of how these domains synergize to provide new insights in the semi-conservative replication mechanisms of the base-J epigenetic marker in kinetoplastids.

2. Point-by-point description of the revisions

Reviewer #1____: ____Evidence, reproducibility and clarity

Summary:

The paper presents a combined experimental (X-ray, SAXS, mutational analysis) and computational (MD, docking, AlphaFold) work that elucidates the mechanism of JDBD:JDNA complex formation.

Major comment:

• How did the authors decide the timescale of the production run? Wouldn't the loop motion (which can be necessary for this study) occur on a timescale of 300+ ns?

While our simulations showed overall stability of the simulated protein (as reflected by the RMSD time series), the RMSF provided clear indications for differences in flexibility in the loops and termini of JBP1. We believe that performing an MD simulation of 100 ns in duplo samples the flexibility and behavior of the JBP1 DNA binding domain (JDBD) sufficiently for obtaining templates for docking studies, which was the purpose of running the simulations. We emphasized this in the manuscript (page 10) by adding: “and obtain additional templates for further docking studies”.

Minor comments:

• Did I understand correctly that the LINCS algorithm constrained only hydrogen-involving bonds? It is not mentioned explicitly. Or am I missing something?

LINCS was indeed used to only constrain hydrogen-involving bonds. We made this more explicit in the MD protocol described in the method section of the manuscript: “The LINCS algorithm (40) was used to constrain hydrogen-involving bond lengths to their zero-energy value”.

• The authors should increase the resolution of figures S1 and S3. They look a bit blurry.

We apologize for that; we tried to improve that by adjusting the figure sizes, but we are constrained by the output from e.g., the Bitclust software. We sincerely hope that the current resolution does not present an obstacle to the reader.

Significance:

The J DNA base is critical for transcription termination at the ends of the polycistronic gene clusters in Leishmania and related species. Hence, understanding the formation mechanism of the JDBD:J-DNA complex can provide an opportunity to develop novel chemotherapeutic treatments against these diseases. This work provides the first crystal structure of JDBD with the disordered loop and suggests that R448 and N455, as well as the N-terminus, are involved in the J-DNA binding process. The article is well-written and can interest readers from biological and biochemical societies. However, my field of expertise is computational chemistry and biochemistry; therefore, I cannot adequately evaluate the accuracy of the experimental techniques used in this work.

We thank the reviewer, but would like to emphasize that our work goes well beyond the new interface of the JDBD, offering significant new insights on the synergy between the THD, the JDBD and the newly identified N-terminus binding to J-DNA, as also outlined in the general summary above.

__Reviewer #2_:_ Evidence, reproducibility and clarity __

The manuscript by de Vries et al. reported the crystal structure of the J-DNA binding domain of JBP1. Although, the structure was already solved, the new structure allows to observe a loop that was disordered in the previous structure. This structure was next used to propose models of DNA complex analyzed by MD. The proposed model was then validated by mutagenesis.

Overall, the findings are interesting and the technical quality of the work is high.

We believe, as we outlined in the summary, that our work goes well beyond showing the new structure and validate the new interface by mutagenesis. In our view, the major findings of the paper have to do with the AlphaFold modeling analysis and validation, and the finding that the N-terminus of JBP1 is involved in DNA binding, something that is not only new, but has also been totally unexpected.

Comments:

-For clarity, a figure showing the domain organization of JBP1 could help the reader in the introduction part.

The domain architecture of JBP1 was added to Figure 1 as panel B.

-In addition to Figure 2 showing the newly observed loop in 2Fo-Fc map, an omit map should be included in Supp data.

A figure of the omit map was added to the supplemental information as Supplemental Figure S1.

-Figure S6 legend should be more precise about the type of HDX MS analysis.

As the HDX-MS data and methods were described in detail in previous work (Heidebrecht et al. 2011), we left the details out in the current manuscript. The reference to this paper was added to Figure S6 for clarity.

-The authors performed MD simulations. But what about DNA curvature upon complex formation?

For the JDBD MD simulations, we did not add at all the (J-)DNA and the current simulations provide no information about its curvature. As mentioned in the discussion, we do expect conformational changes when the J-DNA:JBP1 complex forms, and this likely includes DNA curvature as well as conformational changes between the protein domains. We felt that the current data would not allow to extract new insights from such complicated simulations.

-p.12 Some mutants were characterized, notably their melting temperatures. One mutant shows decreased stability while R448A shows increased stability. What is the structural explanation?

Indeed, the E437A mutant (that showed lower expression compared to the other mutants) showed decreased thermal stability. The R448A shows an increase in stability (~3o C), and so does the H440 mutant (~2o C). While there is no specific structural explanation for these observations, in general mutation to alanine reduces the entropy-loss upon protein folding. The reason we comment about the stability is to point out that the dramatically decreased binding of the N455A and R448A mutants is not due to a decrease of the protein stability. This is now clarified in the manuscript: “the other mutants are as stable or slightly more stable compared to the wild-type, suggesting that the DNA-binding analysis is not affected significantly by altered protein stability.”

-Figure 6E: The chi2 value for the comparison of the experimental curve for THD domain and calculated curve is very high indicating a poor fit. What is the explanation?

The χ2 value indeed reflects differences between the JBP1 THD selected from the AlphaFold model and the structure used in the SAXS experiment. The experimental model is the so-called ΔDBD, which is the full length JBP1, where the JDBD is missing (it has been “spliced out”). Hence, the connecting loops and the N-terminus are present in this ΔDBD structure, whereas in the THD of the AlphaFold model, these parts of the structure were left out. In other words, while the full-length computational model refers to the exact same purified protein, the computationally truncated model and the purified protein for the experiments, have actual differences. Thus, the shape and fit of the experimental curve to the calculated curve can be considered pretty good. This is now clarified in the manuscript by adding: “The χ2 value of the fit is slightly elevated due to presence of the connecting loops between the THD and the JDBD and the N-terminus in the protein used for measuring the SAXS curve, which were removed from the computational model.”.

Significance:

The novelty of the manuscript mainly relies on the description of the crystal structure of JDBD protein without DNA and proposed models of DNA complex within full length protein, models that were validated by mutations or truncations. The current manuscript well suited for a specialized journal.

These findings are indeed novel, especially the discovery and validation of the new interface of JDBD to J-DNA. We want to iterate that we are most excited by the totally unexpected and mechanistically important discovery of the role of the N-terminus of JBP1, that brings together legacy data and raises interest for additional structural studies.

__Reviewer #3_: _Evidence, reproducibility and clarity __

Base J, also known as β-D-glucopyranosyloxymethyluracil, is a modified form of thymidine that has been identified in kinetoplastids and related organisms. It is worth noting that the distribution of Base J in the genome may vary depending on the organism and its life stage and influences its genome dynamics. The synthesis of this hypermodified nucleotide occurs in two steps, which involve the participation of two distinct thymidine hydroxylases, namely J-binding protein 1 and 2 (JBP1 and JBP2), along with a β-glucosyl transferase. In this study, the authors have presented a crystal structure of JBP1 J-DNA binding domain (J-DBD), which includes a previously reported disordered loop that might be involved in JBP1:J-DNA contact. Using this disordered structure as a starting point, the authors conducted Molecular Dynamics simulations and computational docking studies to propose models for the recognition of J-DNA by JBP1 J-DBD. The results from these studies were validated by punctual mutagenesis experiments, which provided additional data for docking and revealed a binding pattern for JBP1 J-DBD on J-DNA. By combining the crystallographic structure of the TET2 JBP1-homologue in complex with DNA and the AlphaFold model of full-length JBP1, the authors have hypothesized that the flexible N-terminus of JBP1 contributes to DNA-binding, which they have confirmed experimentally. However, according to the authors, to gain a deeper understanding of the unique molecular mechanism that underlies the replication of epigenetic information, an experimental determination of a high-resolution JBP1:J-DNA complex involving conformational changes would be necessary. Nevertheless, the present proposed objectives were fully contemplated by the authors.

Major comments:

In my opinion, the present article effectively achieved all the described objectives using appropriate and reproducible methodology, including protein expression and crystallization analysis, Molecular Dynamics analysis using GROMACS-2020.2 software, docking analysis, punctual mutations analyses, and modeling of JBP1:J-DNA complex using the AlphaFold tool. The authors presented the results in a logical and organized manner, making it easy for readers to extract the most important points. However, I believe that the section titled "Results and Discussion" contains more "results" than "discussion". While I understand that the literature on JBPs and base J is still in its early stages, other species of kinetoplastids have JBP1, in which mutations were not lethal as in L. tarentolae (e.g. T. brucei). Therefore, providing information about the structure of JBP1 and how the present results relate to what is known about JBP1 in other species in terms of structure and J-DNA interactions would significantly enrich the discussion of the findings and reinforce their significance and impact. Thus, the authors should have been clearer about the impact of their findings. When discussing the results, the authors should have answered questions such as how the identification of the new residues involved in JBP1 J-DNA binding impacts the current model of JBP1:J-DNA interactions, how this improved model contributes to the understanding of base J synthesis, and if the new model can be extrapolated to other species of kinetoplastids, according to the conservation of JBP1 among them.

Although the article is more focused on protein research rather than parasite general molecular biology and medical studies, the findings may have implications for the development of new treatments for leishmaniases. Therefore, the authors should have discussed the potential of their new improved model as a target for lacking treatments of leishmaniases or at least brought up the point at conclusion section.

We thank the reviewer for pointing out that the comparison between kinetoplastid species could be described more explicit to highlight the impact of the presented results with respect to the variety in JBP1 sequence, and possibly contribute to understanding the role of base-J in the differences in lethality and transcription regulation within these species. We now elaborate on our results in multiple places in the manuscript:

• In the introduction we introduce the differences in lethality and transcription regulation within Leishmania and Trypanosoma (see also minor comment 2 below).
• An alignment of full-length JBP1 sequences of different Trypanosomatidae species was added as Supplemental Figure S10 to support the discussion below.
• The section describing the docking model of JDBD:J-DNA has been ammended with a description regarding the conservation of the residues involved in the binding interface: “The residues described in the JDBD:J-DNA interface are in general highly conserved (Supplemental Figure S12). Asp525 is fully conserved in Leishmania, Trypanosoma, Leptomonas and Bodo saltans species, so are Lys522, Arg532 and ArgR448. Asn455, which we identify in this study, is not conserved in Leptomonas, and Arg517 is not conserved in Trypanosoma also.”

• We renamed the final section to “Conclusions and Outlook” and added some discussion focusing on the conservation of the residues in the N-terminus and in the JDBD between different Trypanosomatidae Specifically, we now discuss how these could contribute in understanding the differences in lethality and transcription termination between Leishmania and Trypanosoma in the absence of base-J.

  Minor Comments:

• Please, re-check the affirmation "99% of base-J is found in telomeric repeats, mainly in GGGTTA repeats wherein the second thymine is modified to base-J (2-4)" in the Introduction. I believe that the distribution of base-J varies among different species of trypanosomatids and, therefore, cannot be generalized. Moreover, among different life stages in some organisms such as T. brucei and Leishmania major, differences on base-J distribution are found. The 99% of telomeric base-J mentioned would be a feature of Leishmania genus. Please, re-check the references 3 and 4.

Indeed, the referee is right to mention that the 99% is a Leishmania-specific observation. We have modified the introduction accordingly. “Base-J is found mainly in telomeric repeats and other repetitive sequences. In Leishmania 99% of base-J is found in telomers, mainly in GGGTTA repeats, wherein the second thymine is modified to base-J (2–4).”

Please, enrich the introduction topic with information about the model species, such as importance as pathological agent, its genomic organisation (core, subtelomeres, telomeres, what is present in subtelomeres, including base j) and polycistronic transcription and base J relevance on this aspect. That way, the reader will have a broad and more complete overview of the relevance of the present study.

We have enriched the introduction with a paragraph (“Leishmania species are uni-cellular […] essentiality of base-J for the life circle of these parasites.”) outlining the issues raised by the referee. As suggested by the referee, this makes it easier to both understand the relevance of the present study and to enrich the discussion about our findings discussed earlier in this letter.

Please, inform the expression vector for Leishmania tarentolae JBP1 used to express the mentioned protein on BL21(DE3)T1R.

The expression vector for JDBD JBP1 used for the crystallization was mentioned in Heidebrecht et al. 2011, which we refer to in the text. For clarity we added the vector to the first sentence in the protein expression and purification section in the material and methods: “using the pETNKI-his-3C-JBP1-JDBD plasmid”.

Please, supply the picture of the gel containing the extracted protein.

The gel of the JDBD mutants and the JBP1 N-terminus truncations was added to the supplemental information as Figure S10.

Significance:

Overall, this study provides important insights into the JBP1 and DNA interactions, which were lacking in the literature. The use of techniques such as protein expression and crystallization analysis, molecular dynamics, and docking analysis is in line with the research objectives. However, the lack of some information about methodology needs to be addressed (minor comments 3 and 4). Personally, methodology such as molecular dynamics and docking analysis is not easy to critique but the results are clear and understandable.

Although the authors should have been clearer about the impact of their findings, as addressed on my major comments, I believe that protein focused molecular parasitologists would benefit from the finds and methodology presented on this manuscript, since the article is more focused on protein research rather than parasite general molecular biology and medical studies, as mentioned on my major comments.

In summary, this study provides new insights into JBP1 and DNA interactions and uses appropriate and reproducible techniques to achieve its objectives. However, the authors should provide more clarity on the impact of their findings and discuss the potential of their new improved model.

My area of expertise: Cell and molecular biology; stem cells and factor controlling their fate; DNA, RNA, and molecular biology related techniques; Trypanosomatids telomere and telomerase

We would like to thank the referee for his positive and constructive outlook, which we believe resulted in changes that put the impact of our findings in clearer perspective.

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 #3

Evidence, reproducibility and clarity

Base J, also known as β-D-glucopyranosyloxymethyluracil, is a modified form of thymidine that has been identified in kinetoplastids and related organisms. It is worth noting that the distribution of Base J in the genome may vary depending on the organism and its life stage and influences its genome dynamics. The synthesis of this hypermodified nucleotide occurs in two steps, which involve the participation of two distinct thymidine hydroxylases, namely J-binding protein 1 and 2 (JBP1 and JBP2), along with a β-glucosyl transferase. In this study, the authors have presented a crystal structure of JBP1 J-DNA binding domain (J-DBD), which includes a previously reported disordered loop that might be involved in JBP1:J-DNA contact. Using this disordered structure as a starting point, the authors conducted Molecular Dynamics simulations and computational docking studies to propose models for the recognition of J-DNA by JBP1 J-DBD. The results from these studies were validated by punctual mutagenesis experiments, which provided additional data for docking and revealed a binding pattern for JBP1 J-DBD on J-DNA. By combining the crystallographic structure of the TET2 JBP1-homologue in complex with DNA and the AlphaFold model of full-length JBP1, the authors have hypothesized that the flexible N-terminus of JBP1 contributes to DNA-binding, which they have confirmed experimentally. However, according to the authors, to gain a deeper understanding of the unique molecular mechanism that underlies the replication of epigenetic information, an experimental determination of a high-resolution JBP1:J-DNA complex involving conformational changes would be necessary. Nevertheless, the present proposed objectives were fully contemplated by the authors.

Major comments:

In my opinion, the present article effectively achieved all the described objectives using appropriate and reproducible methodology, including protein expression and crystallization analysis, Molecular Dynamics analysis using GROMACS-2020.2 software, docking analysis, punctual mutations analyses, and modeling of JBP1:J-DNA complex using the AlphaFold tool. The authors presented the results in a logical and organized manner, making it easy for readers to extract the most important points. However, I believe that the section titled "Results and Discussion" contains more "results" than "discussion". While I understand that the literature on JBPs and base J is still in its early stages, other species of kinetoplastids have JBP1, in which mutations were not lethal as in L. tarentolae (e.g. T. brucei). Therefore, providing information about the structure of JBP1 and how the present results relate to what is known about JBP1 in other species in terms of structure and J-DNA interactions would significantly enrich the discussion of the findings and reinforce their significance and impact. Thus, the authors should have been clearer about the impact of their findings. When discussing the results, the authors should have answered questions such as how the identification of the new residues involved in JBP1 J-DNA binding impacts the current model of JBP1:J-DNA interactions, how this improved model contributes to the understanding of base J synthesis, and if the new model can be extrapolated to other species of kinetoplastids, according to the conservation of JBP1 among them. Although the article is more focused on protein research rather than parasite general molecular biology and medical studies, the findings may have implications for the development of new treatments for leishmaniases. Therefore, the authors should have discussed the potential of their new improved model as a target for lacking treatments of leishmaniases or at least brought up the point at conclusion section.

Minor Comments:

I have some minor comments regarding the text:

1. Please, re-check the affirmation "99% of base-J is found in telomeric repeats, mainly in GGGTTA repeats wherein the second thymine is modified to base-J (2-4)" in the Introduction. I believe that the distribution of base-J varies among different species of trypanosomatids and, therefore, cannot be generalized. Moreover, among different life stages in some organisms such as T. brucei and Leishmania major, differences on base-J distribution are found. The 99% of telomeric base-J mentioned would be a feature of Leishmania genus. Please, re-check the references 3 and 4.
2. Please, enrich the introduction topic with information about the model species, such as importance as pathological agent, its genomic organisation (core, subtelomeres, telomeres, what is present in subtelomeres, including base j) and polycistronic transcription and base J relevance on this aspect. That way, the reader will have a broad and more complete overview of the relevance of the present study.
3. Please, inform the expression vector for Leishmania tarentolae JBP1 used to express the mentioned protein on BL21(DE3)T1R.
4. Please, supply the picture of the gel containing the extracted protein.

Significance

Overall, this study provides important insights into the JBP1 and DNA interactions, which were lacking in the literature. The use of techniques such as protein expression and crystallization analysis, molecular dynamics, and docking analysis is in line with the research objectives. However, the lack of some information about methodology needs to be addressed (minor comments 3 and 4). Personally, methodology such as molecular dynamics and docking analysis is not easy to critique but the results are clear and understandable.

Although the authors should have been clearer about the impact of their findings, as addressed on my major comments, I believe that protein focused molecular parasitologists would benefit from the finds and methodology presented on this manuscript, since the article is more focused on protein research rather than parasite general molecular biology and medical studies, as mentioned on my major comments.

In summary, this study provides new insights into JBP1 and DNA interactions and uses appropriate and reproducible techniques to achieve its objectives. However, the authors should provide more clarity on the impact of their findings and discuss the potential of their new improved model.

My area of expertise: Cell and molecular biology; stem cells and factor controlling their fate; DNA, RNA, and molecular biology related techniques; Trypanosomatids telomere and telomerase

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 manuscript by de Vries et al. reported the crystal structure of the J-DNA binding domain of JBP1. Although, the structure was already solved, the new structure allows to observe a loop that was disordered in the previous structure. This structure was next used to propose models of DNA complex analyzed by MD. The proposed model was then validated by mutagenesis.

Overall, the findings are interesting and the technical quality of the work is high.

Comments:

• For clarity, a figure showing the domain organization of JBP1 could help the reader in the introduction part.
• In addition to Figure 2 showing the newly observed loop in 2Fo-Fc map, an omit map should be included in Supp data.
• Figure S6 legend should be more precise about the type of HDX MS analysis.
• The authors performed MD simulations. But what about DNA curvature upon complex formation?
• p.12 Some mutants were characterized, notably their melting temperatures. One mutant shows decreased stability while R448A shows increased stability. What is the structural explanation?
• Figure 6E: The chi2 value for the comparison of the experimental curve for THD domain and calculated curve is very high indicating a poor fit. What is the explanation?

Significance

The novelty of the manuscript mainly relies on the description of the crystal structure of JDBD protein without DNA and proposed models of DNA complex within full length protein, models that were validated by mutations or truncations. The current manuscript well suited for a specialized journal.

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

Summary:

The paper presents a combined experimental (X-ray, SAXS, mutational analysis) and computational (MD, docking, AlphaFold) work that elucidates the mechanism of JDBD:JDNA complex formation.

Major comment:

• How did the authors decide the timescale of the production run? Wouldn't the loop motion (which can be necessary for this study) occur on a timescale of 300+ ns?

Minor comments:

• Did I understand correctly that the LINCS algorithm constrained only hydrogen-involving bonds? It is not mentioned explicitly. Or am I missing something?
• The authors should increase the resolution of figures S1 and S3. They look a bit blurry.

Significance

The J DNA base is critical for transcription termination at the ends of the polycistronic gene clusters in Leishmania and related species. Hence, understanding the formation mechanism of the JDBD:J-DNA complex can provide an opportunity to develop novel chemotherapeutic treatments against these diseases. This work provides the first crystal structure of JDBD with the disordered loop and suggests that R448 and N455, as well as the N-terminus, are involved in the J-DNA binding process. The article is well-written and can interest readers from biological and biochemical societies.

However, my field of expertise is computational chemistry and biochemistry; therefore, I cannot adequately evaluate the accuracy of the experimental techniques used in this work.

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

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Reply to the reviewers

We thank the reviewers for their comments and constructive suggestions to improve the manuscript. We are encouraged to see that both reviewers acknowledge how the results from our manuscript uses state-of-art technologies to advance molecular underpinnings of centriole length, integrity and function regulation. Both reviewers also highlighted that the manuscript is well laid out and presents clear, rigorous, and convincing data. Reviewer#1 described our manuscript of highest experimental quality and broad interest to the field of centrosome and cell biology form a basic research and genetics/clinical point of view. Here, we explain the revisions, additional experimentations and analyses planned to address the points raised by the referees. We will perform most of the experimentations and corrections requested by the reviewers. We have already made several revisions and are currently working on additional experiments.

Our responses to each reviewer comment in bold are listed below. References mentioned here are listed in the references section included at the of this document.

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

Summary: __In this manuscript, Arslanhan and colleagues use proximity proteomics to identify CCDC15 as a new centriolar protein that co-localizes and interacts with known inner scaffold proteins in cell culture-based systems. Functional characterization using state-of-the-art expansion microscopy techniques reveals defects in centriole length and integrity. The authors further reveal intriguing aberrations in the recruitment of other centriole inner scaffold proteins, such as POC1B and the SFI1/centrin complex, in CCDC15-deficient cells, and observe defects in primary cilia. __

We thank the reviewer for the accurate summary of the major conclusions of our manuscript.

Major points:

1) The authors present a high-quality manuscript that identifies a novel centriolar protein by elegantly revealing and comparing the proximity proteomes of two known centriolar proteins, which represents an important component for the maintenance of centrioles.

We thank the reviewer for highlighting that our manuscript is of high quality and presents important advances for the field.

__2) Data are often presented from two independent experiments (n = 2), which is nice, but also the minimum for experiments in biology. It is strongly recommended to perform at least three independent experiments. __

We agree with the reviewer that analysis of data form three experimental replicates is ideal for statistical analysis. We performed three replicates for the majority of experiments in the manuscript. However, as the reviewer pointed out, we included analysis from two experiments for the following figures:

• Fig. 4H: quantification of CCDC15 total cellular levels throughout the cell cycle by western blotting
• Fig. 5A: CCDC15-positive centrioles in control and CCDC15 siRNA-transfected cells
• Fig. 6B: % centriolar coverage of POC5, FAM161A, POC1B and Centrin-2 in control and CCDC15 siRNA-transfected cells
• Fig. 6C, 6E: Centrin-2 or SFI1-positive centrioles in control and CCDC15 siRNA-transfected cells
• Fig. 6J, K: normalized tubulin length and percentage of defective centrioles in cells depleted for CCDC15 or co-depleted for CCDC15 and POC1B
• Fig. 7F, H: SMO-positive cilia and basal body IFT88 levels in control and CCDC15 siRNA-transfected cells
• Fig. S3H: centriole amplification in HU-treated control and CCDC15 siRNA-transfected cells (no)
• Fig. S3A: centrosomal levels upon CCDC15 depletion There are two reasons for why we performed two experimental replicates for these experiments: 1) results from the two experimental replicates were similar, 2) quantification of data by U-ExM is laborious. To address the reviewer’s comments, we will perform the third experimental replicate for the sets of data that led to major conclusions of our manuscript, which are Figures 4H, 6C, 6E, 6J, 6K, 7F, 7H and S3A.

3) The protein interaction studies presented in Fig. 3 could be of higher quality. While it is great that the authors compared interactions to the centriolar protein SAS6, which is not expected to interact with CCDC15, the presented data raise many questions.

__a) In most cases, co-expression of tagged CCDC15 stabilizes the tested interaction partners, such that the overall abundance seems to be higher. The increase in protein abundance is substantial for Flag-FAM161A (Fig. 3D) and GFP-Centrin-2 (Fig. 3E) and is even higher for the non-interactor SAS6 (Fig. 3G), while it cannot be assessed for GFP-POC1B (Fig. 3F). Hence, the higher expression levels under these conditions make it more likely that these proteins are "pulled down" and therefore do not represent appropriate controls. __

We agree with the reviewer that the differences in protein abundance of the prey proteins upon expression of CCDC15 relative to control might impact the interpretation of the interaction data. To address this concern, we will perform the following experiments:

• To account of the potential stabilizing effects of CCDC15 expression, we will change the relative ratio of plasmids expressing proteins of interest and assess the expression of bait and prey protein levels. We will then repeat the co-immunoprecipitation experiments in conditions where prey expression levels are similar.
• To avoid the potential stabilizing effects of CCDC15 overexpression, we will perform immunoprecipitation experiments in cells expressing GFP or V5-tagged inner scaffold proteins and assess their potential physical or proximity interaction by blotting for endogenous CCDC15. __b) All Co-IP experiments are lacking negative controls in the form of proteins that are not pulled down under the presented conditions. __

For the co-IP experiments, we only included a specificity control for the interaction of the bait protein with the tag of the prey protein (i.e. GBP pulldown of GFP or GFP-CCDC15-expressing cells). As the reviewer suggested, we will also include a specificity control for the interaction of bait with the tag of the prey protein for co-immunoprecipitation experiments (i.e. GFP pulldown of cells expressing GFP-CCDC15 with V5-BirA* or V5-BirA*-FAM161A).

__c) The amounts of co-precipitation of the tested proteins appears very different. Could this reflect strong or weak interactors, or does it reflect the abundance of the respective proteins in centrioles? __

We agree with the reviewer that the quantity of the co-precipitated prey proteins might be a proxy for the interaction strength if the abundance of the bait proteins is similar. However, the expression levels of bait and prey proteins in co-transfected cells are different and thus, cannot be used to derive a conclusion on the interaction strength. For the revised manuscript, we will repeat the IP experiments and comment on this in the discussion section.

__4) The observation that IFT88 is supposedly decreased at the base of cilia in CCDC15-depleted cells requires additional experiments/evidence. Fig. 7G shows the results of n = 2 and more importantly, a similar reduction of gamma-tubulin in siCCDC15. Could the observed reduction in IFT88 be explained by a decrease in accessibility to immunofluorescence microscopy? Would the reduction in IFT88 at the base also be apparent when the signals were normalized to gamma-tubulin signals? __

To address the reviewer’s concern, we quantified the basal body gamma-tubulin and IFT88 levels in control and CCDC15-depleted cells and plotted the basal body IFT88 levels normalized to gamma-tubulin levels in Fig. 7H. Similar to the reduction in IFT88 levels, gamma-tubulin-normalized IFT88 levels was significantly less relative to control cells. Moreover, the gamma-tubulin basal body levels were similar between control and CCDC15 cells. We revised the gamma-tubulin micrographs in Fig. 7G to represent this. These results indicate that the reduction in basal body IFT88 levels upon CCDC15 depletion in specific.

__5) The observed Hedgehog signaling defects are described as follows: "CCDC15 depletion significantly decreased the percentage of SMO-positive cells". It is similarly described in the figure legend. If this was true, the simplest explanation would be that it reflects the reduction in ciliation rate (which is in a similar range). If SMO-positive cilia (instead of "cells") were determined, the text needs to be changed accordingly. __

As the reviewer pointed out, we quantified SMO-positive cilia, but not cells. We are sorry for this typo. We corrected SMO-positive cells as SMO-positive cilia in the manuscript text, Fig. 7 and figure legends.

__6) OPTIONAL: While expansion microscopy is slowly becoming one of the standard super-resolution microscopy methods, which is particularly well validated for studying centrioles, the authors should consider confirming part of their findings (as a proof of principle, surely not in all instances) by more established techniques. This could serve to convince critical reviewers that may argue that the expansion process may induce architectural defects of destabilized centrioles, as observed after disruptions of components, such as in Fig. 6. Alternatively, the authors could cite additional work that make strong cases about the suitability of expansion microscopy for their studies, ideally with comparisons to other methods. __

• SIM imaging was previously successfully applied for nanoscale mapping of other centriole proteins including CEP44, MDM1 and PPP1R35 (Atorino et al., 2020; Sydor et al., 2018; Van de Mark et al., 2015). To complement the U-ExM analysis, we have started imaging cells stained for CCDC15 and different centriole markers (i.e. distal appendage, proximal linker, centriole wall) using a recently purchased 3D-SIM superresolution microscope. We already included the SIM imaging data for CCDC15 localization in centrosome fractions purified from HEK293T cells in Fig. S5B. In the revised manuscript, we will replace confocal imaging data in Fig. 3A and 3B with SIM imaging data.
• As the reviewer noted, expansion microscopy has been successfully used for the analysis of a wide range of cellular structures and scientific questions including nanoscale mapping of cellular structures across different organisms. In particular, U-ExM of previously characterized centrosome proteins various centriole proteins have significantly advanced our understanding of centriole ultrastructure. In our manuscript, we used the U-ExM protocol that was validated for centrioles by comparative analysis of U-ExM and cryo-ET imaging by our co-authors (Gambarotto et al., 2019; Hamel et al., 2017). To clarify these points, we included the following sentence along with the relevant references in the introduction: “Application of the U-ExM method to investigate known centrosome proteins has started to define the composition of the inner scaffold as well as other centriolar sub-compartments (Chen et al., 2015; Gambarotto et al., 2021; Gambarotto et al., 2019; Kong and Loncarek, 2021; Laporte et al., 2022; Mahen, 2022; Mercey et al., 2022; Odabasi et al., 2023; Sahabandu et al., 2019; Schweizer et al., 2021; Steib et al., 2022; Tiryaki et al., 2022; Tsekitsidou et al., 2023).”

Minor points:

1) Text, figures, and referencing are clear and accurate, apart from minor exceptions.

We clarified and corrected the points regarding text, figures and references as suggested by the two reviewers.

__ 2) The title suggests a regulator role for CCDC15 in centriole integrity and ciliogenesis, which has formally not been shown. __

We revised the title as “CCDC15 localizes to the centriole inner scaffold and functions in centriole length control and integrity”.

__3) As the authors observe changes in centriole lengths in the absence of CCDC15, it would be very insightful to compare these phenotypes to other components that affect centriolar length, such as C2CD3, human Augmin complex components (as HAUS6 is identified in Fig. 1) or others. These could be interesting aspects for discussion, additional experiments are OPTIONAL. __

We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section and also included discussion of this data in the discussion section:

“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”

__ 4) While the reduced ciliation rate in the absence of CCDC15 is convincing, the authors did not investigate "ciliogenesis", i.e. the formation of cilia, and hence should re-phrase. The sentence in the discussion that "CCDC15 functions during assembly" should be removed. __

To clarify that we only investigated the role of CCDC15 in the ability of cells to form cilia, we replaced sentences that indicates “CCDC15 functions in cilium assembly” with “CCDC15 is required for the efficiency of cilia formation”.

__5) The existence of stably associated CCDC15 pools with centrosomes (Fig. 2) requires further evidence. The recovery of fluorescence after photobleaching in FRAP experiments is strongly dependent on experimental setups and is only semi-quantitative. A full recovery is unrealistic, hence, it is ideally compared to a known static or known mobile component. I personally think this experiment -as it is presented now- is of little value to the overall fantastic study. The authors may consider omitting this piece of data. __

We agree with the reviewer that FRAP data by itself does not prove the existence of stably associated CCDC15 pool. As controls in these experiments, we use FRAP analysis of GFP-CCDC66, which has a 100% immobile pool at the cilia and 50% immobile pool at the centrosomes as assessed by FRAP (Conkar et al., 2019). To address these points, we toned down the conclusions derived from this experiment by revising the sentence as follows:

Additionally, we note that the following data provides support for the stable association of CCDC15 at the centrioles:

• About 49.6% (± 3.96) of the centrioles still had CCDC15 fluorescence signal at one of the centrioles upon CCDC15 siRNA treatment (Fig. 5A, 5B). The inefficient depletion of the mature centriole pool of CCDC15 is analogous to what was observed upon depletion of other centriole lumen and inner scaffold proteins including WDR90 and HAUS6 (Schweizer et al., 2021; Steib et al., 2020). __6) The data that CCDC15 is a cell cycle-regulated protein is not very convincing (see Fig. 3H), as the signals area weak and the experiment has been performed only once (n= 1). This piece of data does not appear to be very critical for the main conclusions of the manuscript and may be omitted. Otherwise, this experiment should be repeated to allow for proper statistical analysis. __

We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.

__7) Experimental details on how "defective centrioles" are determined are missing. __

We included the following experimental details to the methods section:

“Centrioles were considered as defective when the roundness of the centriole was lost or the microtubule walls were broken or incomplete. In the longitudinal views of centrioles, defective centrioles were visualized as heterogenous acetylated signal along the centriole wall or irregularities in the cylindrical organization of the centriole wall (Fig. 5F). We clarified these points in the methods section.

__ 8) For figures, in which the focus should be on growing centrioles (see Fig. 4), it could be helpful to guide the reader and indicate the respective areas of the micrographs by arrows. __

We added arrows to point to the respective areas of the micrographs in Fig. 4F.

__ 9) Page18: "centriole length shortening" could be changed to "centriole shortening". __

We corrected this description as suggested.

__10) It is unclear how the authors determine distal from proximal ends of centrioles in presented micrographs (see Fig. 5D). __

We determined the proximal and distal ends of the centrioles by taking the centriole pairs as a proxy. Even though we only represent a micrograph containing a single centriole in some of the U-ExM figures including Fig. 5D, the uncropped micrographs contain two centrioles, which are oriented orthogonally and tethered to each other at their proximal ends in interphase cells. We added the following sentence to the methods section to clarify this point:

*“Since centrioles are oriented orthogonally and tethered to each other at their proximal ends in interphase cells, we also used the orientation of the centriole pairs as a proxy to determine the proximal and distal ends of the centrioles.” *

__11) Fig. 7A is missing scale bars and Fig.7 overall is lacking rectangle indicators of the areas that are shown at higher magnification in the insets. __

We added scale bar to Fig. 7A and rectangle indicators for zoomed in regions in Fig. A, E, G.

12) Fig. 7C displays cilia that appear very short, especially when comparing to the micrographs and bar graphs presented. The authors may want to explain this discrepancy.

We thank the reviewer for the comment. The zoomed in representative cilia is 4.1 µM in control cells and 1.4 µM in CCDC15-depleted cells. Therefore, the representative cilia is in agreement with the quantification of cilia in Fig. 7C.

Reviewer #1 (Significance (Required)): • From a technical point of view the authors use two state-of-the-art technologies, namely proximity labeling combined with proteomics and ultrastructure expansion microscopy, that are both challenging and very well suited to address the main questions of this study. ____ • General assessment: The presented study is of highest experimental quality. Despite being very challenging, the expansion microscopy and proximity proteomics experiments have been designed and performed very well to allow solid interpretation. The results of the central data are consistent and allow strong first conclusions about the putative function of the newly identified centriolar protein CCDC15. The study presents a solid foundation for future hypothesis-driven, mechanistic analysis of CCDC15 and inner scaffold proteins in centriole length control and maintaining centriole integrity. The only limitation of the study is that the technically simpler experiments should be repeated to allow proper statistical assessment, which can be addressed easily. • Advance: This is the first study that identifies CCDC15 as a centriolar protein and localizes it to the inner scaffold. It further describes a function for CCDC15 in centriole length control and shows its importance in maintaining centriole integrity with consequences for stable cilia formation in tissue culture. The study provides further functional insights into the interdependence of inner scaffold proteins and the role of CCDC15 in the recruitment of the SFI1/centrin distal complex. • Audience: The manuscript will be of broad interest to the fields of centrosome and cell biology, both from a basic research and genetics/clinical point of view due to the association with human disorders. The state-of-the-art technologies applied will be of interest to a broader cell and molecular biology readership that studies subcellular compartments and microtubules. • Reviewer's field of expertise: Genetics, imaging, and protein-protein interaction studies with a focus on centrosomes and cilia.

We thank the reviewer for recognizing the importance of our work and for supportive and insightful comments that will further strengthen the conclusions of our manuscript. Our planned revisions will address the only major technical limitation raised by the reviewer that requires adding one more experimental replicate for analysis of the data detailed in major point#1. Notably, we also thank the reviewer to specifying the experiments that are not essential or will be out of the scope of our manuscript as “optional”.

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

Summary:

__In this study, Arslanhan et al. propose CCDC15 as a novel component of the centriole inner scaffold structure with potential roles in centriole length control, stability and the primary cilium formation in cultured epithelial cells. Using proximity labelling they explore the common interactors of Poc5 and Centrin-2, two resident molecules of the centriole inner scaffold, to hunt for novel regulators of this structure. The authors leverage expansion microscopy-based localization and siRNA-dependent loss-of-function experiments to follow up on one such protein they identify, CCDC15, with the aforementioned roles in centriole and cilia biology.

This study is designed and laid out nicely; however, to be able to support some of the important claims regarding their proximity labelling results and exploration on the roles of CCDC15, there are several major technical and reproducibility concerns that deem major revision. Similarly, the introduction (perhaps inadvertently) omits much of the recent studies on centriole size control that have highlighted the complexity of this biological problem. As such, addressing the following major points will be essential in further considering this work for publication. __

__We thank the reviewer for recognizing the importance of our work and appreciate the positive reflections on our manuscript and the feedback comments that were well thought-out and articulated and will further strengthen the conclusions of our manuscript. Our planned revisions focus on addressing the reviewer’s comments especially in further supporting our conclusions for proximity-labeling, phenotypic characterization and immunoprecipitation experiments, examining CCDC15 centriole localization in an additional cell line and investigating how CCDC15 works together during centriole length control with known components of the inner scaffold. __

Major points:

__1a) The authors use Poc5 and Centrin-2 molecules as joint baits to reveal the interactome of the centriole inner scaffold, however the work lacks appropriate experimental and analytical controls to argue that this is a proximity mapping "at the centriole inner scaffold". In its current state, it is simply an interactome of total Poc5 and Centrin-2, and it might be misleading to call it an interactome at the centriole inner scaffold (the statistical identification of shared interactors cannot do full justice to their biology at the centrosome). Appropriate expression data needed to delineate how large the centrosomal vs. cytoplasmic (or nucleoplasmic) fraction is for either of these molecules, both without and upon the addition of biotin (to see whether the bulk of interaction data stem from the cytoplasm/nucleoplasm or the centrioles themselves). The authors can test this by selectively blotting a lysate fraction containing the centrosomes after centrifugation, and compare them with the simultaneous blot of the supernatant (which were readily used for the blots presented in Fig. 1B). This experiment also becomes very relevant for the case of Centrin-2, as it also heavily localizes to the nucleoplasm as the authors found out (see Fig. 1A and Fig. S1A). __

__ Additionally, an orthogonal approach should be taken to perform bio-image analysis on their biotin/streptavidin imaging data to demonstrate the exact ratios between the centrosomal vs. cytoplasmic/nucleoplasmic biotin activation with appropriate signal normalization between the biotin/streptavidin images. This is particularly important, as although the authors claim that these cells stably express the V5BirA*, it seems that there is partial clonality to the expression. Some cells in both the Poc5 and Centrin-2 fusion constructs appear to lack the V5/Streptavidin signals upon Biotin addition (such as the two cells in the centre right in Poc5, and again a cell in the centre right for Centrin-2 images). In its current form, Fig. 1A lacks signal quantification and does not report any information about the replicates and distributions of the data. I worry that this may raise concerns on the reproducibility if published in its current form. __a) We agree with the reviewer that the proximity maps of POC5 and

a) Centrin-2 are not specific to the centriole inner scaffold and thus, do not represent the inner scaffold interactome. The proximity maps identified interactions across different pools of POC5 and Centrin-2 in nucleus, cytoplasm and centrosomes (Fig. 1, S1). To highlight these important points, we already included extensive analysis of the different cellular compartments and biological processes identified by the POC5 and Centrin-2 proximity maps in the results section (pg. 9-10).

We think that there are two reasons that caused the misinterpretation of the use of these proximity maps as the “inner scaffold interactome”: 1) the way we introduced the motivation for proximity mapping studies, 2) proposing the use of the resulting interactomes as resources for identification of the full repertoire of the inner scaffold proteins. To clarify these points, we revised the manuscript in all relevant parts that might have led to misinterpretation. Following are the specific revisions:

• To clarify that the proximity maps are not specific to the inner scaffold pools of POC5 and Centrin-2, we revised the title of the results section for Fig. 1 and 2 as follows: “Proximity mapping of POC5 and Centrin-2 identifies new centriolar proteins”.

• To indicate that POC5 and Centrin-2 localizes to the cytoplasm and/or nucleus in addition to the centrosome, we added the following sentence to the result section: “In addition to centrosomes, both fusion proteins also localized to and induced biotinylation diffusely in the cytoplasm and/or nucleus (Fig. 1A).”

• In the introduction, we revised the following sentence “Here, we used the known inner scaffold proteins as probes to identify the molecular makeup of the inner scaffold in an unbiased way.” as follows: *“Here, we used the known inner scaffold proteins as probes to identify new components of the inner scaffold”. *

• To highlight the different cellular pools of POC5 and Centrin-2 and identification of their interactors in these pools, we included the following sentence in the results section: “As shown in Fig. S1, Centrin-2 and POC5 proximity interactomes were enriched for GO categories that are relevant for their published functions during centrosomal, cytoplasmic and/or nuclear biological processes and related cellular compartments (Azimzadeh et al., 2009; Dantas et al., 2013; Heydeck et al., 2020; Khouj et al., 2019; Resendes et al., 2008; Salisbury et al., 2002; Steib et al., 2020; Yang et al., 2010; Ying et al., 2019).”

• We replaced the “interactome” statement with “proximity interaction maps” or “proximity interactors” throughout the manuscript to prevent the conclusion that the proximity maps represent the inner scaffold interactome. b) As the reviewer noted, most centrosome proteins have multiple different cellular pools including the centrosome. For most proteins like gamma-tubulin and centrin, their cytoplasmic/nucleoplasmic pools are more abundant than their centrosomal pools (Moudjou et al., 1996; Paoletti et al., 1996). For the Firat-Karalar et al. Current Biology 2015 paper, I compared the biotinylation levels of centrosomal fractions versus cytoplasmic fractions and confirmed that this is also true in cells expressing myc-BirA* fusions of CDK5RAP2, CEP192, CEP152 and CEP63 (unpublished) (Firat-Karalar et al., 2014). For the revised manuscript, we will compare the biotinylation level of centrosomal, nuclear and cytoplasmic pools of V5Bir*-POC5 and V5BirA*-Centrin-2 using the stable lines. To this end, we will use published centrosome purification protocols. We will include this data in Fig. S1 to highlight that the proximity interactomes represent the different pools of the bait proteins and to show the relative levels of the baits across their different pools.

c) BioID approach has been successfully used to probe centrosome interactions by my lab and other labs in the field. In fact, proximity interaction maps of over 50 centrosome proteins were published as resource papers by Pelletier&Gingras labs (Gheiratmand et al., 2019; Gupta et al., 2015). Analogous to our strategy in this manuscript, these studies generated proximity maps of centrosome proteins by creating cell lines that stably express BioID-fusions of centrosome proteins followed by streptavidin pulldowns from whole cell extracts and mass spectrometry analysis. Since majority of centrosome proteins also have pools in multiple cellular locations, the published BioID proximity maps for centrosome proteins are not specific to centrosomes. However, the proximity maps included all known centrosome proteins and identified new proteins, which shows that centrosome interactions are represented in pulldowns form whole cell lysates. Moreover, maps form whole cell lysates are also advantageous as they are are unbiased and can be used in future studies as resources for studying the functions and interactions of the bait proteins in different contexts.

In the Firat-Karalar et al. Current Biology 2015 paper, I combined centrosome purifications with BioID pulldowns to enrich for the centrosomal interactions in the proximity maps of centriole duplication proteins(Firat-Karalar et al., 2014). However, I started the purification with cells transiently transfected with the BioID-fusion constructs, which resulted in high ectopic expression of the fusions in the cytoplasm and/or nucleus. Therefore, centrosome enrichments were useful as an additional step before mass spectrometry. Comparative analysis of the data for proximity maps of 4 centrosome proteins generated from stable lines or centrosome fractions of transiently transfected cells substantially overlap as compared in the Gupta et al. Cell 2015 study and were more comprehensive (Table S2) (Gupta et al., 2015). Therefore, we are confident that the proximity interactomes we generated for POC5 and Centrin-2 include their centrosomal interactions.

__1b) Similarly, it is not clear whether the expression of Poc5 and Centrin-2 fusion molecules somehow interfere with their endogenous interactions or function. At least some loss-of-function (e.g., RNAi) experiments should be performed where the depletion of endogenous proteins should be attempted to rescue by the fusion constructs. This will help evaluate whether the fusion proteins can rescue the depletion of their endogenous counterparts and behave as expected from a wild-type scenario. __

The reviewer raises an important concern regarding the physiological relevance of the POC5 and Centrin-2 proximity maps. In the manuscript, we showed and discussed the validation of their proximity interactomes by two lines of evidence, which are: 1) the interactomes identified the previously described cellular compartments, biological processes or interactors of POC5 and Centrin-2, 2) the interactomes led to the identification of CCDC15 as a new inner scaffold protein.

As the reviewer indicated, stable expression of POC5 and Centrin-2 in the presence of their endogenous pools might affect cellular physiology and thereby the landscape of the interactomes. We plan to address this using the following experiments:

a) We will perform a set of functional assays to assess whether stable V5BirA*-Centrin-2 and V5BirA*-POC5 cells behaves like control cells in terms of their centrosome number, cell cycle profiles and mitotic progression. We will specifically quantify:

• centrosome number (immunofluorescence analysis for gamma-tubulin and centrin)
• their mitotic index (immunofluorescence analysis by DAPI)
• spindle polarity and percentage of multinucleation (immunofluoerescence analysis for microtubules, gamma-tubulin and DAPI)
• cell cycle profiles (flow cytometry and immunofluorescence)
• apoptosis (immunoblotting for caspase 3) Together, results from these experiments indicate that the V5BirA*-POC5 or Centrin-2-expressing stable lines do not exhibit defects associated with their stable expression.

b) We will perform expansion microscopy in V5BirA*-Centrin-2 and V5BirA*-POC5 cells to assess whether the fusion protein specifically localizes to the centriole inner scaffold, which will provide support for the presence of inner scaffold proteins in their proximity maps. Specifically, we plan to stain the fusion proteins by V5 or BirA antibodies and include the data for the antibody that works for expansion microscopy. This experiment will address whether their stable expression results in specific localization of these proteins at the centriole inner scaffold.

1c) Overall, as the entire claim around the proximity mapping revolve around its assumption about the centriole inner scaffold, these controls seem imperative to substantiate the ground truth of the biology presented in the manuscript.

In the revised manuscript, we toned down and made it clear that Centrin-2 and POC5 proximity maps are not specific to the inner scaffold and do not represent the inner scaffold interactome. Since the maps were generated from the whole cell extract, they will provide a resource for future studies aimed at studying functions and mechanisms of POC5 and Centrin-2 across their different cellular pools including the centrosome.

We would like to also highlight that the proximity maps of POC5 and Centrin-2 are not the major advances of our manuscript. The major advance of our manuscript is the identification of CCDC15 as a new inner scaffold protein that is required for regulation of centriole size and architectural integrity and thereby, for maintaining the ability of centrioles to template the assembly of functional cilia. Importantly, our results identified CCDC15 as the first dual regulator of centriolar recruitment of inner scaffold protein POC1B and the distal end SFI1/Centrin complex and provided important insight into how inner scaffold proteins work together during centriole integrity and size regulation. The new set of experiments we will perform for the revisions of the paper will strengthen these conclusions.

__2) I am curious about the choices of the cell lines in this work. The proximity mapping to reveal CCDC15 as a candidate protein for centriole inner scaffold was performed in HEK293T cells (human embryonic kidney), however its immunostaining was performed using RPE1 and U2OS cells (human retinal and osteosarcoma epithelial cells respectively). This raises questions regarding the generality of CCDC15 as a centriole inner scaffold protein. Could CCDC15 be simply unique to the centriole inner scaffold of epithelial cells such as RPE1 and U2OS cells? Or could the authors demonstrate any information/data on whether it's similarly localized to the inner scaffold in embryonic kidney cells or other cell types? If not, the claims should be moderated to reflect this fine detail. __

To test whether CCDC15 localizes to the inner scaffold in other cell types, we performed U-ExM analysis of CCDC15 localization relative to the centriolar microtubules in differentiating multiciliated epithelial cultures (MTEC). As shown in Fig. S3A, CCDC15 localized to the inner scaffold in the centrioles in MTEC ALI+4 cells. Given that the inner scaffold proteins including CCDC15 and previously characterized ones have not been studied in multiciliated epithelia, this result is important and provides support for potential role of the inner scaffold in ensuring centriole integrity during ciliary beating. Additionally, we examined CCDC15 localization by 3D-SIM in centrosomes purified from HEK293T cells, which showed that CCDC15 localizes between the distal centriole markers CEP164 and Centrin-3 and proximal centriole markers gamma-tubulin and rootletin (Fig. S3B).

3) Discussions and data on the localization of CCDC15 to centriolar satellites appear anecdotal and not fully convincing (Fig. S2D). Given that the authors test the relevance of PCM1 for CCDC15's centriolar localization, it is key to have quantitative data supporting their claim that centriolar satellites can help recruit CCDC15 to the centriole. Could the authors quantify what proportion of CCDC15 localize to the centriolar satellites? One way to do this could be to quantify the colocalization coefficience of CCDC15 and PCM1 signals.

We only observed co-localization of CCDC15 with the centriolar satellite marker PCM1 in cells transiently transfected with mNG-CCDC15. In Fig. S2E, we included the quantification of the percentage of U2OS and RPE1 cells that exhibit co-localization of PCM1 (100% of U2OS cells, about 80% of RPE1 cells). Like CCDC15, ectopic expression of WDR90 revealed its centriolar satellite localization, suggesting a potential link between centriolar satellites and inner scaffold proteins that can be investigated in future studies (Steib et al., 2020). We now included these results in the discussion section as follows:

“As assessed by co-localization with the centriolar satellite marker PCM1, mNG-CCDC15 localized to centriolar satellites in all U2OS cells and in about 80% of RPE1 cells (Fig. S2C-E). Association of CCDC15 with centriolar satellites is further supported by its identification in the centriolar satellite proteomes(Gheiratmand et al., 2019; Quarantotti et al., 2019).”

Even though endogenous staining for CCDC15 did not reveal its localization to centriolar satellites, following lines of data support the presence of a dynamic and low abundance pool of CCDC15 at the centriolar satellites: 1) CCDC15 was identified in the centriolar satellite proteome and interactome (Gheiratmand et al., 2019; Quarantotti et al., 2019). 2) CCDC15 centrosomal targeting is in part regulated by PCM1 (Fig. S2F, S2G). For majority of the proteins identified in the centriolar satellite proteome, their satellite pool can only be observed upon ectopic expression. This might be because their centriolar satellite pool is of low abundance and transient as satellite interactions are extensively identified only in proximity mapping studies, but not in traditional pulldowns

__4) Similar to above (#3), there is no quantitative information on the co-localization or partial co-localization of the signal foci in Fig. 3A and 3B. The authors readily study CCDC15's localization in wonderful detail in their expansion microscopy data, so they could actually consider taking out Fig. 3A and 3B, as the data seem redundant without any quantification. __

To address the reviewer’s concern, we included plot intensity profile analysis of CCDC15 and different centriole markers along a line drawn at the centrioles in Fig. 3A and 3B, which shows the extent of their overlap. As part of our revision plan, we will replace the confocal imaging data in Fig. 3A and 3B with 3D-SIM imaging data of CCDC15 relative to different centriole markers together with plot profile analysis. We already included 3D-SIM imaging of centrosomes purified form HEK293T cells in Fig. S3B. 3D-SIM imaging data will complement the localization data revealed by U-ExM.

__5) Do the authors also feel that CCDC15 localize to the core lumen in a somehow helical manner (Fig. 1A, Fig. 1F top and bottom panels, Fig. 5A etc.)? Le Guennec et al. 2020's helical lattice proposal for the inner scaffold further reaffirms that CCDC15 is indeed a likely major component of the inner scaffold. In my view, authors should state this physical similarity explicitly to further support their findings on CCDC15. __

As the reviewer indicated, cryo–electron tomography and subtomogram averaging of centrioles from four evolutionarily distant species showed that centriolar microtubules are bound together by a helical inner scaffold covering ~70% of the centriole length (Le Guennec et al., 2020). Although U-ExM data do not have enough resolution to show that CCDC15 localizes in a helical manner, we agree with the reviewer that the discussion of this possibility is important and thus we included the following sentence in the results:

“Longitudinal views suggest potential helical organization of CCDC15 at the inner scaffold, which is consistent with its reported periodic, helical structure (Le Guennec et al., 2020).”

__6a) The data on the link between the CCDC15 recruitment and the centriole growth (Fig. 4F) or the G2 phase of the cell cycle (Fig. 4H) are not fully convincing without quantitative data. For Fig. 4F, the authors should consider plotting the daughter centriole length vs the daughter CCDC15 intensities against each another, to see whether more elongated daughters truly tend to have more CCDC15. __

To address the reviewer’s concern, we will plot the daughter centriole length versus CCDC15 intensity at different stages of centriole duplication. In asynchronous cultures that we analyzed with U-ExM, we were not able to find enough cells to perform such quantification. To overcome this limitation, we will perform U-ExM analysis of cells fixed at different points after mitotic shake-off and stained for CCDC15 and tubulin. We will include minimum 10 different representative U-ExM data for different stages of centriole duplication in the revised manuscript along with quantification of length versus signal.

As detailed in the results section, the goal of these experiments was to determine when CCDC15 is recruited to the procentrioles during centriole duplication, but not to suggest a role for CCDC15 in centriole growth. We clarified this by including the following sentence:

“To investigate the timing of CCDC15 centriolar recruitment during centriole biogenesis, we examined CCDC15 localization relative to the length of procentrioles that represent cells at different stages of centriole duplication (Fig. 4F).”

__6b) For Fig. 4H, the argument regarding the cell cycle regulation requires quantification of the bands from several WB repeats, normalized to the expression of GAPDH within each blot (this is particularly relevant, as the bands of CCDC15 do not look dramatically different enough to draw conclusions by eye). __

We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.

__7a) The authors find herein that CCDC15 depletion lead to centrioles that are ~10% shorter than the controls. With the depletion of Poc5 and Wdr90 (other proposed components of the inner scaffold), the centrioles end up larger however (Steib et al., 2020). If the role of inner scaffold in promoting centriole elongation is structural, why are these two results the opposite of each other? I realize there is a brief discussion about this at the end of the paper, however, this requires a detailed discussion and speculation on the relevance of these findings. It would be key to clarify whether the inner scaffold as a structure inhibits or promotes centriole growth - or somehow both? If so, how? __

We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section in pg. 19 and also included discussion of this data in the discussion section in pg. 23:

“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”

__7b) There might be some intriguing opposing regulatory action of Poc5 and CCDC15 as demonstrated here, where CCDC15 depletion leads to slightly over-recruitment of Poc5, and vice versa. Does this suggest that a tug-of-war going on between different molecules that localize to the inner scaffold? Does this provide some dynamicity to this structure, which might in turn regulate centriole length both positively and negatively? This may be analogous to how opposing forces of dyneins and kinesins provide robust length control for mitotic spindles. I am speculating here, but hopefully these may provide some useful grounds for further discussion in the paper. If the authors deem it interesting experimentally, they can test whether the two molecules indeed regulate centriole length by opposing each other's action, by a double siRNA of CCDC15 and Poc5 to see if this retains the centriole length at its control siRNA size (like how they do a similar test for Poc1's potential co-operativity with CCDC15 in Fig. 6J). __

We thank the reviewer for proposing excellent ideas on how inner scaffold proteins work together to regulate centriole length. As proposed by the reviewer, different proteins oppose each other analogous to how dynein and kinesin regulate mitotic spindle length. Loss-of-function and localization dependency data support that CCDC15 cooperates with POC1B, which was supported by phenotypic characterization of co-depleted cells (Fig. 6I-K).

The increase in POC5 levels and coverage at the centrioles upon CCDC15 depletion and vice versa (Fig. 7B, 7G) suggest that CCDC15 and POC5 compete with each other in centriole length regulation. As suggested by the reviewer, we attempted to test this by comparing centriole length in cells co-depleted for CCDC15 and POC5 relative to their individual depletions. Although we tried different depletion workflows, we were not able to co-deplete CCDC15 and POC5. Specifically, we tried transfecting cells with CCDC15 and POC5 siRNAs at the same time or sequentially for 48 h or 96 h. The centrioles in cells that survived co-depletion were positive for both CCDC15 and POC5. This might be because co-depletion of both proteins is toxic to cells. Since CCDC15 and POC5 are likely part of two different pathway in regulation of centrioles and also have other cellular functions, this might have caused cell death. We included the following statement in the discussion to address the excellent model proposed by the reviewer:

“Taken together, our results suggest that CCDC15 cooperates with POC1B and competes with POC5 during centriole length regulation. Moreover, they also raise the exciting possibility that centriole length can be regulated by opposing activities of inner scaffold proteins. Future studies that explore the relationship among centriole core proteins are required to uncover the precise mechanisms by which they regulate centriole integrity and size.”

__8) In their introduction section, the authors discuss how relatively little is known about the size control of centrioles, however they fail to mention a series of recent primary literature that uncover striking, new mechanisms and novel molecular players that highlight the complexity of centriole size control. This complexity appears to arise from the existence of multitude of length control mechanisms that influence the cartwheel or the microtubule length individually, or simultaneously via yet-to-be further explored crosstalk mechanisms. a. As such, when the authors talk about the procentriole size control in the introduction, they should discuss and refer to the following studies, in terms of: • How theoretical and experimental work demonstrate that procentriole length may vary dependent on the levels of its building block Sas-6 in animals (Dias Louro et al., 2021 PMID: 33970906; Grzonka and Bazzi, 2022 bioRxiv). • How a homeostatic Polo-like kinase 4 clock regulates centriole size during the cell cycle (Aydogan et al., 2018 JCB PMID: 29500190), and how biochemistry and genetics coupled with mathematical modelling unravel a conserved negative feedback loop between Cep152 and Plk4 that constitutes the oscillations of this clock in flies (Boese et al., 2018 PMID: 30256714; Aydogan et al., 2020 PMID: 32531200) and human cells (Takao et al., 2019 PMID: 31533936). __

__b. Similarly, when the authors refer to centriole size control induced by microtubule-related proteins, they should highlight the further complexity of this process by referring to: • How a molecule located at the microtubule wall, Cep295/Ana1, can regulate centriole length in flies (Saurya et al., 2016 PMID:27206860) and human cells (Chang et al., 2016 PMID:27185865) - like all the other centriolar MT molecules that the authors discuss in the manuscript. • How a crosstalk between Cep97 and Cep152 influences centriole growth in fly spermatids (Galletta et al., 2016 PMID:27185836). • How a crosstalk between CP110-Cep97 and Plk4 influences centriole growth in flies (Aydogan et al., 2022 PMID:35707992), and this molecular crosstalk is conserved, at least biochemically, in human cells (Lee et al., 2017 PMID:28562169). __

We thank the reviewer for highlighting the papers that uncovered new mechanisms and players of centriole size and integrity control as well as for the detailed explanation of how different studies led to these discoveries in different organisms. We should have discussed these proteins, functional complexes and mechanisms in our manuscript and cited the relevant literature. We inadvertently focused on literature that uncovered centriole length regulation by MAPs and the inner scaffold. In the introduction section of the revised manuscript where we introduced centriole size regulation in pg. 5, we summarized the major findings on the role of different MAPs, cartwheel and PLK4 homeostatic clock in ensuring formation of centrioles at the correct size in different organisms.

__Minor points: __

__1) Introduction section: Literature reference missing for the sentence starting with "Importantly, the stable nature of centrioles enables them to withstand...". __

We cited research articles that show the importance of centriole motility during ciliary motility and cell division.

“Importantly, the stable nature of centrioles enables them to withstand mechanical forces during cell division and upon ciliary and flagellar motility (Abal et al., 2005; Bayless et al., 2012; Meehl et al., 2016; Pearson et al., 2009).

__2) Fig. S1 legend: A typo as follows: CRAPome banalysis should read CRAPome analysis. __

We corrected this typo.

__3) Fig. S2: Info on the scale bar in the legend is missing in Fig. S2A. Scale bars for different panels are missing in general in Fig. S2A. __

We added scale bar information for Fig. S2A and to all other supplementary figure legends that lack scale bar information.

__4) Fig. 3A and 3B: When displaying the data, coloured cartoon diagrams would be beneficial to guide the reader who are not fully familiar with the spatial orientation of these proteins. __

As suggested by the reviewer, we will remove the confocal imaging data for CCDC15 localization from Fig. 3A and 3B. For the revised version, we will include 3D-SIM imaging data along with a diagram that represents the spatial orientation of CCDC15 relative to the chosen centriole markers.

__5) Fig. 3H: No information about the sample number (number of cells or technical repeats examined) reported. __

We included information on the number of experimental replicates and cells analyzed.

__6) Fig. S3B legend: A typo as follows: CCD15-depelted RPE1 cells should read CCDC15-depleted RPE1 cells. __

We corrected this typo.

__7) Fig. S3B legend: A typo as follows: cellswere fixed with should read cells were fixed with. __

We corrected this typo.

__8) There are many spelling mistakes and typos throughout the paper. I have listed a few examples above, but please carefully read through the manuscript to correct all the errors. __

Thank you for indicating the spelling mistakes we missed to correct for initial submission. In the revised manuscript, we carefully read through the manuscript to correct the mistakes.

__9) Fig. S3E: The orange columns depicting % of cells with Sas-6 dots look awkward. Why the columns look larger than the mean line? Please correct as appropriate. __

The total percentage of cells in the two categories (orange and purple) we counted is 100%, which corresponds to the column value at the y-axis. Therefore, the value for each experimental replicate for the orange category is less than 100% and is marked below the 100% line.

__10) Although authors provide microscopy information for the U-ExM and FRAP experiments, there is no information about the microscopy on regular confocal imaging experiments which should be detailed in Materials and Methods. Also, there is no information about the lenses, laser lines and the filter sets that were used in the imaging experiments. These should be provided as well. __

In the methods section, we now included detailed information for the microscopes we used and imaging setup (lenses, laser lines, filter sets, detectors, z-stack size, resolution).

11)

• __ Fig. 2A: lacks a scale bar. __
• __ Fig. 2C legend: lacks info on the scale bar length. __
• __ Fig. 5A legend: lacks info on the scale bar length. __
• __ Fig. 7A: lacks a scale bar. __
• __ Fig. 7G legend: lacks info on the scale bar length. __
• __ Fig. S2C-E: lack scale bars. __
• __ Fig. S3D, F and H: lack scale bars. (Fig. S4 in the revised manuscript)__
• __ Fig. S3J legend: lacks info on the scale bar length. (Fig. S4 in the revised manuscript)__
• __ Fig. S4A, B, D and E: lack scale bars. (Fig. S5 in the revised manuscript)__
• __ Fig. S4C legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__
• __ Fig. S4G legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__ We added the scale bars and the size information to the figures and figure legends for the above figures.

Reviewer #2 (Significance (Required)): __The findings of this study join among the relatively new literature (e.g., Steib et al., 2020 and Le Guennec et al. 2020) on the nature of centriole inner scaffold and its potential roles in centriole formation, integrity and its propensity to form the primary cilium. Therefore, it will be of interest to a group of scientists studying these topics in the field of centrosomes/cilia.

My expertise is on the biochemistry and genetics of centriole formation in animals.__

We thank the reviewer for his/her comments and constructive feedback to improve our manuscript. We are encouraged to see that the reviewer acknowledges how the results from our manuscript advances our understanding of centriole length, integrity and function regulation.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, Arslanhan et al. propose CCDC15 as a novel component of the centriole inner scaffold structure with potential roles in centriole length control, stability and the primary cilium formation in cultured epithelial cells. Using proximity labelling they explore the common interactors of Poc5 and Centrin-2, two resident molecules of the centriole inner scaffold, to hunt for novel regulators of this structure. The authors leverage expansion microscopy-based localization and siRNA-dependent loss-of-function experiments to follow up on one such protein they identify, CCDC15, with the aforementioned roles in centriole and cilia biology.

This study is designed and laid out nicely; however, to be able to support some of the important claims regarding their proximity labelling results and exploration on the roles of CCDC15, there are several major technical and reproducibility concerns that deem major revision. Similarly, the introduction (perhaps inadvertently) omits much of the recent studies on centriole size control that have highlighted the complexity of this biological problem. As such, addressing the following major points will be essential in further considering this work for publication.

Major comments:

1. The authors use Poc5 and Centrin-2 molecules as joint baits to reveal the interactome of the centriole inner scaffold, however the work lacks appropriate experimental and analytical controls to argue that this is a proximity mapping "at the centriole inner scaffold". In its current state, it is simply an interactome of total Poc5 and Centrin-2, and it might be misleading to call it an interactome at the centriole inner scaffold (the statistical identification of shared interactors cannot do full justice to their biology at the centrosome). Appropriate expression data needed to delineate how large the centrosomal vs. cytoplasmic (or nucleoplasmic) fraction is for either of these molecules, both without and upon the addition of biotin (to see whether the bulk of interaction data stem from the cytoplasm/nucleoplasm or the centrioles themselves). The authors can test this by selectively blotting a lysate fraction containing the centrosomes after centrifugation, and compare them with the simultaneous blot of the supernatant (which were readily used for the blots presented in Fig. 1B). This experiment also becomes very relevant for the case of Centrin-2, as it also heavily localizes to the nucleoplasm as the authors found out (see Fig. 1A and Fig. S1A).

Additionally, an orthogonal approach should be taken to perform bio-image analysis on their biotin/streptavidin imaging data to demonstrate the exact ratios between the centrosomal vs. cytoplasmic/nucleoplasmic biotin activation with appropriate signal normalization between the biotin/streptavidin images. This is particularly important, as although the authors claim that these cells stably express the V5BirA*, it seems that there is partial clonality to the expression. Some cells in both the Poc5 and Centrin-2 fusion constructs appear to lack the V5/Streptavidin signals upon Biotin addition (such as the two cells in the centre right in Poc5, and again a cell in the centre right for Centrin-2 images). In its current form, Fig. 1A lacks signal quantification and does not report any information about the replicates and distributions of the data. I worry that this may raise concerns on the reproducibility if published in its current form.

Similarly, it is not clear whether the expression of Poc5 and Centrin-2 fusion molecules somehow interfere with their endogenous interactions or function. At least some loss-of-function (e.g., RNAi) experiments should be performed where the depletion of endogenous proteins should be attempted to rescue by the fusion constructs. This will help evaluate whether the fusion proteins can rescue the depletion of their endogenous counterparts and behave as expected from a wild-type scenario.

Overall, as the entire claim around the proximity mapping revolve around its assumption about the centriole inner scaffold, these controls seem imperative to substantiate the ground truth of the biology presented in the manuscript. 2. I am curious about the choices of the cell lines in this work. The proximity mapping to reveal CCDC15 as a candidate protein for centriole inner scaffold was performed in HEK293T cells (human embryonic kidney), however its immunostaining was performed using RPE1 and U2OS cells (human retinal and osteosarcoma epithelial cells respectively). This raises questions regarding the generality of CCDC15 as a centriole inner scaffold protein. Could CCDC15 be simply unique to the centriole inner scaffold of epithelial cells such as RPE1 and U2OS cells? Or could the authors demonstrate any information/data on whether it's similarly localized to the inner scaffold in embryonic kidney cells or other cell types? If not, the claims should be moderated to reflect this fine detail. 3. Discussions and data on the localization of CCDC15 to centriolar satellites appear anecdotal and not fully convincing (Fig. S2D). Given that the authors test the relevance of PCM1 for CCDC15's centriolar localization, it is key to have quantitative data supporting their claim that centriolar satellites can help recruit CCDC15 to the centriole. Could the authors quantify what proportion of CCDC15 localize to the centriolar satellites? One way to do this could be to quantify the colocalization coefficience of CCDC15 and PCM1 signals. 4. Similar to above (#3), there is no quantitative information on the co-localization or partial co-localization of the signal foci in Fig. 3A and 3B. The authors readily study CCDC15's localization in wonderful detail in their expansion microscopy data, so they could actually consider taking out Fig. 3A and 3B, as the data seem redundant without any quantification. 5. Do the authors also feel that CCDC15 localize to the core lumen in a somehow helical manner (Fig. 1A, Fig. 1F top and bottom panels, Fig. 5A etc.)? Le Guennec et al. 2020's helical lattice proposal for the inner scaffold further reaffirms that CCDC15 is indeed a likely major component of the inner scaffold. In my view, authors should state this physical similarity explicitly to further support their findings on CCDC15. 6. The data on the link between the CCDC15 recruitment and the centriole growth (Fig. 4F) or the G2 phase of the cell cycle (Fig. 4H) are not fully convincing without quantitative data. For Fig. 4F, the authors should consider plotting the daughter centriole length vs the daughter CCDC15 intensities against each another, to see whether more elongated daughters truly tend to have more CCDC15. For Fig. 4H, the argument regarding the cell cycle regulation requires quantification of the bands from several WB repeats, normalized to the expression of GAPDH within each blot (this is particularly relevant, as the bands of CCDC15 do not look dramatically different enough to draw conclusions by eye). 7. The authors find herein that CCDC15 depletion lead to centrioles that are ~10% shorter than the controls. With the depletion of Poc5 and Wdr90 (other proposed components of the inner scaffold), the centrioles end up larger however (Steib et al., 2020). If the role of inner scaffold in promoting centriole elongation is structural, why are these two results the opposite of each other? I realize there is a brief discussion about this at the end of the paper, however, this requires a detailed discussion and speculation on the relevance of these findings. It would be key to clarify whether the inner scaffold as a structure inhibits or promotes centriole growth - or somehow both? If so, how?

There might be some intriguing opposing regulatory action of Poc5 and CCDC15 as demonstrated here, where CCDC15 depletion leads to slightly over-recruitment of Poc5, and vice versa. Does this suggest that a tug-of-war going on between different molecules that localize to the inner scaffold? Does this provide some dynamicity to this structure, which might in turn regulate centriole length both positively and negatively? This may be analogous to how opposing forces of dyneins and kinesins provide robust length control for mitotic spindles. I am speculating here, but hopefully these may provide some useful grounds for further discussion in the paper. If the authors deem it interesting experimentally, they can test whether the two molecules indeed regulate centriole length by opposing each other's action, by a double siRNA of CCDC15 and Poc5 to see if this retains the centriole length at its control siRNA size (like how they do a similar test for Poc1's potential co-operativity with CCDC15 in Fig. 6J). 8. In their introduction section, the authors discuss how relatively little is known about the size control of centrioles, however they fail to mention a series of recent primary literature that uncover striking, new mechanisms and novel molecular players that highlight the complexity of centriole size control. This complexity appears to arise from the existence of multitude of length control mechanisms that influence the cartwheel or the microtubule length individually, or simultaneously via yet-to-be further explored crosstalk mechanisms.

a. As such, when the authors talk about the procentriole size control in the introduction, they should discuss and refer to the following studies, in terms of: - How theoretical and experimental work demonstrate that procentriole length may vary dependent on the levels of its building block Sas-6 in animals (Dias Louro et al., 2021 PMID: 33970906; Grzonka and Bazzi, 2022 bioRxiv). - How a homeostatic Polo-like kinase 4 clock regulates centriole size during the cell cycle (Aydogan et al., 2018 JCB PMID: 29500190), and how biochemistry and genetics coupled with mathematical modelling unravel a conserved negative feedback loop between Cep152 and Plk4 that constitutes the oscillations of this clock in flies (Boese et al., 2018 PMID: 30256714; Aydogan et al., 2020 PMID: 32531200) and human cells (Takao et al., 2019 PMID: 31533936).

b. Similarly, when the authors refer to centriole size control induced by microtubule-related proteins, they should highlight the further complexity of this process by referring to: - How a molecule located at the microtubule wall, Cep295/Ana1, can regulate centriole length in flies (Saurya et al., 2016 PMID:27206860) and human cells (Chang et al., 2016 PMID:27185865) - like all the other centriolar MT molecules that the authors discuss in the manuscript. - How a crosstalk between Cep97 and Cep152 influences centriole growth in fly spermatids (Galletta et al., 2016 PMID:27185836). - How a crosstalk between CP110-Cep97 and Plk4 influences centriole growth in flies (Aydogan et al., 2022 PMID:35707992), and this molecular crosstalk is conserved, at least biochemically, in human cells (Lee et al., 2017 PMID:28562169).

Minor comments:

• Introduction section: Literature reference missing for the sentence starting with "Importantly, the stable nature of centrioles enables them to withstand...".
• Fig. S1 legend: A typo as follows: CRAPome banalysis should read CRAPome analysis.
• Fig. S2: Info on the scale bar in the legend is missing in Fig. S2A. Scale bars for different panels are missing in general in Fig. S2A.
• Fig. 3A and 3B: When displaying the data, coloured cartoon diagrams would be beneficial to guide the reader who are not fully familiar with the spatial orientation of these proteins.
• Fig. 3H: No information about the sample number (number of cells or technical repeats examined) reported.
• Fig. S3B legend: A typo as follows: CCD15-depelted RPE1 cells should read CCDC15-depleted RPE1 cells.
• Fig. S3B legend: A typo as follows: cellswere fixed with should read cells were fixed with.
• There are many spelling mistakes and typos throughout the paper. I have listed a few examples above, but please carefully read through the manuscript to correct all the errors.
• Fig. S3E: The orange columns depicting % of cells with Sas-6 dots look awkward. Why the columns look larger than the mean line? Please correct as appropriate.
• Although authors provide microscopy information for the U-ExM and FRAP experiments, there is no information about the microscopy on regular confocal imaging experiments which should be detailed in Materials and Methods. Also, there is no information about the lenses, laser lines and the filter sets that were used in the imaging experiments. These should be provided as well.
• Fig. 2A: lacks a scale bar.
• Fig. 2C legend: lacks info on the scale bar length.
• Fig. 5A legend: lacks info on the scale bar length.
• Fig. 7A: lacks a scale bar.
• Fig. 7G legend: lacks info on the scale bar length.
• Fig. S2C-E: lack scale bars.
• Fig. S3D, F and H: lack scale bars.
• Fig. S3J legend: lacks info on the scale bar length.
• Fig. S4A, B, D and E: lack scale bars.
• Fig. S4C legend: lacks info on the scale bar length.
• Fig. S4G legend: lacks info on the scale bar length.

Significance

The findings of this study join among the relatively new literature (e.g., Steib et al., 2020 and Le Guennec et al. 2020) on the nature of centriole inner scaffold and its potential roles in centriole formation, integrity and its propensity to form the primary cilium. Therefore, it will be of interest to a group of scientists studying these topics in the field of centrosomes/cilia.

My expertise is on the biochemistry and genetics of centriole formation in animals.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, Arslanhan and colleagues use proximity proteomics to identify CCDC15 as a new centriolar protein that co-localizes and interacts with known inner scaffold proteins in cell culture-based systems. Functional characterization using state-of-the-art expansion microscopy techniques reveals defects in centriole length and integrity. The authors further reveal intriguing aberrations in the recruitment of other centriole inner scaffold proteins, such as POC1B and the SFI1/centrin complex, in CCDC15-deficient cells, and observe defects in primary cilia.

Major comments:

• The authors present a high-quality manuscript that identifies a novel centriolar protein by elegantly revealing and comparing the proximity proteomes of two known centriolar proteins, which represents an important component for the maintenance of centrioles.
• Data are often presented from two independent experiments (n = 2), which is nice, but also the minimum for experiments in biology. It is strongly recommended to perform at least three independent experiments.
• The protein interaction studies presented in Fig. 3 could be of higher quality. While it is great that the authors compared interactions to the centriolar protein SAS6, which is not expected to interact with CCDC15, the presented data raise many questions. 1) In most cases, co-expression of tagged CCDC15 stabilizes the tested interaction partners, such that the overall abundance seems to be higher. The increase in protein abundance is substantial for Flag-FAM161A (Fig. 3D) and GFP-Centrin-2 (Fig. 3E) and is even higher for the non-interactor SAS6 (Fig. 3G), while it cannot be assessed for GFP-POC1B (Fig. 3F). Hence, the higher expression levels under these conditions make it more likely that these proteins are "pulled down" and therefore do not represent appropriate controls. 2) All Co-IP experiments are lacking negative controls in the form of proteins that are not pulled down under the presented conditions. 3) The amounts of co-precipitation of the tested proteins appears very different. Could this reflect strong or weak interactors, or does it reflect the abundance of the respective proteins in centrioles?
• The observation that IFT88 is supposedly decreased at the base of cilia in CCDC15-depleted cells requires additional experiments/evidence. Fig. 7G shows the results of n = 2 and more importantly, a similar reduction of gamma-tubulin in siCCDC15. Could the observed reduction in IFT88 be explained by a decrease in accessibility to immunofluorescence microscopy? Would the reduction in IFT88 at the base also be apparent when the signals were normalized to gamma-tubulin signals?
• The observed Hedgehog signaling defects are described as follows: "CCDC15 depletion significantly decreased the percentage of SMO-positive cells". It is similarly described in the figure legend. If this was true, the simplest explanation would be that it reflects the reduction in ciliation rate (which is in a similar range). If SMO-positive cilia (instead of "cells") were determined, the text needs to be changed accordingly.
• OPTIONAL: While expansion microscopy is slowly becoming one of the standard super-resolution microscopy methods, which is particularly well validated for studying centrioles, the authors should consider confirming part of their findings (as a proof of principle, surely not in all instances) by more established techniques. This could serve to convince critical reviewers that may argue that the expansion process may induce architectural defects of destabilized centrioles, as observed after disruptions of components, such as in Fig. 6. Alternatively, the authors could cite additional work that make strong cases about the suitability of expansion microscopy for their studies, ideally with comparisons to other methods.

Minor points:

• Text, figures, and referencing are clear and accurate, apart from minor exceptions.
• The title suggests a regulator role for CCDC15 in centriole integrity and ciliogenesis, which has formally not been shown.
• As the authors observe changes in centriole lengths in the absence of CCDC15, it would be very insightful to compare these phenotypes to other components that affect centriolar length, such as C2CD3, human Augmin complex components (as HAUS6 is identified in Fig. 1) or others. These could be interesting aspects for discussion, additional experiments are OPTIONAL.
• While the reduced ciliation rate in the absence of CCDC15 is convincing, the authors did not investigate "ciliogenesis", i.e. the formation of cilia, and hence should re-phrase. The sentence in the discussion that "CCDC15 functions during assembly" should be removed.
• The existence of stably associated CCDC15 pools with centrosomes (Fig. 2) requires further evidence. The recovery of fluorescence after photobleaching in FRAP experiments is strongly dependent on experimental setups and is only semi-quantitative. A full recovery is unrealistic, hence, it is ideally compared to a known static or known mobile component. I personally think this experiment -as it is presented now- is of little value to the overall fantastic study. The authors may consider omitting this piece of data.
• The data that CCDC15 is a cell cycle-regulated protein is not very convincing (see Fig. 3H), as the signals area weak and the experiment has been performed only once (n= 1). This piece of data does not appear to be very critical for the main conclusions of the manuscript and may be omitted. Otherwise, this experiment should be repeated to allow for proper statistical analysis.
• Experimental details on how "defective centrioles" are determined are missing.
• For figures, in which the focus should be on growing centrioles (see Fig. 4), it could be helpful to guide the reader and indicate the respective areas of the micrographs by arrows.
• Page18: "centriole length shortening" could be changed to "centriole shortening".
• It is unclear how the authors determine distal from proximal ends of centrioles in presented micrographs (see Fig. 5D).
• Fig. 7A is missing scale bars and Fig.7 overall is lacking rectangle indicators of the areas that are shown at higher magnification in the insets.
• Fig. 7C displays cilia that appear very short, especially when comparing to the micrographs and bar graphs presented. The authors may want to explain this discrepancy.

Significance

• From a technical point of view the authors use two state-of-the-art technologies, namely proximity labeling combined with proteomics and ultrastructure expansion microscopy, that are both challenging and very well suited to address the main questions of this study.
• General assessment: The presented study is of highest experimental quality. Despite being very challenging, the expansion microscopy and proximity proteomics experiments have been designed and performed very well to allow solid interpretation. The results of the central data are consistent and allow strong first conclusions about the putative function of the newly identified centriolar protein CCDC15. The study presents a solid foundation for future hypothesis-driven, mechanistic analysis of CCDC15 and inner scaffold proteins in centriole length control and maintaining centriole integrity. The only limitation of the study is that the technically simpler experiments should be repeated to allow proper statistical assessment, which can be addressed easily.
• Advance: This is the first study that identifies CCDC15 as a centriolar protein and localizes it to the inner scaffold. It further describes a function for CCDC15 in centriole length control and shows its importance in maintaining centriole integrity with consequences for stable cilia formation in tissue culture. The study provides further functional insights into the interdependence of inner scaffold proteins and the role of CCDC15 in the recruitment of the SFI1/centrin distal complex.
• Audience: The manuscript will be of broad interest to the fields of centrosome and cell biology, both from a basic research and genetics/clinical point of view due to the association with human disorders. The state-of-the-art technologies applied will be of interest to a broader cell and molecular biology readership that studies subcellular compartments and microtubules.
• Reviewer's field of expertise: Genetics, imaging, and protein-protein interaction studies with a focus on centrosomes and cilia.

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Reply to the reviewers

Manuscript number: RC-2022-01716

Corresponding author(s): Thomas, Langer

1. General Statements

We have performed a comprehensive and time-resolved analysis of the mitochondrial proteome upon induction of cellular senescence and observed rapid metabolic rewiring of mitochondria. In particular, we identified two metabolic pathways, the 1C-folate metabolism and the branched-chain amino acid (BCAA) catabolism that were rapidly rewired upon senescence induction. Our analysis therefore provides unprecedented insight into the function and metabolic adaptations of mitochondria in senescent cells, which could also serve as a reference for future studies. Moreover, we demonstrate that quantification of mitochondrial abundance using the mitochondrial volume allows to reconcile seemingly contradicting conclusions on the function/fitness of mitochondria in senescent cells. In our opinion, our studies therefore represent a valuable and significant contribution to our understanding of the role of mitochondria in senescence.

2. Point-by-point description of the revisions

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

In the manuscript "Metabolic rewiring of mitochondria in senescence revealed by the time resolved analysis of the mitochondrial proteome", Kim et al performed the proteomic approach to investigate the mitochondrial programming during senescence induction of cultural fibroblast. The main findings mentioned by author are the enhanced catabolism of branched-chain amino acids and the reduction of 1C-folate metabolism.

1. * The author claimed their approaches are "time-resolved analysis" from day 1 to day 7 during the senescence induction. However, they did not adequately describe the transition of molecular signatures and cellular states from normal cells to senescent cells in each timepoint. The authors need to quantify the protein levels of p16, p21, and p53 and transcript levels of SASP factors in each timepoint to define the stages during induction and discuss how their finding related to this transition. * As per the reviewer's requests, we monitored the molecular markers during the transition to the senescent state by decitabine. The mRNA level of CDKN1A (encoding p21) was significantly increased on days 5 and 7, while that of CDKN2A (encoding p16) was moderately but significantly increased (~40 %) on day 7 (updated Suppl. Figure 1B). Furthermore, mRNA levels of two core SASP genes, IL1A and IL6 were significantly increased on day 7.

These results complement our analysis of protein levels of senescent markers including p16 and p21 and several SASP proteins (updated Suppl. Figure 2C). Of note, decreased intracellular protein levels of HMGB1 and HMGB2 indicate a senescent rather than a pre-senescent state (PMID: 27700366; 23649808) and demonstrate that cells display transcriptomic signatures of a senescent state after decitabine treatment for seven days. However, the mass spectrometric analysis of the cellular proteome revealed an accumulation of p21 on day 5 but not on day 7 (updated Suppl. Figure 2C). We therefore performed additional experiments to further corroborate the senescent state of the cells under these conditions and to collectively address concerns raised by reviewer 1 (points 1, 5) and reviewer 2 (points 2, 3). Senescence is defined by an irreversible cell-cycle arrest. Consistently, cells maintained the proliferation-deficient state and did not re-enter the cell cycle for 7 days after the removal of decitabine (updated Suppl. Figure 1D). Moreover, cells reached a plateau of SA-b-Gal positivity on day 7, which was maintained after 7 days of decitabine removal (updated Suppl. Figure 1E). We also examined the protein levels of several senescence markers (updated Suppl. Figure 1F). DNA damage was acutely induced upon decitabine treatment as evidenced by phosphorylated H2A.X at serine 139 (p-H2A.XS139). This was accompanied by the rapid reduction of lamin B1 (LMNB1) which is a hallmark of senescence (PMID: 22496421). In agreement with the EdU data (updated Suppl. Figure 1D), the loss of phosphorylated Rb at serine 807/811 (p-RbS807/811) and cyclin A2 (CCNA2), essential for G1-S transition, from day 3 indicated a cell cycle-arrested state.

Together, we conclude that cells start to become senescent on day 5 and reach the senescent state on day 7 after decitabine treatment. We now show these data in the updated Supplementary figure 1 and modified the text accordingly.

• The authors treated decitabine and doxorubicin in different periods. Sometimes they properly prepared two different control groups, and sometimes they use only one control group. This issue should be unified. *

Proteomic analysis revealed that DMSO treatment for 7 days did not affect the cellular proteome (Reviewer figure 1), indicating that DMSO is as ineffective as H2O in our experimental conditions. When cells treated with decitabine and doxorubicin were assayed in the same experiment, cells treated with DMSO were used as a common control. When decitabine and doxorubicin-treated cells were assayed independently, either DMSO or H2O was used as the control accordingly.

Reviewer figure 1. The pairwise comparison of proteome from cells treated with DMSO at different time points. The x-axis denotes log2FC and y-axis does –log(adj.P-value). The data are of the same origin from the updated Suppl. Figure 2.

• The mitochondria dysfunction and the increasing mitochondrial mass in cellular senescence have been reported in cell culture study previously. The authors described that the mitochondrial activity normalized to mitochondria volume decreased in senescent cells, which raises the importance of the exact value (mitochondria volume) they used for normalization. However, the quantification result in Figure 1 shows obvious batch effects and variation which make their estimation not reliable enough. The authors should increase replicate numbers in image analysis to provide robust quantification results. Besides, the orthogonal method for measuring mitochondrial mass should be also performed to confirm that the FC of volume is reliable. *

We have increased the number of experiments quantifying the mitochondrial volume in senescent cells (updated Figure 1B). Despite some variation between experiments, we observed a significant increase in mitochondrial volume, which could be explained by an increased length of mitochondrial tubules, while the mitochondrial width remained unaltered. New quantification revealed an about 8-fold increase of mitochondrial volume both upon decitabine and doxorubicin treatment (about 30% lower than our original calculation). These experiments are now shown as violin plots, showing the distribution of the experimental data along with the median and quartile values (updated Figure 1B). They further substantiate our conclusion that the bioenergetic activity of mitochondria is increased per senescent cell, but decreased when calculated relative to the mitochondrial volume.

• The normalization and scaling strategy of proteomic data were not described in method. Senescent cells show increasing cell size and protein abundance. The authors should describe how they processed the peptide counts in detail. It is confused whether the up regulation (FC>1) represents the increment per cell, per mitochondrion, or in the protein abundance. *

We apologize for not being clear at this point. For clarification, we have amended the text in the method part on p. 22:

´The proportion of proteins of a certain subcellular compartment with the total cellular proteome was calculated by dividing the sum of the TMT reporter intensities for all proteins of this compartment by the sum of TMT reporter intensities for all quantified proteins. Prior to differential expression analysis, TMT reporter intensities were normalized to within the TMT multiplex using VSN (PMID: 12169536). Intensity normalization and differential expression analysis was carried out using proteins quantified in all 32 samples (total peptide counts) or using the subset of mitochondrial proteins only (mitochondria-specific peptide counts). Thus, the fold-change denotes the change in protein abundance within a given (sub-)proteome.`

• The protein amounts of CDKN1A and CDKN2A were not increased on day 7 in Sup Fig 2C. The authors need to provide the explanation of them to prevent bias in their cellular senescence-dependent findings. In addition, ARF and INK4a should be separately quantified.

*

We have performed a series of additional experiments to corroborate that cells are senescent on day 7 (see point 1). We have not detected p14ARF, but p16INK4A in our proteomic analysis. CDKN2A thus refers to p16INK4A. We have updated Supplementary figure 2C for clarification.

• This comment is also related to comment #4. In line 223, the authors mentioned "This is accompanied by a decrease in mitochondrial translation, consistent with the observed decreased respiratory activity of mitochondria in senescent cells.". First, the linkage between mitochondrial translation and respiratory activity should be further illustrated. Second, the results in Fig. 2G and 2H clearly showed that the overall respiratory activity was enhanced in senescent cells (day 7), and only the activity normalized by mitochondrial volume showed decreased. How the authors normalize proteomic data from whole cell lysates with mitochondrial mass is missed in this manuscript.*

Mitochondrial DNA encodes essential subunits of OXPHOS complexes. Therefore, decreased mitochondrial translation is accompanied by reduced respiratory activity. We have clarified this point on p. 13 of the revised manuscript.

The proteomic data show the abundance of mitochondrial proteins within the cellular proteome. Our proteomic analysis established that the mitochondrial protein mass increases proportionally to that of the cell (updated Figure 3B), consistent with the increase in mitochondrial volume. For clarification, we have now improved the description of our quantification method in the manuscript on p. 22.

Reviewer #1 (Significance (Required)):

Overall, the central findings of the study provide informative evidence to support several concepts and biological observations in previous reports. However, because of the lack of sufficient description and experimental verification, part of the conclusion is not rigorous enough and needed to be further improved.

To address the concerns of the reviewer, we provide now more experimental evidence that the cells attain the senescent state when analyzed by time-resolved proteomics and improved the description of our experimental procedures.

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

*Kim et al. applied a new method to demonstrate that senescent cells accumulate with dysfunctional mitochondria. They isolated mitochondrial to profile mitochondrial proteome in a time-dependent manner and revealed a metabolic shift in mitochondria during the senescence process. However, many groups have widely studied mitochondrial biology in senescent cells (Joao F. Passos and Thomas Von Zglinicki et al.). Based on the previous finding, cellular senescence is also known for dramatic changes in mitochondrial mass, dynamics, structure, metabolism, and function. Thus, the current work is descriptive and incremental. *

We kindly disagree with this statement of the reviewer. We do appreciate and acknowledge previous studies on mitochondria in senescent cells, but are convinced that our work provides novel insight, as to how mitochondria are affected upon establishment of senescence. Rather than considering mitochondria as dysfunctional, our proteomic and metabolomic data indicate reprogramming of mitochondria: reduced respiratory activities are accompanied by enhanced BCAA catabolism, fatty acid metabolism, and Ca2+ transport (updated Figure 4A, updated Figure 5).

We would also like to point out that several reports on the role of mitochondria in senescent cells were seemingly contradicting and difficult to reconcile with each other. Some studies observed a decreased membrane potential and increased ROS production in senescent cells, while at the same time, mitochondrial respiration appeared to be increased (PMID: 15018610, 20160708). Other studies reported an increased OXPHOS activity due to enhanced mitochondrial metabolism of glucose/pyruvate and fatty acids (PMID: 23945590, 23685455, 30778219, 22421146). Our work provides a rationale for these apparently disparate findings, highlighting that the assessment of mitochondrial function/fitness in senescent cells requires the accurate determination of mitochondrial mass/volume. We show that senescent cells harbor more mitochondria with reduced respiratory activity.

As a side note, we did not isolate mitochondria but determined the cellular proteome and analyzed organellar proteomes (such as the mitochondrial proteome) based on reference databases (see also updated Suppl. Figure 2D).

I have specific comments listed below:

*Major: 1. The authors stated that mitochondrial DNA (mtDNA) was decreased per mitochondrion. However, in Fig 2A, there is no statistical significance. So, this statement is not valid. *

We have determined mtDNA levels in two additional, independent experiments but did not observe a statistically significant decrease in senescent cells due to a relatively high experimental variability (n=5). We have updated Figure 2A and corrected the text accordingly on p. 6.

• The authors investigated the mitochondrial proteome alterations during CS development (days 1 to 7 post-treatment of decitabine). However, in supplemental Fig. 2C, p16 and p21 did not increase on day 7. So, the mitochondria authors studied are the authors studied in a pre-senescent state. What is the rationale for this study, and why did the authors not examine mitochondria at the fully senescent stage?*

We kindly disagree with the statement of the reviewer that analyzed was a pre-senescent state. As outlined in detail in reply to reviewer 1 (point 1), the analysis of a series of established senescent markers on mRNA and protein levels demonstrates that cells have reached the senescent state after seven days of drug treatment. Most importantly, we show by EdU staining in Suppl. Figure 1D that cells are in cell cycle arrest on day 7 and now provide additional evidence (EdU- and SA-b-Gal staining, senescence and cell cycle markers) that this state is maintained for another seven days, excluding a quiescent state (updated Suppl. Figure 1D, 1E). This includes the loss of lamin B1, which is associated with senescence but not quiescence (PMID: 22496421).

• The authors claimed that the fraction of mitochondrial proteins did not significantly change (Shown in Fig. 3B). Again, this could be due to cells at the pre-senescent stage; I wonder if this change could be significant after cells are fully senescent.*

As discussed above, we provide now additional evidence demonstrating that cells are in a senescent state. Of note, our findings are in agreement with a recent report (PMID: 35987199), showing that mitochondrial and cellular proteomes are altered proportionally in senescent cells.

• The data in Fig. 4E is not statistically significant. Please increase n to confirm your conclusion.*

Considering the causal relationship between mitochondrial translation and OXPHOS deficiency, we feel that this point is rather confirmatory. We therefore present now instead two representative images (updated Figure 4D)

• Are these mitochondrial proteome alterations associated with the senescent cell's functional output or other features? Are these changes cell type-dependent.*

To address the functional impact of the mitochondrial reprogramming of metabolism in senescent cells, we blocked BCAA catabolism by knocking down the rate-limiting enzyme BCKDHA, before treating cells with decitabine or doxorubicin. However, the interpretation of these experiments was hampered by increased cell death upon BCKDHA knockdown independent of DNA damage. Thus, the BCKDHA appears to be essential for cell viability under our cell culture conditions, precluding an assessment of the role of the BCAA catabolism for the functional output of senescent cells. We included these data in the updated Suppl. Figure 5D and briefly mentioned them in the text on p. 10.

• I suggest the authors clarify explicitly the knowledge gap that the current study accomplished.*

We apologize for not being clear and have revised the manuscript to clarify this point. As pointed out in the General Statement, we have performed a comprehensive and time-resolved analysis of the mitochondrial proteome upon induction of cellular senescence and observed rapid metabolic rewiring of mitochondria. In particular, we identified two metabolic pathways, the 1C-folate metabolism and the BCAA catabolism that were rapidly rewired upon senescence induction. Our analysis therefore provides unprecedented insight into the function and metabolic adaptations of mitochondria in senescent cells, which could also serve as a reference for future studies. Moreover, we demonstrate that quantification of mitochondrial abundance using the mitochondrial volume allows to reconcile seemingly contradicting conclusions on the function/fitness of mitochondria in senescent cells. In our opinion, our studies therefore represent a valuable and significant contribution to our understanding of the role of mitochondria in senescence.

Minor: Please carefully check the statistical analysis. N of 2 is not sufficient for One-way ANOVA.

We have revisited the statistical analysis of our experiments and noted a mistake in the original Figure 4E (statistical analysis with n=2). We apologize for this mistake and have corrected it (see reply point 4) as updated Figure 4D.

Reviewer #2 (Significance (Required)):

I do not see the significance of the current work. The work is descriptive and incremental, which reduce the impact of this manuscript.

My expertise is in cellular senescence and aging.

As outlined in the General Statement and in reply to reviewer 2 (point 6), we provide insight into changes in the mitochondrial proteome in senescent fibroblasts in an unprecedented manner. Although metabolic reprogramming of mitochondria has been described, our results highlight the relevance of two metabolic pathways in senescent cells, the one-carbon and the BCAA metabolism, which to our knowledge has not been described before. Moreover, our work reveals the importance to adequately quantify mitochondrial abundance, when assessing the bioenergetic activity of mitochondria in (enlarged) senescent cells.

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

The manuscript by Kim and colleagues investigated the metabolic and proteomic changes in senescent fibroblasts. The authors performed a time-resolved analysis of the proteome and revealed the impacts on mitochondrial proteome. They also applied tracing approaches to further demonstrate the impact on mitochondrial metabolism and revealed a potential impact of branched-chain amino acid catabolism and carbon-folate metabolism in senescent fibroblasts. They concluded that the reprogramming of mitochondria influences the senescence-associated secretory phenotype (SASP) impacting diseases associated with senescent cells.

1. • The authors quantified the volume of mitochondria to examine mitochondrial functions. Some data were normalized "per cell" and "per mito". Should it read per mito volume? The comparison between the two normalization procedures in Fig 2 is important but also confusing. Can the authors speculate why non-mitochondrial respiration seems to be increased in decitabine/doxorubicin conditions (Fig. 2G/H)? Are the data significantly affected after normalization to non-mitochondrial respiration?* As anticipated by the reviewer, ´per mito` indeed refers to the mitochondrial volume. We have adjusted the text on p. 6 to clarify this point.

An increase in non-mitochondrial respiration in senescent cells was also reported by the von Zglinicki group (PMID: 28330601). A major source of non-mitochondrial OCR is thought to be cytosolic/peroxisomal H2O2 production by cyclooxygenase (COX), and NADPH oxidase, which consume oxygen to produce H2O2. Especially, the cytosolic H2O2 level is known to be higher in senescent cells (PMID: 10075689). Moreover, cyclooxygenase 1 (PTGS1) is significantly upregulated in our proteomics data (Reviewer figure 2), which could explain the reason for the increased non-mitochondrial OCR in senescent cells.

Reviewer figure 2. The pairwise comparison of PTGS1 level at each time point from the proteomics data in Figure 3. **: P Of note, normalization to non-mitochondrial respiration does not significantly alter our conclusions. We observed a significant decrease in basal respiration and spare respiratory capacity both upon decitabine and doxorubicin treatment, which recapitulates our original findings taking mitochondrial abundance into account (Reviewer figure 3).

Reviewer figure 3. Oxygen consumption rates of senescent fibroblasts after normalization to non-mitochondrial OCR. (A, B) Left: representative graphs of OCR data. Right: quantification of respiratory parameters based on the OCR graph. Welch t-test, Bonferroni-Dunn correction, n=5.

• The tracing data are impactful and critical to confirm metabolic changes. Can the authors explain why they added the tracer to the regular growth medium (instead of substituting the metabolite of interest)? The media composition of the proteomic and the metabolic experiments is not identical. For instance, additional 5.5mM 13C glucose has been added to the 13C glucose tracer experiment while all other experiments were performed with 5.5mM 12C glucose only. Changes in media composition certainly affect cell function and metabolism. The authors may want to repeat key tracing experiments to mimic experimental conditions used in proteomics analysis.*

The use of glucose-containing MEM had only practical reasons, because glucose-free MEM is not commercially available. However, this does not confound our proteomic analysis between day 1 and 7, since the tracing experiments in MEM containing glucose and 13C glucose were performed to the established senescent cells on day 7.

• The impact on branched-chain amino acids is interesting. Did the authors observe 13C incorporation into the TCA cycle from BCAA? Increased BCAA catabolism may increase mitochondrial respiration, but the authors observed decreased OCR in senescent cells. Further, does inhibition of BCAA catabolism rescue the phenotype observed in senescent cells?*

We did not observe any significant incorporation of BCAA carbons into malate but found an 3-5 fold increased flux into lipogenic TCA cycle intermediates, such as acetyl-CoA and citrate (updated Figure 5D). In agreement with glucose and glutamine being the major source of lipogenic acetyl-CoAs in cell culture (PMID: 31119666), the absolute changes are rather minor. We therefore carefully discuss the possibility that BCAA carbons are metabolized to supply the lipogenic carbon moieties in senescent cells rather than increasing mitochondrial respiration in the text on p. 12.

To address the functional impact of the mitochondrial reprogramming of metabolism in senescent cells, we blocked BCAA catabolism by knocking down the rate-limiting enzyme BCKDHA, before treating cells with decitabine or doxorubicin (see also Reviewer 2, point 5). However, the interpretation of these experiments was hampered by increased cell death upon BCKDHA knockdown independent of DNA damage. Thus, the BCKDHA appears to be essential for the cell viability under our cell culture conditions, precluding an assessment of the role of the BCAA catabolism for the functional output of senescent cells. We included these data in the updated Suppl. Figure 5D and briefly mentioned them in the text on p. 10.

Reviewer #3 (Significance (Required)):

Understanding the metabolic reprogramming of mitochondria in senescent cells is interesting and of high interest to the research community. However, some clarification is needed on experimental conditions, as media compositions in proteome and metabolome experiments were different which certainly affects cell metabolism and function.

We thank the reviewer for their positive evaluation of the significance of our work. In the revised manuscript, we have now clarified the technical issues raised showing that different culture conditions do not confound our proteomic and metabolomic analysis.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Kim and colleagues investigated the metabolic and proteomic changes in senescent fibroblasts. The authors performed a time-resolved analysis of the proteome and revealed the impacts on mitochondrial proteome. They also applied tracing approaches to further demonstrate the impact on mitochondrial metabolism and revealed a potential impact of branched-chain amino acid catabolism and carbon-folate metabolism in senescent fibroblasts. They concluded that the reprogramming of mitochondria influences the senescence-associated secretory phenotype (SASP) impacting diseases associated with senescent cells.

1. The authors quantified the volume of mitochondria to examine mitochondrial functions. Some data were normalized "per cell" and "per mito". Should it read per mito volume? The comparison between the two normalization procedures in Fig 2 is important but also confusing. Can the authors speculate why non-mitochondrial respiration seems to be increased in decitabine/doxorubicin conditions (Fig. 2G/H)? Are the data significantly affected after normalization to non-mitochondrial respiration?
2. The tracing data are impactful and critical to confirm metabolic changes. Can the authors explain why they added the tracer to the regular growth medium (instead of substituting the metabolite of interest)? The media composition of the proteomic and the metabolic experiments is not identical. For instance, additional 5.5mM 13C glucose has been added to the 13C glucose tracer experiment while all other experiments were performed with 5.5mM 12C glucose only. Changes in media composition certainly affect cell function and metabolism. The authors may want to repeat key tracing experiments to mimic experimental conditions used in proteomics analysis.
3. The impact on branched-chain amino acids is interesting. Did the authors observe 13C incorporation into the TCA cycle from BCAA? Increased BCAA catabolism may increase mitochondrial respiration, but the authors observed decreased OCR in senescent cells. Further, does inhibition of BCAA catabolism rescue the phenotype observed in senescent cells?

Significance

Understanding the metabolic reprogramming of mitochondria in senescent cells is interesting and of high interest to the research community. However, some clarification is needed on experimental conditions, as media compositions in proteome and metabolome experiments were different which certainly affects cell metabolism and function

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Referee #2

Evidence, reproducibility and clarity

Kim et al. applied a new method to demonstrate that senescent cells accumulate with dysfunctional mitochondria. They isolated mitochondrial to profile mitochondrial proteome in a time-dependent manner and revealed a metabolic shift in mitochondria during the senescence process. However, many groups have widely studied mitochondrial biology in senescent cells (Joao F. Passos and Thomas Von Zglinicki et al.). Based on the previous finding, cellular senescence is also known for dramatic changes in mitochondrial mass, dynamics, structure, metabolism, and function. Thus, the current work is descriptive and incremental. I have specific comments listed below:

Major:

1. The authors stated that mitochondrial DNA (mtDNA) was decreased per mitochondrion. However, in Fig 2A, there is no statistical significance. So, this statement is not valid.
2. The authors investigated the mitochondrial proteome alterations during CS development (days 1 to 7 post-treatment of decitabine). However, in supplemental Fig. 2C, p16 and p21 did not increase on day 7. So, the mitochondria authors studied are the authors studied in a pre-senescent state. What is the rationale for this study, and why did the authors not examine mitochondria at the fully senescent stage?
3. The authors claimed that the fraction of mitochondrial proteins did not significantly change (Shown in Fig. 3B). Again, this could be due to cells at the pre-senescent stage; I wonder if this change could be significant after cells are fully senescent.
4. The data in Fig. 4E is not statistically significant. Please increase n to confirm your conclusion.
5. Are these mitochondrial proteome alterations associated with the senescent cell's functional output or other features? Are these changes cell type-dependent?
6. I suggest the authors clarify explicitly the knowledge gap that the current study accomplished.

Minor: Please carefully check the statistical analysis. N of 2 is not sufficient for One-way ANOVA.

Significance

I do not see the significance of the current work. The work is descriptive and incremental, which reduce the impact of this manuscript. My expertise is in cellular senescence and aging.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript "Metabolic rewiring of mitochondria in senescence revealed by the time resolved analysis of the mitochondrial proteome", Kim et al performed the proteomic approach to investigate the mitochondrial programming during senescence induction of cultural fibroblast. The main findings mentioned by author are the enhanced catabolism of branched-chain amino acids and the reduction of 1C-folate metabolism.

1. The author claimed their approaches are "time-resolved analysis" from day 1 to day 7 during the senescence induction. However, they did not adequately describe the transition of molecular signatures and cellular states from normal cells to senescent cells in each timepoint. The authors need to quantify the protein levels of p16, p21, and p53 and transcript levels of SASP factors in each timepoint to define the stages during induction and discuss how their finding related to this transition.
2. The authors treated decitabine and doxorubicin in different periods. Sometimes they properly prepared two different control groups, and sometimes they use only one control group. This issue should be unified.
3. The mitochondria dysfunction and the increasing mitochondrial mass in cellular senescence have been reported in cell culture study previously. The authors described that the mitochondrial activity normalized to mitochondria volume decreased in senescent cells, which raises the importance of the exact value (mitochondria volume) they used for normalization. However, the quantification result in Figure 1 shows obvious batch effects and variation which make their estimation not reliable enough. The authors should increase replicate numbers in image analysis to provide robust quantification results. Besides, the orthogonal method for measuring mitochondrial mass should be also performed to confirm that the FC of volume is reliable.
4. The normalization and scaling strategy of proteomic data were not described in method. Senescent cells show increasing cell size and protein abundance. The authors should describe how they processed the peptide counts in detail. It is confused whether the up regulation (FC>1) represents the increment per cell, per mitochondrion, or in the protein abundance.
5. The protein amounts of CDKN1A and CDKN2A were not increased on day 7 in Sup Fig 2C. The authors need to provide the explanation of them to prevent bias in their cellular senescence-dependent findings. In addition, ARF and INK4a should be separately quantified.
6. This comment is also related to comment #4. In line 223, the authors mentioned "This is accompanied by a decrease in mitochondrial translation, consistent with the observed decreased respiratory activity of mitochondria in senescent cells.". First, the linkage between mitochondrial translation and respiratory activity should be further illustrated. Second, the results in Fig. 2G and 2H clearly showed that the overall respiratory activity was enhanced in senescent cells (day 7), and only the activity normalized by mitochondrial volume showed decreased. How the authors normalize proteomic data from whole cell lysates with mitochondrial mass is missed in this manuscript.

Significance

Overall, the central findings of the study provide informative evidence to support several concepts and biological observations in previous reports. However, because of the lack of sufficient description and experimental verification, part of the conclusion is not rigorous enough and needed to be further improved.

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Reply to the reviewers

Detailed Answer to the Reviewers

Reviewer #1

__Summary __

The authors used a novel imaging technique to monitor glutamate release and correlated these measurements with gold standard electrophysiological measurements. The genetically encoded glutamate reporter, iGluSnFR, was expressed in mouse spiral ganglion neurons using the approach described in Ozcete and Moser (2021, EMBO J). The iGluSnFR signals and the postsynaptic currents were measured at the endbulb of Held synapse. A small effect of the expression of iGluSnFR on the mEPSC kinetics was found (but see comment 1). Furthermore, deconvolution of the iGluSnFR signals was performed enabling the comparison of some presynaptic properties assessed with either iGluSnFR or electrophysiology.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

__Major comments __

1. The central finding of the study is the prolonged decay time constant of the mEPSC. The difference is small but astonishingly significant (0.172 {plus minus} 0.002 and 0.158 {plus minus} 0.001, P=0.003). The SEM is about 100 times smaller than the measured time constant. This is biologically not plausible. Therefore, I am skeptical about the statistical significance of the results.

We appreciate the feedback of the reviewer. We agree that our presentation of the data was easy to misunderstand and we changed it (see below). We modeled the statistical relationship of kinetic parameters with a mixed effects model (as described in methods). Since the presentation of regression parameters for this kind of data is not very usual in synaptic neuroscience (nor very informative in this study), we instead opted to report SEM and a p-value derived from the fit of the linear mixed effects model. For the SEM, there is no clear way to take into account the clustered nature of the data, so we calculated the SEM over all observations. Since the SEM is proportional to 1/sqrt(n) and the number of recorded mEPSCs is very large, this does indeed yield a very small SEM. We agree that reporting the SEM over all observations is unusual and leads to misunderstandings in this case. Now, we instead report the re-calculated the mean / SEM for all parameters over the median values per cell. We changed the presentation of the data also for the other values presented in the MS in all tables and the relevant parts of the main texts.. We note that the summary statistics do not directly influence the further statistical modeling.

1. Analysis of the size of RRP with electrophysiology and iGluSnFR is potentially interesting but iGluSnFR recordings could not resolve the spontaneous fusion of single vesicles. Therefore, it is not possible to estimate RRP with these iGluSnFR recordings. This limitation of the approach should be emphasised more clearly.

Yes, we think the inability to resolve single vesicles is one of the major limitations of the study and we note this in the introduction and in the relevant section of the discussion. We agree that it should be clear in the relevant section that we are not able to measure RRP size without resolving single vesicle release and modified the wording of the relevant results section to reflect this better (line 267, 497). We still believe that the cumulative release analysis is potentially interesting to researchers in the field, as RRP size is not the only parameter that can be estimated in this way. In particular, an estimation of the release probability in resting conditions is possible by dividing the amplitude of the first response (i.e. response to a single stimulus) by the RRP estimate even without knowing the exact number of vesicles that comprise either.

1. The control conditions (no surgery/no virus injection) are not the correct conditions for comparison with the experimental conditions (surgery/virus injection and sensor expression). The control group should be operated and injected with saline or ideally with a virus expressing GFP at the extracellular membrane. The authors addressed this issue by citing their previous work (Özcete and Moser, 2021). However, I am not convinced that surgery does not induce subtle changes that could explain the small differences in mEPSCs.

This is an excellent point that should be addressed in further research. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.

__Minor comments __

The supplementary figures are not listed in the order in which they appear in the main text.

We now list the supplementary figures in the order in which they appear in the main text.

Figure 2B and 3 are not referenced in the main text.

We now reference the figures in the text.

The PPR in Figure 3 shows a PPR that cannot be evaluated because of the unusual plot with lines that are too thick.

We updated Fig.3 and chose a more straight forward way to display the PPRs.

Line 105: "...while simultaneously monitoring currents in postsynaptic cells". This sentence is not correct given that the EPSCs have not been shown yet at this point of the manuscript.

We removed this part of the sentence.

Line 110: "SV and are not cause are cause by spontaneous action potentials...". The sentence does not make sense.

We corrected the sentence.

Line 168-9: "...we did not find significant differences in amplitude and kinetics...". According to Table 2 (2mM Ca2+ condition), both Imax and Q appear to be almost twice as high in iGluSnFR as in control (2.05 {plus minus} 0.06 and 1.34 {plus minus} 0.03, respectively; P=0.241). Is this not a significant difference?

The difference was not significant. The misunderstanding likely stems from the same problem in the presentation of the values as for the mEPSCs. We replaced the SEMs with the SEMs of the cell median to avert this.

Table 4. 2mM Ca2+ condition. The Rrefill parameter is about an order of magnitude smaller in the iGluSnFR-expressing group. Is this correct or just a typo?

Thank you for spotting this: it was an error with regards to unit conversion. The value for the control group was off by a factor of 10. We corrected this mistake.

Referees cross-commenting

I also agree with the comments of the other reviewers.

Significance

General assessment

This topic is currently of interest because iGluSnFR techniques are widely used. However, the study is preliminary. The scientific progress in terms of quantity and quality is limited. For example, Figs. 1 and 5 show only images and traces with little scientific significance.

Advance

The main advance of the study is the implementation of the deconvolution of the iGluSnFR signal and the comparison of the back extrapolation with the first stimulus (Fig. 6). This comparison was similar between electrophysiology and iGluSnFR when deconvolution of the iGluSnFR data was performed. These data therefore argue against saturation of iGluSnFR, as expected from a large number of previous analyses of iGluSnFR.

There is little methodological improvements compared with the group's previous study (Ozcete and Moser, 2021 EMBO J). In this earlier study, a different synapse was analyzed but the same iGluSnFR was injected into the scala tympani of the right ear through the round window in the same way as in this study. Surprisingly, the authors do not refer to Ozcete and Moser (2021) in the relevant methods section.

Thank you for spotting this omission. We now cite Özçete and Moser (2021) in the appropriate place in the methods section as well.

Reviewer #2

Summary

In the manuscript 'Optical measurement of glutamate release robustly reports short-term plasticity at a fast central synapse' the authors present a careful analysis of whether direct measurements of transmitter release using the genetically-encoded indicator iGluSnFR, are suitable for assessing changes in transmitter release at the spiral ganglion neuron end bulbs of Held in the mouse cochlear nucleus. What sets this study apart from other studies, which have demonstrated the utility of iGluSnFR measurements, is the use of a camera-based fluorescence readout as opposed to confocal or 2P microscopy methods and that it is performed in the cochlear nucleus.

The primary methodology is the comparison of electrophysiological measurements of excitatory postsynaptic currents from bushy cells with fluorescence changes in the end bulbs of iGluSnFR expressing auditory nerve fibers with and without stimulation of the auditory nerve fibers. The experiments are technically demanding and introducing genetically encoded indicators in neurons of the cochlea is no small accomplishment. An important observation is that mEPSCs are slightly modified (prolonged) due to expression of iGluSnFR in the presynaptic end bulbs. This is perhaps not surprising as iGluSnFR binds glutamate and may act as a buffer to reduce the peak and slightly prolong the increase in cleft glutamate concentration after release from synaptic vesicles. To my knowledge, others have not reported iGluSnFR effects on mEPSCs. Perhaps earlier studies have not checked as carefully, alternatively previous studies had a too-low fraction of presynaptic terminals expressing iGluSnFR (or less expression of iGluSnFR) to detect a change in EPSC parameters, or this is a synapse-specific phenomenon. However, the authors demonstrate that EPSCs evoked by electrical stimulation of the auditory nerve fibers are unaffected by expression of iGluSnFR in the presynaptic neurons. Further findings are that the determined decay time constant is substantially longer than at other synapses (~16 ms at hippocampal synapses, Dürst et al., 2018). Synaptic depression was robustly reported by iGluSnFR at this synapse, but determination of single quantal events and thus quantal analysis was not really possible at this synapse using iGluSnFR in conjunction with the imaging and analysis techniques presented. The manuscript is carefully written and presented.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

Major points

1) The ROIs are selected to be 'outer bounds' of the glutamate spread from the synapses being studied. My concern is that these generously-sized ROIs include signal from many iGluSnFR molecules which are distal to the release sites and thus will be reached only slowly by low concentrations of glutamate or be contributing only noise and no changes in fluorescence. I suggest the temporal resolution could be improved by restricting the analysis of fluorescence changes to fewer pixels within the ROIs with the fastest rising/highest amplitude responses.

Thanks for this helpful comment: The data in our data set should be well-suited to perform this analysis in addition to the presented analysis and so we added this new analysis to the Revision Plan.

2) The observation that despite a 2 fold increase in eEPSCs when changing from 2 mM to 4 mM extracellular calcium there is no change in iGluSnFR peak is curious as pointed out by the authors but not really discussed.

We don’t currently have an obvious explanation but consider saturation of the iGluSnFR peak response likely to contribute. In response to the comment of the reviewer, we have added the analysis of integrated iGluSnFR data, which we previously found to be more robust toward saturation than the peak, to the revision plan. We plan to add the relevant discussion along with the new analysis.

Are the traces presented in Figure 5 examples from the same recording?

Traces in fig. 5 are grand averages (wording modified for clarity). Unfortunately, it was not possible to routinely measure iGluSnFR responses from the same cell in 2mM Ca2+ and 4 mM Ca2+ as the time needed for the protocols was rather long which influenced cell stability and imaging conditions would deteriorate during the exchange of the bath solution. We think it is not quite possible to directly compare the absolute iGluSnFR responses at different extracellular Ca2+ levels.

Assuming the examples are from one cell I first assumed the lack of change of peak was saturation of iGluSnFR but the larger fluorescence change with 100 Hz stimulation suggests otherwise. How many endbulbs are contacting one BC? Do you capture iGluSnFR responses from only one or several? In the previous point I suggested that restricting analysis to the soonest reacting pixels might improve temporal resolution but in the case of detecting the peaks with higher and normal calcium, these fastest reacting signals are probably also more likely to be saturated with glutamate.

The eEPSCs elicited by this stimulation paradigm are monosynaptic (see methods / electrophysiology section), but there might be other iGluSnFR expressing endbulbs on the same bushy cell. Since we reduce the current just enough such that any further reduction leads to a complete failure to elicit an EPSC, we believe these additional endbulbs are not releasing glutamate. We cannot, however, exclude the possibility that iGluSnFR on neighboring structures captures any potential spillover glutamate.

Minor points

• mEPSCs are usually recorded in tetrodotoxin, I didn't find any mention in methods/results

In this system, sEPSCs are not affected by TTX (Oleskevich and Walmsley, 2002) and thus usually recorded without adding TTX. We discuss this more explicitly and added a clarification to reflect this assumption (on line 111).

• the large numbers of abbreviations make it difficult in places to follow the manuscript please at least define them again in the figure legends (e.g. BC, AVCN in figure 1, Q, FWHM in figure 2 etc.)

We went over the manuscript again and removed some abbreviations or redefined them in captions.

• it is a bit unusual to report results of a Wilcoxon test and at the same time mean and SEM instead of medians, if different tests were used then it is important to indicate this where the p values are given or make the sentence in the methods more definitive

We agree that the initial presentation of the data was ambiguous. We changed the presentation to reflect this (see also answer to reviewer 1).

• the liquid junction potential is reported as 12 mV, pretty sure it should be -12 mV (unless the QX-314 or some other of the more exotic ingredients in the extracellular solution is having a dramatic effect on the LJP).

We follow the usual conventions of P. H. Barry, Methods in Enzymology, Vol. 171, p. 678, as described in E. Neher, Methods in Enzymology, Vol. 207, p. 123, in which the LJP is defined as the potential of the bath solution with respect to the pipette solution. We subtracted this positive potential (+12mV) in the end to obtain the membrane potential which therefore was more hyperpolarized than the nominal potential.

I wonder if one of the faster/lower affinity iGluSnFR variants would be better suited for studying this synapse.

We agree with the reviewer that future studies should explore the potential of faster/lower affinity iGluSnFR variants for studying the endbulb synapse. The reasons why we employed the original version include: i) sharing the same mice for studies of cochlear ribbon synapses (Özcete & Moser, 2021) and cochlear nucleus synapses (this MS) for the sake of reducing animal experiments, ii) good signal to background facilitating our first study establishing the recording in brainstem slice, iii) less signal to background and shorter signals with the new variants (as found in preliminary recordings from cochlear ribbon synapses) that would make the endbulb recordings more challenging. We have added the following statement to discussion. “Future imaging studies of glutamate release at calyceal synapses should explore the potential of new iGluSnFR variants with lower affinity that provide more rapid signal decay. This will ideally go along with imaging at higher framerate and might require stronger intensities of the excitation light to boost the fluorescence signal.” on line 430.

The paper would benefit from a careful reading to shorten the text and to check for clarity. For instance page 15 line 436 I don't understand how 'the results can reduce the likelihood of biologically relevant changes'. I think the authors meant something different

Thank you for spotting this. We reworded the sentence (now on line 399): "The data on hand suggests that this is not the case. Firstly, even if a larger sample size may uncover more subtle effects neurotransmission of evoked events, our measurements suggest a small effect size. Secondly, even as we did find changes in mEPSC, it is probable that the biological significance is limited"

• page 5 'width' is misspelled

Fixed.

• page 18 'strychnine' is misspelled

Fixed.

• on many of the figures is text that it much too small

We went through the manuscript and increased the text size in the figures, where appropriate.

__Referees cross-commenting __

I agree with all the comments of the other reviewers - both raise the point that there should be a 'control' AAV injected for comparison of the mEPSCs which I missed but is of course quite important. See https://pubmed.ncbi.nlm.nih.gov/24872574/ for a study of AAV serotype-dependent effects on presynaptic release.

We now added a section on other possible factors influencing the results, citing the study above.

Significance

The main audience for this paper will be fairly specialized. Researchers interested in properties of presynaptic release and some specialists in synaptic transmission in the auditory system will be the main readers/citers of this work.

The work is an important technical/methodological report. It highlights an important effect of expressing iGluSnFR and also demonstrates that the effect is overall not very problematic. Additional problems using iGluSnFR are also indicated.

I am an electrophysiologist, studying synaptic transmission and plasticity with experience using a wide range of optogenetic tools

Reviewer #3

__Summary __

In the present manuscript, the authors explore the information that can be obtained using optical measurement of glutamate release with iGluSnFR on synaptic dynamics in the endbulb of Held.

They virally express iGluSnFR in presynaptic terminals, patch the postsynaptic cells and combine high-frame-rate optical recordings with electrophysiological measurements. Their first finding is that mEPCSs are prolonged when presynaptic cells express the glutamate indicator, which they interpret as buffering of extracellular glutamate by the indicator. Next, they repeated the experiment, this time with stimulating evoked EPSCs. In contrast to the previously observed effects, iGluSnFR did not affect the time course or the amplitude of the evoked EPSCs. The authors then asked whether iGluSnFR signals can be used to study synaptic dynamics, specifically, synaptic depression. In these experiments, the authors observed a change in the paired-pulse ratio with ISI of 10ms, but not longer intervals. They analyzed presynaptic release and did not find statistically significant differences.

Can iGluSnFR signals be used for the analysis of synaptic release? When stimulated at a low frequency of 10Hz (allowing the fluorescence to return close to baseline levels in between pulses), iGluSnFR dynamics were somewhat comparable to postsynaptic signals. At higher frequencies, the slow time course of the indicator prevented the identification of individual responses and the resulting fluorescence had a very different shape. To resolve this problem, the authors used deconvolution analysis (fig 6). This analysis revealed a linear relationship between the optical readout and the patch-clamp data.

I find the manuscript to be clearly written, the findings are well presented and discussed and are novel and of substantial interest to neuroscientists in the field. I do have a number of questions about experiments and analysis that may have an effect on the conclusions of this work.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

1. In experiments comparing the effects of iGluSnFR expression on release dynamics (figure 1-4), the authors compare infected presynaptic cells to control (uninfected). The assumption is that synaptic buffering by iGluSnFR may affect glutamate diffusion in the synaptic cleft. However, it is possible that viral infection itself changes presynaptic properties. The authors should compare release from cells infected with GFP or a comparable indicator.

We agree that this is an important control experiment to be done in the future and that causal attribution is not in the scope of this study. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We now also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.

1. Analysis of pool parameters presented in table 4 indicates almost doubling of RRP size with iGLuSnFR with 2 mM Ca++. While not significant, this result may indicate a real effect that may have been missed due to low power (N=3 and 7 for these experiments). I do not believe the authors did a power analysis in this study. How was the number of experiments determined? I would suggest increasing the number of experiments to avoid type II errors.

We thank the reviewer for this critical comment. Indeed, we would also have liked to have a greater statistical power for these experiments, but had to face the situation that the establishing the method required more animals than expected and the animal license did not offer further animals for the analysis. Moreover, we note that the obtained RRP size estimates were generally lower compared to previous estimates of our lab for the endbulb synapse (e.g. Butola et al., 2021: ~20 nA for 2 mM Ca2+ in Fig. 5). This can partially be attributed to the use of cyclothiazide in previous studies, which we avoided given reports of presynaptic effects of cyclothiazide. As the series resistances of the included recordings were below 8 MOhm (mean series resistances: 2mM Ca, injected: 5.58 MOhm; 2mM Ca, control: 5.93 MOhm; 4mM Ca, injected: 5.75 MOhm; 4mM Ca, control: 6.0 MOhm) and series resistance compensation was set to 80% we do not expect clamp-quality to contribute to the smaller estimates in the present data set.

We have now added a statement noting the preliminary nature of these results and indicated that further experiments will be required to more certainly conclude on potential effects of iGluSnFR or the manipulation on endbulb transmission: “Our preliminary train stimulation analysis of vesicle pool dynamics in the presence and absence of AAV-mediated iGluSnFR expression in SGNs has not revealed significant differences between the two conditions. Further experiments, potentially involving faster versions of iGluSnFR and employing trains of different stimulation rates for model based analysis of vesicle pool dynamics (Neher and Taschenberger, 2021) will help to assess the value and impact of iGluSnFR in the analysis of transmission at calyceal synapses.” on line 381.

1. The deconvolution analysis assumes an instantaneous rise time. Yet previous work (Armbruster et al., 2020) that took into account diffusion, suggested potentially slower rise time dynamics. More importantly, the deconvolved waveforms do not match the shapes of the EPSCs (figures 5 and supp 6-2).What is the aim of the deconvolution? It was not clear from the text, but I assume it shows iGluSnFR binding to glutamate - in which case the slow waveforms are indicative of extrasynaptic iGluSnFR activation.

The deconvolution analysis was mainly used to recover the average responses to stimuli in the train without contamination by previous responses (see also Taschenberger et al. 2016, their figure 6).

We did also try to use the average singular response instead of the exponential fit as a kernel for the (Wiener) deconvolution analysis, which more closely resembled the observed (fast) rise. Unfortunately, this led to markedly worse results, likely because of the noise levels in the measurements. We believe that it would be beneficial to model the rise of the signal more precisely if glutamate imaging data is acquired at higher framerates.

The broad wave forms may be due to extrasynaptic binding of glutamate, but we also note that each frame corresponds to ~10ms and there is only ~10 data points between stimuli, so the responses are unlikely to be as sharp as eEPSCs.

However, I suppose that the more interesting question is whether iGluSnFR could be deconvolved to reveal the underlying release events, similar to how calcium signals can be used to inform about single action potentials.

We agree that it would be particularly interesting to use a "mini iGluSnFR" signal to deconvolve the resulting traces. Unfortunately, we failed to detect iGluSnFR signals reporting individual release events at this time, preventing this kind of analysis.

1. I suggest referencing and discussing (Aggarwal et al., 2022; Srivastava et al., 2022) . These highly relevant papers analyzed iGluSnFR to probe synaptic release.

References:

Aggarwal, A., Liu, R., Chen, Y., Ralowicz, A. J., Bergerson, S. J., Tomaska, F., Hanson, T. L., Hasseman, J. P., Reep, D., Tsegaye, G., Yao, P., Ji, X., Kloos, M., Walpita, D., Patel, R., Mohr, M. A., Tilberg, P. W., Mohar, B., Team, T. G. P., . . . Podgorski, K. (2022). Glutamate indicators with improved activation kinetics and localization for imaging synaptic transmission. bioRxiv, 2022.2002.2013.480251. https://doi.org/10.1101/2022.02.13.480251

Armbruster, M., Dulla, C. G., & Diamond, J. S. (2020). Effects of fluorescent glutamate indicators on neurotransmitter diffusion and uptake. Elife, 9. https://doi.org/10.7554/eLife.54441

Srivastava, P., de Rosenroll, G., Matsumoto, A., Michaels, T., Turple, Z., Jain, V., Sethuramanujam, S., Murphy-Baum, B. L., Yonehara, K., & Awatramani, G. B. (2022). Spatiotemporal properties of glutamate input support direction selectivity in the dendrites of retinal starburst amacrine cells. Elife, 11. https://doi.org/10.7554/eLife.81533

We thank the reviewer for the suggestions. Some of these studies were not available when we first drafted the manuscript. We now added a section discussing these studies starting on line 466:

Optimizing the imaging technique may reduce noise level, while the development of improved GEGIs could improve the signal to a level, at which spontaneous release events can be identified reliably in the cochlear nucleus. In retinal slices, where quantal events have been reliably observed with two-photon imaging, temporal deconvolution was successfully employed to estimate release rates from iGluSnFR signal (Srivastava et al., 2022; James et al., 2019). Subcellular targeting of iGluSnFR variants to the postsynaptic membrane may reduce measurement errors introduced by contributing extrasynaptic iGluSnFR signal and improve spatial resolution of glutamate imaging data(Hao et al., 2023; Aggarwal et al., 2022).

Referees cross-commenting

I also agree with the comments made by other reviewers!

Significance

Overall, this study addresses an important problem in basic neuroscience research. With the developing reliance on optical measurement of neuronal function, it is important to understand the impact of the indicators on physiological function and the limitations of the technique. The study is well-executed and will be informative to neuroscientists performing optical glutamate recording to study single-cell and circuit function in and beyond the auditory system.