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Referee #1

Evidence, reproducibility and clarity

Summary:

In the manuscript "The AMPK-TORC1 signalling axis regulates caffeine-mediated DNA damage checkpoint override and cell cycle effects in fission yeast," the authors studied the role of genes that are potentially involved in the caffeine-mediated override of a cell cycle arrest caused by activation of the DNA damage checkpoint. The methylxanthine substance caffeine has been known to override the DNA damage checkpoint arrest and enhance sensitivity to DNA damaging agents. While caffeine was reported to target the ATM ortholog Rad3, the authors previously reported that caffeine targets TORC1 (Rallis et al, Aging Cell, 2013). Inhibition of TORC1, like caffeine, was also reported to override DNA damage checkpoint signaling. Therefore, in the present study, the authors compared the effects of caffeine and torin1 (a potent inhibitor for TORC1 and TORC2) on cell cycle arrest caused by phleomycin, a DNA damaging agent, using various gene deletion S. pombe mutants.

The authors concluded that they identified a novel role of Ssp1 (calcium/calmodulin-dependent protein kinase) and Ssp2 (catalytic subunit of AMP-activated kinase) in the cell cycle effects caused by caffeine, based on the following findings; (1) the caffeine-mediated DNA damage checkpoint override requires Ssp1 and Ssp2; (2) Ssp1 and Ssp2 are required for caffeine-induced hypersensitivity against phleomycin; (3) under normal growth conditions, caffeine leads to a sustained increase of the septation index in a Ssp2-dependent manner; (4) Caffeine activates Ssp2 and partially inhibits TORC1.

Major comments:

I do not think that many of the authors' claims are supported by the results of the present study. The corresponding parts are detailed below.

1. The conclusion of the first paragraph in the Results (top in page 6; Our findings indicate that caffeine and torin1 indirectly and directly inhibit TORC1 activity respectively.) is not supported by the data in Figure 1. The result that caffeine, but not torin1, requires Ssp1 and Ssp2 to override the phleomycin-induced cell cycle arrest does not necessarily indicate that caffeine indirectly inhibits TORC1 via Ssp1 and Ssp2. Rather, the authors should mention that this conclusion is based on the authors' previous reports by citing them (e.g., Rallis et al, Sci Rep, 2017).

To add to Figure 1, an additional experiment using a constitutively active AMPK mutant, a temperature-sensitive TORC1 mutant, and a srk1 deletion mutant will help the authors claim their original conclusion as one possibility.<br /> 2. The conclusion of the second paragraph in the Results (lower-middle in page 6; Our results indicate that caffeine induces the activation of Ssp2.) is not based on the results of Figure 2. Figure 2 simply illustrates that both caffeine and torin1 cause hypersensitivity to phleomycin dependent on Ssp1 and Ssp2.<br /> 3. The conclusion of the fourth paragraph in the Results (middle in page 7) is not clearly supported by the result, due to an insufficient data analysis. As the cell length and the progress through mitosis are the key assay parameters in Figure 3, the average cell length should be shown next to each micrograph of Figure 3A and 3B. In Figure 3C, a mitotic index and the average cell length should be shown next to each micrograph. A statistical analysis is necessary for the authors to compare the measurements and to claim as the headline (Caffeine exacerbates the ssp1D phenotype under environmental stress conditions), as the effect of caffeine was not evident.<br /> 4. In the middle of page 8, the statement "Accordingly, the effect of caffeine and torin1 on DNA damage sensitivity was attenuated in gsk3D mutants (Figure 5C and 5D)." is not supported by the corresponding results. Rather, Figure 5C and 5D look almost same.<br /> 5. The description and the conclusion of the last paragraph in the Results (bottom in page 8 - page 9) are not supported by the results of Figure 6, due to an insufficient data analysis. The extent of phosphorylation must be quantified as a ratio of the phosphorylated species (e.g., pSsp2) to all species of the protein (e.g., Ssp2).

From Figure 6, the authors claim that caffeine (10 mM) partially inhibits TORC1 signaling. However, the authors previously showed that the same concentration of caffeine inhibited phosphorylation of ribosome S6 kinase as strongly as rapamycin, the potent TOR inhibitor (Rallis et al, Aging Cell, 2013). The authors are advised to assess phosphorylation of S6 kinase again in the present study and compare to the results of the present results in Figure 6, because addition of that data may allow the authors to discuss that caffeine affects TORC1 downstream pathways at different intensities.

Also, immunoblotting of the same proteins looks somehow different from panel to panel (e.g., pSsp2 in panel A and D; Actin in panel A, C, and D). Therefore, the blotting result before clipping had better be shown as a supplementary material.

Minor comments:

1. (Figure 1) The septation index of the phleomycin-treated cells (without any further additional drugs) should be shown, as a baseline.
2. (Figure 1D, Optional) As a ppk18D cek1D double deletion mutant is reported, the authors are advised to add and test that mutant in this experiment.
3. (Figure 2) The authors need to clarify the number of cell bodies spotted (e.g., in the Figure legend).
4. (Figure 3) The different number of cells in micrographs may give an (wrong) impression on the cell proliferation rate. Therefore, it is advisable to use the micrographs in which the similar number of cells are shown for conditions with the similar cell proliferation rates.
5. (Figure 4B) ssp2D, not spp2D.
6. (Figure 4) The septation index of the none-treated cells should be shown as a baseline.
7. (Figure 6B, 6E) What do the black arrows indicate? Figure Legend does not seem to explain them.
8. (Figure 6C) Indicate which part of the Maf1-PK blot corresponds to the phosphorylated species, because Maf1-PK is probed with an anti-V5 (not a phosphorylation-specific) antibody.
9. (Figure 6D) gsk3Dssp1D, not gs3Dssp1D.

Significance

As caffeine is implicated in protective effects against diseases including cancer and improved responses to clinical therapies, the topic of the present study is of interest and importance to the broad audience.

In the present study, the most significant finding is that caffeine- and torin1-induced hypersensitivity to phleomycin is dependent on Ssp1 and Ssp2 (Figure 2). This result may be important in chemotherapy against cancers. On the other hand, caffeine is known to activate AMPK (e.g., Jensen Am J Physiol Endocrinol, 2007). Besides, as detailed in the Major comments, many of the major conclusions are not supported by the present results. Therefore, based on my field of expertise (cell cycle, cell proliferation, and TOR signaling), I conclude that the present study hardly extends the knowledge in the field of "the cell biology of caffeine."

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Referee #3

Evidence, reproducibility and clarity

Summary

Cheng et al. use single-cell sequencing to determine how Nodal signaling influences endodermal and prechordal plate fate specification in zebrafish. Much data and data analyses are presented, but the conclusions that can be drawn remain vague and do not go far beyond what previous studies have already established. While the datasets are a potentially useful resource, the conceptual impact is limited.

Major comments

1. The major weakness of the paper is that previous studies have already shown that differential Nodal signaling (and additional mechanisms) can induce anterior endoderm versus prechordal plate. In particular, the studies of Barone et al. (2017) and Sako et al. (2016) have provided much more convincing insights, because they combine genetic manipulations with in vivo imaging. In contrast, the current study mostly infers fate specification from scRNA-seq data. This approach is fraught with artifacts, because pseudotime trajectories are only a proxy for developmental processes, and UMAPs can misrepresent relationships between different cell states and types. The potentially more novel findings (roles for ripply; role of chromatin accessibility) are quite preliminary. Therefore, the conceptual advances provided by the study are minor.
2. The study attempts to distinguish between anterior endoderm and prechordal plate, but there is little evidence that anterior endoderm versus most/all endoderm is studied. Clear markers for anterior endoderm would be needed (or live imaging as in Barone et al.).
3. The claim that prechordal plate gives rise to prechordal plate and endoderm is confusing. The initial prechordal plate is different from the later prechordal plate. Please use a more precise nomenclature.
4. Gsc is described to be expressed highly in anterior endoderm progenitors but Figures 1C and 1J do not support this.
5. I am not sure what to make of the Nodal and Lefty manipulations. There is plenty of data but previous studies by the Heisenberg lab have provided much more definitive insihgts into the role Nodal signaling in this fate decision. Please put your results into the context of these studies.
6. The chromatin accessibility results and conclusions seem trivial in light on previous observations that Nodal signaling (and many other signaling pathways) activate gene expression via enhancers, a hallmark of which is increased accessibility upon activation.
7. The ripply1 overexpression result is potentially interesting, but needs to be complemented with a loss of function analysis.

Referee cross-commenting

It is gratifying to see that all three reviewers appreciate the potential of the data, but they find the results not as conclusive as one might wish, and they question the conceptual novelty of the claims when compared to previous studies. I share their suggestions and concerns.

Significance

The study provides new single-cell data and analyses but does not provide major conceptual advances when compared to previous studies (e.g. Barone et al. (2017); Sako et al. (2016)). In its current form a small group of researchers in the zebrafish Nodal field might be interested in further exploring the data in this paper and combine it with in situ gene expression analyses and fate mapping.

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Referee #2

Evidence, reproducibility and clarity

In this study, Chen and colleagues examine the molecular basis for the segregation of mesodermal and endodermal fates during zebrafish gastrulation. For this, they focused on cell fate separation within the anterior mesendoderm, which gives rise to prechordal plate (pp) and anterior endoderm (endo) progenitors. Using a combination of "-omics" approaches and live imaging in both embryos and explants, the authors find that endo progenitors derive from the pp and are specified by comparatively lower levels of Nodal signaling. Mechanistically, higher Nodal signaling levels in pp cells correlates with chromatin openness. Furthermore, the authors provided evidence that gsc and ripply1 activity can repress endo specification. Overall, the authors suggest a model whereby different Nodal signaling levels promote cell fate diversification through modulation of epigenetic states.

The paper is well written, and the data presented in this study nicely supports the author's interpretation that anterior endo cells derive from the pp and that it requires lower Nodal signaling levels. However, it is unclear what are the core differences between this model and previous work (Sako, et al. 2016; Barone, et al. 2017) and how to interpret these findings in light of recent work in the field, implicating FGF signaling as a critical regulator of the segregation between mesoderm and endoderm in zebrafish (Economou et al. 2023). To reinforce their findings, it would thus be important for the authors to use their datasets to investigate further between these distinct models and explore the role of FGF signaling in this process. For instance, can they observe differential activation of FGF targets in early progenitors cells with higher vs. lower Nodal signaling?

Similarly, the link between Nodal signaling and chromatin openness is interesting, however, it is still unclear how causative these differences are for the cell fate segregation investigated in this study (this is in line with the way the authors describe these findings). However, given my previous point, I think it would be important to dissect this link further to strengthen the novelty of the study.

Finally, to prove that gsc and ripply1 cooperate in wild-type embryos for the segregation between pp and endo progenitors, it would be important to include further functional data. For instance, describe the respective loss-of-function phenotypes, as well as whether, at endogenous levels, they can partially compensate for each other's loss-of-function. A similar analysis should be included for osr1 to validate the need for cooperation between these distinct transcriptional repressors in anterior endo specification (a hypothesis nicely raised by the authors in the discussion of this study). Finally, is the expression of these transcriptional repressors restricted to the ppl? If so, why? Would they require peak levels of Nodal signaling, only present in the pp, for their induction? What are the expression levels of these regulators in the morphants for ndr1 and lefty1 (which show differences in Nodal signaling levels)?

Significance

This study tackles an important question in vertebrate gastrulation, which has been under intense investigation over the last years. By integrating sequencing datasets from previously published studies, as well as newly-generated datasets, the authors provide evidence that anterior endo progenitors derive from the pp, which is nicely confirmed using live imaging. The findings that anterior endo progenitors are specified by comparatively lower levels of Nodal signaling than pp constitutes a major part of this manuscript. However, it is not clear i) what is necessarily new compared to previous studies implicating Nodal signalling in this process and, ii) how to interpret these findings in the light of recent work in the field disputing this more Nodal-based model. Accordingly, it was previously shown that the duration of Nodal signaling, partially through the action of gsc, played a key role in the differentiation between pp and endo progenitors (Sako, et al. 2016). Furthermore, previous work showed that endo cells leaving the ppl showed shorter-lived cell-cell contacts and, thus, on average lower Nodal signaling (Barone, et al. 2017). Since a recent model challenged the idea that differences in Nodal signaling are sufficient to account for the segregation between mesoderm and endoderm progenitors and instead suggested that an interplay between Nodal and FGF is necessary for the stochastic switch between these two cell fates (Economou et al. 2023), it would be important for the authors to use their datasets to investigate further these distinct models. This would synthetize both previous and current findings into a conceptual framework explaining how endoderm progenitors are specified.

Audience: This study would be relevant for a broad audience of cell and developmental biologists, interested in morphogen signaling, cell fate specification and pattern formation.

Expertise in zebrafish development, gastrulation, morphogen signaling and morphogenesis.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In zebrafish embryos, progenitor cells for both the prechordal plate and anterior endoderm reside at the dorsal margin in early gastrulation. Both cell populations are induced via signaling through the Nodal signaling pathway, however the mechanisms that send Nodal-exposed cells to one fate versus the other remain a matter of debate. Cheng et al use single-cell RNA sequencing to investigate the mechanistic origins of this developmental decision. They argue that both populations emerge from a common progenitor pool marked by the prechordal-plate marker gene goosecoid (gsc). By adding single-cell ATACseq analysis, they go on to argue that Nodal signaling encourages open chromatin states at target genes, and that this may underly the distinction between prechordal plate and endodermal fates. Finally, they suggest two potential regulators (gsc and ripply1) that may repress commitment to the endodermal fate.

Major Comments:

1. In lines 128-136, the authors describe a live imaging experiment to support the argument that anterior endodermal cells emerge from a gsc+ progenitor pool. The claim is that sox17+ cells (marked by RFP fluorescence) arise in gsc+ cells (marked by GFP fluorescence). From the presented data, I find it very hard to evaluate this claim. The GFP signal appears quite close to background in the highlighted cell. Additionally, the argument- as presented-turns on the behavior of a single highlighted cell. I think that this analysis should be clarified and extended to support the claim.

I suggest that the authors (1) plot average cell fluorescence over time rather than a 'line scan' across the cell, (2) draw cell borders from the mask used in each frame for clarity of presentation, and (3) plot the trajectories of gsc+/sox17+, gsc-/sox17- and gsc+/sox17-cells for comparison.

Alternatively, it could be helpful to extract fluorescence intensities for each cell in the field of view and scatter the RFP vs. GFP intensity for each cell. If the claim is true, three distinct subpopulations should be visible (i.e. gsc+/sox17-, gsc-/sox17- and gsc+/sox17+). Statistical analysis supporting the significance of these differences (e.g. comparing the means of each reporter within the populations) would be clarifying.

OPTIONAL: The live imaging experiment the authors present is quite ambitious, but perhaps overly difficult for the task at hand. I think this point could be more easily and clearly demonstrated by using two-color fluorescent in situs or HCR staining for gsc and sox17. Using an endpoint measurement would allow for deeper sampling across multiple embryos, and would likely yield clearer signals for cell type quantifications.<br /> 2. In the same section, I suggest that the authors address the possibility that the sox17+ cells observed don't go on to become part of the anterior endoderm. I commend the authors experimental work to support their scRNA-Seq data, however observation of the expression of a reporter gene (injected on a plasmid) is not equivalent to demonstrating that those cells adopt a given fate in the end. Is it not possible that the sox17 expression is transient, and these cells revert to prechordal plate fate? This point would be sealed by a formal fate mapping study (e.g. photoconversion of sox17::kaede cells), but I don't think this is a necessary bar for publication.<br /> 3. In Figure 1 M, the explant data does not seem to clearly support the claim that higher Nodal signaling intensities favor prechordal plate over endoderm. It appears that, for the endodermal panel, 2/3 replicates for 6 pg and 10 pg injections resulted in no endodermal cells observed. Could the authors clarify how this reflects the certainty of the conclusion? No statistical analysis is indicated on this panel or the one below.<br /> 4. OPTIONAL: The analysis presented in Fig. 1M strikes me as rather indirect (i.e. deconvolution of bulk RNA-Seq data to infer cell population proportions), and not strongly compelling. I think a stronger support of this point would be to inject Nodal into embryos and measure positive cell counts for gsc and an endodermal marker (e.g. sox32 or sox17) via HCR or in situ hybridization. This would yield a direct measurement of the cell counts in question. I think this would greatly support the claim, but I don't think should be considered a requirement for publication.<br /> 5. In Fig. 2H, the authors analyze responses to ectopic Nodal gradients in order to corroborate the results of their LIANA analysis. This experiment is a welcome addition to the argument, but has weak points that should be addressed.<br /> - a. The description of image analysis procedures used to construct the quantification plots are inadequate. It seems likely that the nuclei were segmented from the DAPI images, but this was not clear from the methods section. The authors should completely describe the segmentation pipeline and include sample code in the supplementary material.<br /> - b. The methods section seems to suggest that the analysis was performed exclusively on maximum intensity projections. I think this procedure may make the data hard to interpret and should be modified/support with additional analysis. For example, there is no reason that, at any given position in the image, the brightest DAPI and pSmad2 channel pixels occur in the same plane. Segmentation boundaries may therefore not reliably match between channels in the maximum intensity projection. The segmentation should be performed using the full Z-stack images. This can be done using widely-available software packages (e.g. CellProfiler).<br /> - c. The fluorescence images in 2H (specifically for the pSmad2 channel) look like they may contain some artifacts that carry through into the quantification. Specifically, there appears to be substantial non-specific background (both hazy and punctate) in the lft1 mutant that may artificially elevate the quantified intensity. This is evident in the quantification as a larger 'offset' to which the gradient decays than in the other presented images. This may be another explanation for the observation that pSmad2 staining is stronger in this background. I suggest that the authors (a) present all fluorescence images from the dataset in the supplement to allow for visual inspection, and (b) estimate the effect of fluorescence background on their quantifications to ensure that this artifact is not the source of the claimed difference.<br /> 6. In lines 267-284 and Fig. 4 L, the authors make the argument that ripply1 acts as a cell-autonomous repressor of endodermal fate. I find the argument for the cell autonomous character of its function hard to follow. Specifically, the authors lean on the experiment in which a plasmid with a sox17 promoter-ripply1 construct is injected, resulting in a decrease in endodermal cell count. Could the authors elaborate on how this proves a cell autonomous effect? Is it not possible that ripply1 expressed from this construct induces a signal that influences neighboring cells?<br /> 7. The suggestion that prechordal plate fate is favored (over endodermal fate) by higher Nodal signaling levels is interesting. This claim is supported by the derivation of a 'Nodal score' from RNAseq data. However, I don't see where the score is defined in the Methods section or in the supplementary materials. If this was accidentally omitted (my apologies if I am just missing it), it should be added. Additionally, I found the description in the main text to be opaque, and the paper would benefit from a more intuitive/friendly explanation of this metric.

Additionally, could the authors comment on what they believe-in terms of Nodal signaling history for a given cell- this score represents? Does it correlate with integrated Nodal exposure? Nodal exposure duration? Peak Nodal exposure? Given the results of Sako et al-that Nodal exposure duration is a critical determinant of prechordal plate fate- it would be useful to know if the authors believe their Nodal score findings point toward a different mechanism.

Minor Comments:

1. Line 84: The authors refer to the prechordal plate cells being 'more mature' than endoderm. It is unclear what the claim is here; some elaboration would be helpful.
2. The fluorescence images in Fig. S2 are virtually invisible in the PDF. The images should be rescaled to make them visible.
3. Fig. 2H would be easier to make sense of if the image panels were labeled. Please indicate which color corresponds to which stain.

Significance

I believe that this study fills in some details on the process of anterior endoderm specification that will be of interest to specialists in zebrafish Nodal signaling. I believe that the strongest and most novel section is the combined scRNA-Seq/ATAC-Seq analysis. This dataset is likely to be of interest to researchers who want to dig into potential mechanisms for the separation anterior endoderm and prechordal plate. Further, the singling out of ripply1 as a potential regulator of endodermal specification is interesting, and I hope that the authors follow this promising lead in future work.

While this study does provide a useful single-cell view of the specification of anterior endoderm, I didn't feel that it came to a concrete conclusion about the mechanism of separation of the anterior endoderm and prechordal plate. A few interesting processes/players are suggested by the findings- for example, Nodal/Lefty signaling between the populations or ripply1 expression could tip the balance- but I don't believe these hypotheses were tested clearly. The authors correctly point out that models for Nodal-driven endoderm/mesoderm separation have recently emerged in the literature, however the findings presented here don't rule out either of these models or compellingly support an alternative. I don't believe that this should preclude publication, however I do think it will limit the reach of the paper. Experiments that more concretely test the possible mechanisms hinted at here- for example, studying the separation of the two lineages in ripply1 mutants- would strengthen the paper's reach.

My enthusiasm for the paper is also somewhat reduced by the fact that some key findings of the paper can be found in earlier work. Acknowledgement of this prior work in the relevant sections could be improved. Specifically:

1. The finding that anterior endoderm cells emerge from a gsc-expressing population in the dorsal margin was strongly suggested in the classic Warga et al paper on the origin of zebrafish endoderm. There, fate mapping experiments demonstrate that dorsal marginal cells (in the first two cell tiers) in the late blastula can go on to form both endoderm and mesoderm. This strongly implies that anterior endoderm cells emerge from a gsc+ population, given that these cells are firmly within the gsc expression domain. I also note that the scRNAseq data from Fig. 2 in Farrell et al directly demonstrates that some sox17+ endoderm cells express gsc in their developmental trajectory. The findings in this paper are a welcome confirmation of these earlier observations, however this context should be discussed.
2. The observation that squint and lefty single mutants (either lefty1 or lefty2) can alter the propensity to adopt endodermal or mesodermal fates has also been observed previously. See for example Fig.1 in Norris et al, Figs 3 and 4 in Rogers et al, or Fig.1 in Chen et al. Acknowledging some of these earlier findings would benefit the paper.

As a reviewer, I feel most qualified to comment on the embryological aspects of the presented work. While I am generally familiar with the single-cell genomics toolkit, I am not in a position to rigorously assess the technical merit of that side of this work. Accordingly, I have tried to restrict my comments to the embryology side.

References:

1. Warga, R.M. and Nüsslein-Volhard, C., 1999. Origin and development of the zebrafish endoderm. Development, 126(4), pp.827-838.
2. Farrell, J.A., Wang, Y., Riesenfeld, S.J., Shekhar, K., Regev, A. and Schier, A.F., 2018. Single-cell reconstruction of developmental trajectories during zebrafish embryogenesis. Science, 360(6392), p.eaar3131.
3. Norris, M.L., Pauli, A., Gagnon, J.A., Lord, N.D., Rogers, K.W., Mosimann, C., Zon, L.I. and Schier, A.F., 2017. Toddler signaling regulates mesodermal cell migration downstream of Nodal signaling. Elife, 6, p.e22626.
4. Rogers, K.W., Lord, N.D., Gagnon, J.A., Pauli, A., Zimmerman, S., Aksel, D.C., Reyon, D., Tsai, S.Q., Joung, J.K. and Schier, A.F., 2017. Nodal patterning without Lefty inhibitory feedback is functional but fragile. Elife, 6, p.e28785.
5. Chen, Y. and Schier, A.F., 2002. Lefty proteins are long-range inhibitors of squint-mediated nodal signaling. Current Biology, 12(24), pp.2124-2128.
6. Sako, K., Pradhan, S.J., Barone, V., Ingles-Prieto, A., Müller, P., Ruprecht, V., Čapek, D., Galande, S., Janovjak, H. and Heisenberg, C.P., 2016. Optogenetic control of nodal signaling reveals a temporal pattern of nodal signaling regulating cell fate specification during gastrulation. Cell reports, 16(3), pp.866-877.

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Reply to the reviewers

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

Summary: In this manuscript by Berg et al the authors demonstrate that RNA polymerase activity is important for the formation of nuclear blebs. This is an interesting and significant finding because prior work has suggested nuclear bleb formation is a result of changes in nuclear rigidity (lamins) or chromatin (via histone modifications). Overall I thought the manuscript was quite interesting and the data well presented. I think the inclusion of multiple mechanisms of blebbing (VPA treatment, as well as lamin B KO) helps to further support the importance of RNA polymerase/transcription activity in the blebbing process. However, I do have some concerns regarding the conclusions of the data that I think should be addressed as a revision.__

We appreciate that Reviewer states that “the manuscript was quite interesting and the data well presented”, it is a “significant advancement”, and “the first report of this phenomena, and thus will be impactful to the nuclear mechanics field.”

In the points below, the Reviewer specifically suggests that we: 1) clarify possible contributions from RNA pol III, 2) address how global vs. local chromatin motion might contribute to our findings, and 3) discuss the force production capabilities of RNA pol II. We also appreciate the feedback regarding the conclusions and have made the specific changes requested in the revision.

Major Comments:____ 1. One concern I have is that the alpha-amanitin inhibitor has been shown to also inhibit RNA polymerase III. In an old study (1974 Weinmann PNAS) it appears that the inhibitor starting at 1 to 10 ug/ml. In this study the authors are using 10 uM alpha-amanitin, which is ~ 9 ug/ml and within the range of inhibiting some RNA polymerase III. Additionally, the other drug (actinomycin D) is even less specific for RNA polymerase II. I would suggest that the authors consider one of the following approaches 1) acknowledge in the manuscript the potential for RNA polymerase III to be important in the blebbing process 2) try a 10-fold lower dose of alpha-amanitin and see if that also inhibits blebbing, 3) try to find a way to demonstrate that RNA polymerase III activity is not inhibited at the 10 uM alpha-amanitin dosage, or 4) consider an alternate method to perturb RNA polymerase II activity (see Zhang Science Advances 2021 for an auxin-based approach to downregulate RNA polymerase II).

The Reviewer raises the point that alpha-amanitin inhibits both RNA pol II and III. In the revised manuscript, we provide new data to further support that the observed effects arise from RNA pol II. We now include new data from cells treated with the transcription inhibitors flavopiridol (which inhibits RNA pol II elongation) and triptolide (which inhibits RNA pol I and II initiation). These transcription inhibitors also suppress nuclear blebbing in VPA-treated nuclei (Figure 2C) as well as three other nuclear blebbing perturbations in chromatin and lamins (Supplemental Figure 1A). These new experiments directly show that nuclear bleb suppression by transcription inhibitors can be observed without possible inhibition of RNA pol III by alpha-amanitin.

__ A second concern I have is that the inhibition of RNA polymerase is global. Thus it is difficult to know for sure the biophysical function of the polymerase occurs immediately at the bleb, or instead is somehow affecting the overall chromatin state throughout the entire nucleus. I agree that figure 3 does provide some evidence that major mechanical and biophysical properties of the nuclei are not changed in response to the inhibition of the polymerase. However, micromanipulation experiments are done with isolated nuclei, which may be somehow mechanically altered already by isolation from cells. I feel that there still must be given some consideration in the discussion of the possibility that RNA polymerase activity outside of the bleb may be having some role in the stabilization of the chromatin and blebbing propensity.__

We appreciate the Reviewer’s insightful comments and we have revised the manuscript to clarify that we do not attribute blebbing purely to local effects. Instead, we argue that global changes in chromatin motion driven by transcription could contribute to nuclear blebs.

We did not intend to communicate that alterations to chromatin or its dynamics were necessarily only local. Indeed, we found that relative levels in RNAP Ser2 and Ser5 phosphorylation were different inside the blebs (Figure 6). Nonetheless, transcription was perturbed globally in our experiments, so we realized that blebbing could be driven by global changes (Figure 1). We hypothesize that global regulation of transcription can stimulate nuclear blebbing since transcription and its inhibition can, respectively, drive and suppress correlated chromatin motion throughout the entire nucleus (as previously observed by Zidovska et al. (PNAS 2013) and Shaban et al. (NAR 2018, Genome Biol. 2020), among others). We have revised the manuscript to clarify this point (Discussion section, page 15). We have also added new simulation snapshots showing global chromatin motions and how these motions are coupled to nuclear morphology (Figure 7C).

In response to the concern that isolated nuclei exhibit different mechanical properties than nuclei inside of cells, we refer to our previously published micromanipulation measurements (Stephens et al. MBoC 2017). There, we found that nuclei within the cell and outside of the cell have quantitatively similar spring constants and qualitatively similar force-extension curves. Therefore, we are confident that the lack of change in nuclear stiffness measured by micromanipulation accurately reflects the mechanics of nuclei inside of cells across different perturbations.

__ While I lack expertise to evaluate the basis of the model, I appreciate the model can show that motor activity can influence bulge. But it is not clear in the manuscript that RNA polymerase can generate these kinds of forces. The Liu citation is a model, and does not provide direct evidence that the RNA polymerase can generate force, or forces large enough to be meaningful. To me the model in this paper (Figure 7) felt as if it was only a possible hypothesis of why the RNA polymerase has an effect on blebbing, but I imagine there could be other hypotheses that would cause the same effect. The authors state (in the abstract) that RNA pol II can generate active forces, but I am concerned this is not sufficiently established. Since this motor/force activity of RNA polymerase is not experimentally demonstrated in this paper the authors should either do a better job of including evidence of this from the literature or consider removing this part of the manuscript.__

RNA polymerase is capable of exerting forces in excess of 10 pN (e.g., see Wang et al. Science 1998; Herbert et al., Annu Rev Biochem 2008). The collective activity of many motors (10’s of thousands, e.g., see Zhao et al. Proc. Natl. Acad. Sci. 2014) may generate even larger forces. As discussed in our earlier modeling paper, this force scale is consistent with the motor strengths studied in our simulations (Liu et al. Phys. Rev. Lett. 2021); in the present work, we present simulation results for motors that generate 0.14 pN forces. Thus, transcription, in principle, could generate forces even larger than the ones we considered in the model.

Additional experiments indicate that at larger length scales, RNA polymerase activity appears to drive coherent motions of chromatin throughout the cell nucleus (Zidovska et al. PNAS 2013; Shaban et al. NAR 2018; Shaban et al. Genome Biol 2020). It is these motions, driven by motors, that appear to drive the formation of nuclear bulges in our model (please see new panel Figure 7C).

Therefore, the aim of the model is to build on established and new results to better understand how transcription could alter nuclear morphology. Our model is adapted from earlier models, which could reproduce observations of chromatin-based nuclear rigidity, (Stephens et al. MBoC 2017, Banigan et al. Biophys J 2017, Strom et al. eLife 2021), some aspects of nuclear morphology (Banigan et al. Biophys J 2017, Lionetti et al. Biophys J 2020), and possibly explain how nonequilibrium motor activity (such as RNA pol II) can drive coherent chromatin dynamics (Liu et al. PRL 2021), which have been observed in live-cell imaging experiments (e.g., Zidovska et al. PNAS 2013; Shaban et al. NAR 2018; Shaban et al. Genome Biol. 2020, among others). The precise form of the motor activity is not the focus of our model (or the previous motor model in Liu et al. PRL 2021). Instead, our simulation result indicates that the relatively small motor forces that generate coherent chromatin dynamics could explain the surprising observation that transcription is a critical component of nuclear blebbing.

To address the Reviewer’s comment, we have added additional text to the Introduction and the Results sections to support the inclusion of motors to model the possible effects of transcription on chromatin dynamics and nuclear shape.

In the Introduction (page 4), we now write:

Simulations suggest that chromatin connectivity combined with the forces generated by polymerase motor activity (~10 pN per polymerase (Herbert et al. 2008)) could generate these dynamics (Liu et al., 2021).

In the Results section (page 10), we write:

We consider motors that generate sub-pN forces, well below the 10 pN forces that may be generated by individual RNA polymerases (Herbert et al. 2008).

Additionally, we have updated Table 1 to include the simulated motor strength.__ __

__ Minor Comments: 1. Did the authors do any analysis to see if the increased RNA transcription with VPA treatment (Figure 1B) has any spatial relationship to where the bleb occurs? Could an analysis of this be done similar to Figure 6 (with a bleb/body ratio)?__

The Reviewer raises an interesting point about measuring RNA localization relative to the bleb. We measured RNA intensity in the bleb and the nuclear body for wild type cells only. We find that RNA levels are significantly decreased in the bleb (80% of body signal, p

__ Is there anything known about lamin B1 KO cells as to whether or not they have increased transcription? Or could the authors do an analysis like they did with VPA treatment to check this?____ If they were to have increased transcription this would further support the authors' proposed mechanism of transcription itself (or RNA polymerase activity) driving blebbing).__

In the revised manuscript, we show that several nuclear perturbations that are known to decrease nuclear stiffness and cause increased nuclear blebbing also rely on active transcription. Lamin B1 knockout or knockdown cells have been shown to result in changes in transcription. However, it was difficult to find data that shows whether the overall level of transcription changes. Collaborators of ours have unpublished data that indicates that twice as many genes are upregulated as downregulated upon lamin B1 knockdown, but this still does not assess the total level of transcription within the nucleus. Alternatively, increasing transcription via other means is fraught with off-target effects, which would require many additional complementary experiments. We thank the Reviewer for this interesting suggestion, but we believe this is beyond the scope of this manuscript, in which we have focused on showing that transcription inhibition suppresses bleb formation.

__ Figure 1D, the VPA ser2 image appears much brighter than the untreated image. Yet the graph shows they are similar. Perhaps a more representative image should be used?__

The image used reflects the data that Ser2 signal is brighter (by ~10%) in VPA-treated cells but is not significantly altered compared to wild type (unt), and thus it is an accurate reflection of the data.

__ Can the authors comment if there is less DNA at the bleb site? In Figure 6 A this appears to be the case (based on the VPA image). If true, is the alpha-amanitin treatment rescuing this such that there is more DNA at the bleb (maybe causing the bleb to be smaller?).__

We find that there is less DNA signal intensity per unit area in the nuclear bleb as compared to the nuclear body (bleb has ~60% the signal of the body; see teal dots/data in Figure 6B). This agrees with previously published work from our lab (Stephens et al. 2018 MBoC).

Alpha-amanitin treatment does not rescue this effect. Decreased DNA enrichment in the bleb remains with alpha-amanitin treatment (p > 0.05, comparing across all 4 conditions in Figure 6B).

__ What is the significance of bleb vs non-bleb nuclear rupture? Is there anything known in the literature as to how these ruptures may be different in terms of biophysics, impact to DNA, repair? It would be helpful to have some context, as well as to understand if non-bleb rupture is something that may have been previously missed in other contexts.__

The Reviewer asks a valid and interesting question that this manuscript only begins to address. In general, we believe that ruptures occurring with blebs vs. without blebs may reflect aspects of the underlying mechanism(s) of blebbing and rupture, in the presence or absence of transcription. We offer a few further thoughts below.

1) Non-bleb nuclear ruptures have been reported in a few papers by our group (Stephens et al., 2019 MBoC) and others (Chen et al., 2018 PNAS), but much is still unknown.

2) Non-bleb nuclear rupture is part of normal nuclear behavior, as it accounts for ~20% of nuclear ruptures in wild type and perturbed cells (VPA and LMNB1-/-).

3) Overall, we think that bleb-based and non-bleb-based ruptures may occur through different mechanisms. The simplest difference is that bleb-based nuclear ruptures follow the nucleus’ ability to form blebs, whereas non-bleb-based nuclear rupture occurs in cases where there is less bleb formation, suggesting that factors other than the ability to form blebs may also be important for rupture. In the current study, we observed that bleb-based nuclear ruptures (and bleb formation) require transcription. In another manuscript from our lab under review, bleb-based nuclear ruptures (and nuclear blebbing) can be suppressed by actin contraction inhibition and increased by increased actin contraction (Pho et al., biorxiv 2022).

Additionally, we note it was reported that non-bleb-based nuclear ruptures, at least some of which are driven by microtubule prodding, result in increased levels of DNA damage (Earle et al. Nat Mater 2020), as has been observed for bleb-based ruptures (Stephens et al., 2019 MBoC; Xia et al. J Cell Bio 2018). Thus, nuclear rupture in general is thought to lead to DNA damage. However, total levels of DNA damage due to rupture may be controlled by different cellular processes.

In the revision, we have clarified our motivation for quantifying ruptures with and without blebs. We have also added a few remarks, drawn from the above comments, to the Discussion section (pages 11-14).

Reviewer #1 (Significance (Required)):____ General assessment: This study is a careful analysis of how RNA polymerase inhibition reduces nuclear blebbing. The study demonstrates this very well, using a variety of approaches. However, some limitations are the overstatement of some conclusions (specifically that it is RNA polymerase II when the inhibitor may also affect RNA polymerase III; that the RNA polymerase activity is important at the bleb and involves motor activity). Advance: This paper is a significant advancement because it shows the role of transcription in the biophysics of the nuclear shape. To my knowledge this is the first report of this phenomena, and thus will be impactful to the nuclear mechanics field. Audience: I think the findings are of broad interest, including beyond the nuclear mechanics field. I think the audience would be the entire cell biology community. Expertise: My expertise is in cell mechanics, including forces at the the nuclear LINC complex. While I do not work in the field of nuclear blebbing and rupture, I follow this field quite closely.

We greatly appreciate the Reviewer’s statement that “To my knowledge this is the first report of this phenomena, and thus will be impactful to the nuclear mechanics field.__” __We thank the Reviewer for their thoughtful comments and suggestions, which have helped to improve the manuscript. __

__

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

The authors present data supporting the potential involvement of active transcription in the formation of nuclear blebs when the global deacetylase inhibitor valproic acid (VPA) has been applied to cells

Reviewer #2’s greatest concern throughout the review was that we focused on the use of VPA as a model for generating increased nuclear blebbing and 24-hour treatment with alpha-amanitin as a transcription inhibitor. In the revised manuscript, we provide new data to show that nuclear blebbing generated by a variety of different nuclear perturbations (VPA, DZNep, LMNB1-/-, and LA KD Figure 2D __and __Supplemental Figure 1A) is reliant on active transcription in two different cell lines (MEF and HT1080, Figure 2 A and B). This is supported by use of four different transcription inhibition drugs, which work over varying time periods (24 hrs in alpha-amanitin, triptolide, or flavopiridol; actinomycin D for 1.5 hrs Figure 2C). We also timelapse imaged during drug treatment to show that transcription inhibitors for which we used 24-hour incubation times, can suppress nuclear blebs within 8 hours (Supplemental Figure 1B). __We also show that nuclear bleb formation and stability in wild type is transcription dependent (__Figure 5). We believe the new data added in our revised manuscript addresses the concerns of the Reviewer that the findings were specific to VPA and alpha-amanitin together only.

__Reviewer #2 (Significance (Required)):____

The authors present data supporting the potential involvement of active transcription in the formation of nuclear blebs when the global deacetylase inhibitor valproic acid (VPA) has been applied to cells. __

While somewhat interesting, this is a rather specific condition that is further restricted by the limited use of experimental approaches. For example, the only deacetylase inhibitor used is VPA. Is this because VPA is the only one to trigger the effect? The authors should expand their approach to include additional inhibitors or, preferably, a directed knockdown tactic that targets the specific HDACs driving their phenomena.

The Reviewer is concerned that we have used limited experimental approaches by focusing on VPA treatment to induce nuclear blebs and alpha-amanitin overnight treatment to suppress nuclear blebbing. VPA treatment is a well-established perturbation to induce nuclear blebbing via HDAC inhibition, and it is similar to a variety of other nuclear perturbations that also induce blebs (Stephens et al. MBoC 2018, 2019; Kalinin et al. MBoC 2021; Pho et al. biorxiv 2022).

Nonetheless, to clearly address the Reviewer’s concerns we have provided new data which shows that four different nuclear perturbations are suppressed by transcription inhibition and that four different transcription inhibitors suppress nuclear blebbing. In addition to these perturbations, we also note that transcription inhibition affects bleb formation and stability in wild type cells. Below we outline the diverse experimental approaches that support the major conclusion of our manuscript.

Our data shows that transcription inhibition suppresses nuclear blebbing through data for:

1. Multiple cell lines (MEF and HT1080, Figure 2, A and B) – original data
2. Multiple transcription inhibitors (Figure 2C __and Supplemental Figure 1__):
3. Alpha-amanitin (RNA pol II and III degradation) – original data
4. Triptolide (RNA pol I and II initiation inhibition) – new data
5. Flavopiridol (RNA pol II elongation inhibition) – new data

6. Actinomycin D (DNA intercalation) – original data

7. Multiple perturbations that cause nuclear blebbing (Figure 2D ____and Supplemental Figure 1):

8. VPA histone deacetylase inhibitor, which increases euchromatin and chromatin decompaction; used because it is the most highly studied treatment by our lab (Stephens et al., 2017, 2018, 2019 MBoC; Pho et al., 2022 biorxiv) – original data
9. DZNep histone methyltransferase inhibitor, which decreases heterochromatin and chromatin decompaction (Stephens et al., 2018, 2019 MBoC) – new data
10. Lamin B1 null cells (LMNB1-/- or LB1-/-) (many previous works, including Stephens et al. MBoC 2018) – original data

11. Lamin A constitutive knockdown cells (LA KD) (Vahabikashi et al., 2022 PNAS) – new data

12. Nuclear bleb formation and stabilization in wild type cells is dependent on transcription in addition to VPA (Figure 5). – original data

13. Time dependence of suppression of nuclear blebbing requested by Reviewers 2 & 3:
14. Actinomycin D treatment of 1.5 hrs is sufficient to suppress nuclear blebs (Figure 2C) – original data
15. Transcription inhibition with alpha-amanitin, triptolide, and flavopiridol all show an increased rate of nuclear bleb reabsorption in the first 8 hrs of treatment for both VPA and LMNB1-/- perturbations (Supplemental Figure 1B) – new data.
16. This new data indicates that even formed blebs require active transcription to remain blebbed for long times
17. This new data also shows that the effect of transcription inhibition on nuclear blebbing does not require 24 hours of treatment.

__Moreover, the authors imply that VPA works through histone deacetylation yet do not provide direct evidence. It is equally likely that the application of VPA alters the acetylation pattern of a non-histone protein that eventually alters nuclear blebbing. __

The Reviewer questions whether histone deacetylation due to VPA treatment is responsible for nuclear blebbing. As the Reviewer notes in their next point below, histone deacetylation (e.g., by VPA or TSA treatment) as a mechanism for nuclear blebbing was previously established by work from our lab (Stephens et al., 2018 and 2019 MBoC) and others (Kalinin et al. MBoC 2021). This was described and referenced in the original manuscript’s introduction.

To summarize previous work, inhibition of histone deacetylation by VPA induces chromatin decompaction (Stypula-Cyrus et al. PLoS One 2013, Lleres et al. J Cell Bio 2009), increasing histone acetylation/euchromatin (Göttlicher et al. EMBO J 2001; Krämer et al. EMBO J 2003). In turn, this softens the nucleus (Stephens et al. MBoC 2017; Shimamoto et al. MBoC 2017), which succumbs to nuclear blebbing (Stephens et al., MBoC 2018). Softening and blebbing effect can also be induced by histone hyperacetylation via TSA or histone demethylation via DZNep (Stephens et al., MBoC 2018). This effect can be reversed by chromatin compaction via increased histone methylation/heterochromatin formation (Stephens et al. MBoC 2019).

In the present work, we measured histone acetylation (H3K9ac) in both VPA and VPA+alpha-amanitin perturbations to ensure that alpha-amanitin does not simply reverse the increase in VPA-based histone acetylation and thereby decrease nuclear blebbing, which it does not (Figure 3, A and B).

Altogether, inhibition of histone deacetylation by VPA as a mechanism for nuclear blebbing is established by the previous literature. The present work builds on those results to uncover a surprising new driver of nuclear blebbing which is transcirption. Therefore, we consider it to be unnecessary to provide further confirmatory measurements of VPA-treated cells beyond what is already provided in the manuscript. Finally, we point to the inclusion of new data from three other nuclear perturbations that cause nuclear blebbing that can be suppressed by transcription inhibition (Figure 2).

__Regardless, the reported findings with VPA were previously reported (Stephens et al. 2018) and the influence of alpha amanitin only represents an incremental advancement in our understanding of nuclear blebs. __

The finding that alpha-amanitin inhibits nuclear blebbing implies that a previously unknown mechanism/pathway, involving an essential genomic process, is critical to nuclear shape regulation. We therefore strongly disagree with the Reviewer that bleb inhibition upon alpha-amanitin treatment represents an incremental advance.

Moreover, the existing literature generally argues that nuclear blebbing is caused by actin-based compression and confinement. It is widely believed that the cytoskeleton deforms the nucleus, which can herniate a nuclear bleb in softer nuclei. Here, we show that with transcription inhibition there are no overt changes to actin contraction (Supplemental Figure 2), actin confinement (Figure 3E), and nuclear mechanics (Figure 3G). However, levels of blebbing change anyway! This will be a new and surprising result to those who believe the current prevailing narrative from the literature. We have now shown for the first time that transcription is also needed to form and stabilize nuclear blebs; to our knowledge, this was almost entirely unknown until now.

Further supporting our belief in the significance of our findings, Reviewer #1 and Reviewer #3 clearly state that our work is novel and important:

Reviewer #1 “To my knowledge this is the first report of this phenomena, and thus will be impactful to the nuclear mechanics field.”

Reviewer #3 “This is an interesting study that shows, for the first time, that inhibition of transcription reduces the occurrence of nuclear blebs in cells that have been pre-treated with valproic acid.”

To address the Reviewer’s concern, we have revised the manuscript to clarify that active transcription is required to form nuclear blebs across all of the perturbations now presented in this manuscript. Furthermore, we have clarified that transcription inhibition appears to suppress blebbing without altering other cellular components and properties (actin, nuclear stiffness) that are widely believed to control blebbing (see Results page 7, Results page 10, Discussion page 14).

Adding to the concern is that actinomycin D does not have the same level of influence as alpha amanitin (Figure 2), which suggests the alpha amanitin is having a pleotropic impact on blebbing. To validate that the changes in blebbing in the presence of VPA are dependent upon active transcription, the authors should use the anchor-away technique to remove RNAP from the nucleus thereby avoiding any indirect effects of the drugs (i.e., alpha amanitin) in use. Further adding concern that it is an indirect outcome is the prolonged incubation period (16-24 hours) that is apparently needed to observe the changes (page 5 paragraph 4). If it is active transcription that is causing the change in blebbing, then this should be apparent in a much shorter time frame (The Reviewer is worried about possible differences between transcription inhibitors actinomycin D and alpha amanitin. To further address these concerns in the revised manuscript, we now present new data for VPA without transcription inhibitor and VPA with transcription inhibition vy four different transcription inhibitors (__Figure 2C). Inhibitors include alpha-amanitin (RNA pol II degradation), triptolide (transcription initiation inhibition), flavopiridol (transcription elongation inhibition), and actinomycin D (DNA intercalation). All VPA plus transcription inhibitor treatments result in a significant decrease in nuclear blebbing relative to VPA treatment alone (p (p > 0.05, Figure 2C). Thus, there is no significant difference in the degree of nuclear blebbing suppression between the four different transcription inhibitors used.

Furthermore, the Reviewer raises concerns about the time interval from the start of transcription inhibitor treatment to suppression of nuclear blebbing. We agree that considering this time interval is valuable. However, we need to consider that the time interval for each of the different transcription inhibitors to take effect is different (Bensaude 2011 Transcription). Alpha-amanitin inhibits transcription in 4-8 hours (10 µM, Nguyen et al., 1996 NAR), triptolide (1 µM, Chen et al. 2014 Genes Dev) and flavopiridol (0.5 µM, Chen et al., 2005 Blood) work in 2-4 hours, and actinomycin D works in about 1 hour (10 mg/mL, Lai et al. 2019 Methods). These times are now mentioned in the manuscript (Figure 2 legend and Methods section).

It was not, however, known in advance how long it would take for transcription inhibition to have an effect on nuclear morphology. Therefore, the time to observe bleb suppression could have been longer than these treatment durations. As mentioned above, treatment with actinomycin D for 1.5 hours results in a similar decrease in nuclear blebbing as compared to the other inhibitors with 24-hour treatment (Figure 2C). To further address these concerns, we provide new data in the revised manuscript showing tracking of nuclear bleb reabsorption during the first 8 hours of treatment with alpha amanitin, triptolide, and flavopiridol via live cell imaging. Nuclear bleb reabsorption for both VPA and LMNB1-/- perturbations goes from ~5 % to 30% or greater during the first 8 hours of treatment with each of the transcription inhibitors (Supplemental Figure 1B), consistent with the time required to fully inhibit transcription. This supports our conclusion that transcription is essential to stabilizing nuclear blebs.

__In addition to these issues, the authors rely on immunofluorescence signals to measure the levels of various factors including the Ser5 and Ser2 phosphorylation, which is capturing the total levels of these factors and not the DNA bound forms. If the changes in blebbing actually involve transcription initiation, then the authors should include measurements on the DNA-bound factors. __

We are measuring Ser5 and Ser2 phosphorylation of RNA polymerase to track the actively DNA transcribing population. These markers appear on DNA-bound RNAP. Ser5 and Ser7 of RNAP are phosphorylated during initiation, and subsequently dephosphorylated during transcription elongation, while Ser2 is added at that time (Hsin and Manley 2012 Genes Dev). Ser2 is removed at transcription termination. Therefore, we expect immunofluorescence to measure DNA-bound RNAP.

__As reported the authors conclude that there is no changes in Ser2 and Ser5 phosphorylation yet they report that total RNA levels rise (Figure 1). How is the disconnect between RNA levels and Ser2 and Ser5 phosphorylation occurring? __

The Reviewer raises a question about how VPA treatment increases RNA levels but not levels of active RNA pol Ser2 and Ser5. While this is an interesting question, without a dedicated investigation, we can only speculate, at best; this question is beyond the scope of the paper focused on how transcription inhibition suppresses nuclear blebbing. The point of this data is to show that treatment with alpha-amanitin alone and along with VPA causes decreases in both RNA and RNA pol II Ser2 and 5 confirming transcription inhibition.

__Comparably, they use H3K9ac immunofluorescence as a measure of euchromatin. While the authors might be gaining a view on the total levels of H3K9ac under these experimental conditions, it is not clear whether this is DNA associated or not. Minimally, the authors should perform ATAC-Seq to judge the changes in euchromatin. __

The Reviewer questions the use of H3K9ac immunofluorescence as measurement of euchromatin levels, particularly in VPA-treated cells. The relationship between VPA and chromatin decompaction / euchromatin levels has been previously established (e.g., Stypula-Cyrus et al. PLoS One 2013, Felisbino et al. J Cell Biochem 2014, Lleres et al. J Cell Bio 2009). New data in Figure 3B shows that heterochromatin marker H3K9me2,3 also is not altered by alpha-amanitin treatment. In the case VPA + alpha-amanitin treatment, micromanipulation and nuclear height measurements provide further evidence that chromatin decompaction remains, since chromatin-based force response is unchanged from VPA treatment alone (Figure 3, E and G).

Again, we note that our manuscript focuses on the effects of transcription on nuclear blebbing and rupture, which were not previously reported and differ from the current understanding in the literature. Furthermore, ATAC-seq is a major undertaking that is simply not appropriate for further proving an auxiliary point about a previously established effect.

In summary, the original manuscript addresses this point. The specific experiment requested by the Reviewer is not necessary and is far beyond the scope of this study.

A final major concern is the lack of a correlation between the blebbing and nuclear ruptures (page 7 paragraph 3; Figure 4). If ruptures are not correlating with the blebbing, what is the relevance of the blebbing?

The Reviewer is asking for a clarification of the importance of nuclear blebbing in relation to nuclear ruptures. We have revised the manuscript to add new text to the Figure 4 legend clarifying the measurements and to the Discussion section describing the importance of this data (Discussion pages 12-13 and page 14). We discuss this in more detail below.

We would like to clarify that blebbing and nuclear rupture are not uncorrelated, as suggested by the Reviewer. We and others have shown that nuclear blebs are sites of high curvature that result in nuclear ruptures. In the present manuscript, timelapse imaging of nuclear bleb formation has been observed to result in nuclear rupture within minutes in all imaged cases (Figure 5). This data in the manuscript agrees with previous published data from our lab of bleb formation to rupture in >95% of the time (Stephens et al., 2019 MBoC). Furthermore, stabilized nuclear blebs persist for hours (Supplemental Figure 1B) and undergo more rupture, as shown in Figure 4D. Therefore, ruptures remain correlated with nuclear blebs in our study.

What we have shown, however, is that the percentage of cells that undergo at least one nuclear rupture during the time lapse is not statistically significantly decreased from VPA-treated levels by the addition of alpha-amanitin (Figure 4B). This appears to be due to two factors: 1) a basal level of nuclear rupture (see wild type data in Figure 4) and 2) an increase in the level of non-bleb-based nuclear rupture. However, importantly, non-bleb-based ruptures appear to occur less frequently for cells that undergo nuclear ruptures. Of the cells that exhibit nuclear rupture, those with non-bleb-based ruptures on average undergo only a single rupture over a 3-hour timelapse whereas those undergoing bleb-based rupture undergo an average of > 2 ruptures over the same time (Figure 4D).

Altogether, these data point to a correlation between blebbing and rupture, where blebbing can promote nuclear rupture, but is not essential for rupture. Therefore, observations of blebs are important in that they correspond to increases in nuclear rupture and corresponding nuclear dysfunction, such as DNA damage. The observation of non-bleb-based rupture, while not entirely a new (Chen et al. PNAS 2018, Stephens et al. MBoC 2019, Pho et al. bioRxiv 2022), is interesting because it may be driven by a different mechanism; transcription is not essential for nuclear ruptures in the absence of nuclear blebs but promotes rupture in the presence of blebs. These results add to our knowledge of the factors regulating nuclear integrity and shape, and we anticipate that they will be further investigated in future studies.

Finally, beyond these findings, we speculate that blebbing itself may be harmful to cell nuclear function. Previous studies have observed that nuclear deformations can cause DNA damage (Shah et al. Curr Biol 2021), chromatin reorganization (Jacobson et al. BMC Biol 2018, Golloshi et al. EMBO J 2022), and alterations to mechanotransduction (reviewed in Kalukula et al. Nat Rev Mol Cell Biol 2022). The extent to which the changes associated with these “nuclear deformations” require blebbing, rupture, or both is under investigation by various labs. Furthermore, previous studies (Shimi et al. Genes Dev 2008; Pfleghaar et al. Nucleus 2015) along with the present study (RNA Pol Ser2 and Ser5; Figure 6) have shown that chromatin content and, possibly, functionality is different within the nuclear bleb. Data in another manuscript in preparation from our lab, further suggests that there is limited exchange of biomolecular content between the nuclear body and bleb. Therefore, while we cannot conclusively claim that blebs are themselves deleterious to function, there is a growing body of suggestive evidence that this is the case.

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

This is an interesting study that shows, for the first time, that inhibition of transcription reduces the occurrence of nuclear blebs in cells that have been pre-treated with valproic acid. The data that supports this is in Figure 2, collected in two different cell types (MEFs and HT1080 cells). The effect appears robust. New data is also provided that a marker of initiation of transcription but not transcriptional elongation is enriched in valproic acid-induced blebs.

We thank Reviewer #3 for positive comments that our study is “interesting”, “reproducible”, and data that shows the effect of transcription on nuclear blebbing “for the first time”.

This Reviewer asks for clarifications on 1) how transcription is a new mechanism for nuclear bleb formation and not part of the traditional view, 2) the generality of our conclusions (similar to Reviewer #2) since we report “on the inhibition of transient, small, valproic acid-induced blebs by alpha-amanitin”, and 3) the insight the modeling provides. We have provided new data and made changes to the manuscript to address all the Reviewer’s comments.

__ Major comments

1. The paper makes general claims about transcription and nuclear shape, when in reality, it is only reporting on the inhibition of transient, small, valproic acid-induced blebs by alpha-amanitin. This scenario under which the experiments were performed, for which there is no obvious physiological counterpart, ought not to be construed to challenge or contrast with the current understanding that the nucleus maintains its shape by resisting cytoskeletal forces. Cytoskeletal forces are well-known to establish nuclear shape; nuclear shape in this context, is generally taken to refer to the gross shape of the nucleus (e.g. elliptical, circular, etc.), and not small local blebs that may form due to F-actin based confinement or other mechanisms. Thus, this interpretation is overstated:

"Surprisingly, we find that while nuclear stiffness largely controls nuclear rupture, it is not the sole determinant of nuclear shape. This contrasts with previous studies, which suggested that the nucleus maintains its shape by resisting cytoskeletal and/or other external antagonistic forces (Khatau et al., 2009; Le Berre et al., 2012; Hatch and Hetzer, 2016; Stephens et al., 2018; Earle 12 et al., 2020)."

__

The Reviewer appears to be concerned with two issues in this comment. First, the Reviewer is concerned about our use of the word shape, which could be interpreted too generally, rather than as categorizing the blebbing and rupture phenomena that we observe in this study. We appreciate the Reviewer’s feedback and have made changes to this sentence as well as the paper in general to clarify that we are focused on nuclear blebs. Second, there is the issue of to what degree our results modify our understanding of the role of nuclear stiffness in nuclear blebbing and rupture. We discuss this below.

To address the Reviewer’s comment that the results are limited to “the inhibition of transient, small, valproic acid-induced blebs by alpha-amanitin” we provide new data and context for our results. The revised manuscript includes 1) new data using four transcription inhibitors and four nuclear blebbing perturbations and 2) original data showing that nuclear blebs are persistent rather than small and transient, and they alter gross nuclear shape. Our results are relevant to a wider range of blebbing/rupture and bleb/rupture suppression scenarios, as exemplified by the different nuclear perturbations, transcription inhibitors, cell types tested in our experiments, and long lifetimes for nuclear blebs. More specifically:

1) The Reviewer notes that our original studies were done with VPA and alpha-amanitin, similar to Reviewer #2 concerns. We provide new data to now show that 4 different transcription inhibitors can suppress nuclear blebbing across 2 chromatin and 2 lamin perturbations (Figure 2 and Supplemental Figure 1). Thus, our new data supports the idea that transcription is broadly required for nuclear blebbing.

2) The Reviewer states that blebs are small and transient, and that “shape” is meant to reflect the gross shape (e.g., circular). In fact blebs are long-lived as we show with new data that most (>95%) of VPA and LMNB1-/- blebs, remain at the end of an 8-hour timelapse (Supplemental Figure 1B). Furthermore, on average, nuclear blebs account for 15% of the nuclear size in VPA-treated cells (Figure 6E). While not measured in this paper, many studies have shown that nuclear blebs cause gross circularity to decrease significantly and that changes in circularity are associated with nuclear rupture (e.g., Stephens et al. MBoC 2018, Xia et al. JCB 2018). Most recently, we show nuclear blebs decreased nuclear circularity significantly in another manuscript under review (Pho et al., 2022 biorxiv).

The Reviewer also argues that our data showing the importance of transcription in nuclear blebbing “ought not to be construed to challenge or contrast with the current understanding that the nucleus maintains its shape by resisting cytoskeletal forces.” We acknowledge that our results are not sufficient to rule out the broad assertion made by the Reviewer. However, our data shows for the first time that nuclear blebbing relies on transcriptional activity, while we measure no change in actin contraction or confinement or nuclear stiffness (respectively, Supplemental Figure 2 and Figure 3, C-E). Consequently, these results are a challenge to the current understanding, which must be updated by our results and future experiments. At the same time, we note that this manuscript’s Discussion section acknowledges that we have data in another preprint in which inhibition of actin contraction decreases nuclear blebbing to near 0% in wild type and perturbations (Pho et al., 2022 biorxiv). Together, these observations suggest a complicated picture in which multiple factors are jointly responsible for regulating nuclear blebbing and rupture.

__ As an aside, the data in the paper does not appear to support the interpretation that "nuclear stiffness largely controls nuclear rupture". It is unclear what the authors mean by this statement.__

We originally intended that comment to state the previous understanding in the literature, but we realize it was unclear. We appreciate the Reviewer’s feedback and have revised the text.__ __

__ 2. Further to point 2, treatment with alpha-amanitin does nothing to the occurrence of blebbing in normal cells. Thus, the data are specifically applicable to valproic acid-treated cells. As such, the broad interpretations related to nuclear shape and mechanics should be tempered.__

The Reviewer is concerned that we cannot support the claim that this effect is broad and general; these concerns are also raised by Reviewer #2. We have provided new data and highlight original data to support that this effect is in fact broad and general, and moreover, that the data supports a role for transcription in nuclear blebbing.

We specifically address the Reviewer’s statement: “treatment with alpha-amanitin does nothing to the occurrence of blebbing in normal cells”. In the original manuscript, we provided data that showed that wild type nuclear bleb formation and stability are suppressed upon transcription inhibition (Figure 5) even though the percentage of wild type nuclei exhibiting a bleb is not changed by alpha-amanitin treatment (Figure 2). We also provided data showing that the predominant type of nuclear rupture changes with alpha-amanitin treatment, including in wild type cells (blebbed vs. not, Figure 4C). Thus, while the effects of transcription inhibition are most easily visible in VPA-treated cells, they are also present in wild type cells in how blebs are formed and stabilized (Figure 5). We have revised the manuscript to better highlight this important point.

In addition, we again emphasize that our results extend beyond VPA-induced blebs. Our revised manuscript now includes new data of 4 different perturbations (to chromatin histone modifications and lamins A and B) that induce nuclear blebs, which can be suppressed by 4 different transcription inhibitors (Figure 2 and Supplemental Figure 1). As previously noted by both Reviewers 1 and 3, this effect is reproducible in different cell lines. This new data directly addresses the concern that the effect is only applicable to VPA and alpha amanitin.

Nonetheless, we agree with the Reviewer that we cannot support broader claims that nuclear mechanical properties are unaltered by transcription inhibitors across all scenarios, as we only measured this change in VPA-treated cells. Micromanipulation force experiments are detailed and time consuming, making it difficult to include data for multiple perturbations. We chose VPA because we have the most measurements of this perturbation which have remained consistent over the life of micromanipulation force measurements. Therefore, we have revised our statements on nuclear mechanics in the revised manuscript (page 14).

__ T____he motor model for RNA pol II activity assumes that the motor 'repels' nearby chromatin units. It is not clear how this is related to the mechanism of motor action of RNA pol II on chromatin during transcription.__

The point of the model is not to precisely reproduce the manner in which transcribing RNA pol II exerts forces on the chromatin fiber. Instead, we have developed a coarse-grained model to study how the collective activity of molecular motors might drive chromatin dynamics and consequently, changes in nuclear shape, either global or local.

The model itself is based on our earlier models, which were used to recapitulate and understand how changes to chromatin mechanical properties governed nuclear rigidity (Stephens et al. MBoC 2017, Banigan et al. Biophys J 2017, Strom et al. eLife 2021; also see a similar model by Lionetti et al. Biophys J 2020) and how nonequilibrium activity due to molecular motors, such as RNA pol II, can drive coherent chromatin dynamics (Liu et al. PRL 2021), which have been observed in live-cell imaging experiments (e.g., Zidovska et al. PNAS 2013; Shaban et al. NAR 2018; Shaban et al. Genome Biol. 2020, among others). The current model therefore explores how the newly observed connection between transcription and nuclear blebbing could be explained by known phenomena.

We note that the "repelling” motors used to model RNA pol II activity in the present work are in many ways qualitatively similar to the dipolar “extensile” motors used by other researchers to model motor-driven chromatin dynamics (e.g., see Saintillan et al. PNAS 2018). More generally, study of “active matter” over the last 20-30 years (and statistical physics over the last century) has shown that precise details of active molecular agents are often unimportant to the larger-scale behavior of the system (e.g., see Marchetti et al. Rev Mod Phys 2013). Thus, we view the repulsive motors as modeling the effective behavior of many RNA pol II within a sub-micron region of chromatin. Better establishing the differences between different choices of motor activities is the subject of a modeling paper in preparation.

To address the Reviewer’s concern, we have more clearly stated the scientific foundations of the model, and we have revised our description of the model to clarify that we do not intend to model the behavior of individual RNA pol II by individual repulsive motors (see Results section, page 10).

__The motor model also does not seem to add conclusive insight to the manuscript, as the nuclear shapes predicted are not directly comparable to the experimental shapes which are flat and smooth with only an occasional, single, local bleb. __

The Reviewer raises two related points with this comment: that bulges and blebs are not directly comparable, and therefore, that the model “does not seem to add conclusive insight to the manuscript.”

We agree with the Reviewer that bulges in the simulations are not blebs as they are observed in the experiments. However, it seems likely to us that bulges are necessary precursors to bleb formation; it is difficult to envision how a large local nuclear protrusion could form without first bulging outward from the nuclear body. Furthermore, we disagree with the assertion that nuclei are generally flat and smooth, as qualitative and quantitative analysis of imaging data reveals that nuclei exhibit shape fluctuations and irregularities across multiple scales (see, for example, Chu et al. PNAS 2017, Patteson et al. JCB 2019, Stephens et al. MBoC 2019, Liu et al. PRL 2021).

Nonetheless, the observation of bulges but not blebs is a shortcoming of the simulation model. We believe this shortcoming reflects a tradeoff made in developing this model; we chose to develop and study a model with relative simplicity compared to a real cell nucleus. A more complicated model might better capture some aspects of nuclear blebbing at the expense of additional complexity. For example, the current model does not allow lamin-lamin or chromatin-lamin bonds to rupture, either stochastically or due to high forces. This effect, which is likely present in vivo, might be necessary for generating more bleb-like structures in simulations. Developing and refining such a model is an active pursuit within our collaboration, but for the moment, it is beyond the present purpose of the model.

Instead, the purpose of the model is to determine whether the observed effect of transcription inhibition on nuclear blebbing / localized shape deformations can be understood through known biophysical phenomena. Established models – to the extent that they exist – were insufficient because they typically relied on nuclear mechanics, which our experiments provide data that transcription is not changing nuclear mechanical rigidity. The current model demonstrates how motor activity within chromatin can alter the structure and dynamics of the lamina. The simulations are certainly not proof that transcription affects nuclear blebbing through the proposed mechanism. However, they are a first-of-their kind demonstration of how nonequilibrium biophysical activity (such as that generated by transcription) within a biopolymer system (chromatin) can emergently alter the geometry of the confining boundary (the lamina). This new result provides a plausible interpretation for the experiments in the manuscript.

In the revised manuscript, we have clarified our modeling approach and objectives in the Results and Discussion sections, and we have more clearly identified and discussed the limitations of the model (Results pages 10-11, Discussion page 15).

The model offers 'proof of principle', but is not capable of ruling out alternative mechanisms (such as nuclear pressurization by confinement, chromatin decompaction, or changes to osmotic pressure). It may be more appropriate to include the model in the discussion as opposed to presenting it as a new result that can be reliably interpreted through comparisons with experiment.

We respectfully disagree with the suggestion to include the model in the Discussion section instead of the Results. As discussed above, the model is new biophysics research and the simulations produced new scientific results, even if the overall interpretation remains open.

However, we have some thoughts about the alternatives suggested by the Reviewer. This is discussed in detail below, but briefly: experimental data, rather than the model itself, suggests that the alternative mechanisms mentioned by the Reviewer do not explain the effects of transcription. After treatment with alpha-amanitin, we do not observe changes to actin-based confinement or contraction (Figure 3E, Supplemental Figure 2), and there are no changes to chromatin histone modifications or nuclear rigidity (Figure 3). We also are skeptical of osmotic pressure arguments since 1) fluid, ions, and small biomolecules should freely flow through nuclear pores to maintain osmotic pressure balance between the nucleus and the cytoplasm, especially on hours-long time scales, and 2) increasing the osmotic pressure by fragmenting chromatin has previously been observed to have either no effect or a suppressive effect on nuclear stiffness (Stephens et al. MBoC 2017, Belaghzal et al. Nat Genet 2021), which would potentially increase blebbing (the opposite of the effect suggested by the Reviewer). We have addressed this further in the revised Results section (page 10) and below.__ __

__ 4. The data in the paper is not strong enough to rule out the more conventional mechanism of nuclear pressurization, which could be caused by F-actin based confinement or chromatin decompaction, or changes to osmotic pressure. Immunostaining of myosin is not a reliable way to compare myosin activity across conditions. It is possible that the long treatment with alpha-amanitin (unto 24 h, Fig. 2) relieves the pressure in the nucleus without measurable changes in the already established cell shape and hence the nuclear shape (height changes in spread cells are small at best -- valproic acid appears to reduce height by ~0.5 microns in Figure 3E which is smaller than the optical resolution along the z-axis of a typical confocal microscope).__

The Reviewer has proposed several alternative mechanisms and questioned the use of immunostaining and nuclear height measurements in the manuscript. We address each of these below.

Specifically, the Reviewer is concerned that we cannot rule out the more conventionally believed mechanisms of 1) actin confinement, 2) actin contraction 3) chromatin decompaction and/or 4) osmotic pressure. We have revised the text to clarify that our data and data from others strongly supports that these four “conventional” mechanisms are not responsible for transcription inhibition-based nuclear blebbing suppression (revisions on pages 7, 10, 14).

1) Actin confinement, as measured by nuclear height does not change upon transcription inhibition (Figure 3, C-E). Thus, our data supports the idea that transcription inhibition suppresses nuclear blebbing through a different mechanism. The Reviewer objects to this measurement on the basis that even the 0.5 µm change observed for VPA-treated cells is below optical resolution. However, optical resolution is not relevant to this measurement because we are not resolving two objects; rather, we are measuring the size of one object, the nucleus.

When two dots/objects are separated in the same frame or in different z slices, one needs to clearly distinguish two gaussians point spreads from the two objects a distance X apart. That is resolution and that is not the relevant limitation here. We measure the size of one object (the nucleus) using full-width half-maximum, which can quantify changes in nuclear height at scales finer than the optical resolution. For example, the FWHM of a fluorescence bead can be observed to change by just 10’s of nm depending on the light emitted; with small wavelengths, one has smaller FWHM (from the Rayleigh criterion, θ = 1.22λ/D, where λ is the wavelength of the light). Our measurements are through a z-stack at 200 nm steps, thus the change in distance from wild type to VPA-treated of 0.5 µm is 2.5 z steps (not smaller than one z step). Finally, we have additional data showing our ability to measure these differences many times over (Pho et al. 2022 biorxiv).

Image left is from: https://en.wikipedia.org/wiki/Full_width_at_half_maximum

Image right is a crop of Figure 3D from the manuscript.

2) Actin contraction, as measured by γMLC2, does not change either (Supplemental Figure 2). However, we know that actin contraction is a major determinant of nuclear blebbing (Mistriotis et al., 2019 JCB and Pho et al., 2022 biorxiv). Therefore, our data support that transcription affects blebbing in some other way than actin contraction.

The Reviewer disputes this finding by stating that “immunostaining of myosin is not a reliable way to compare myosin activity across conditions.” Published reports show that γMLC2 immunostaining is a reliable way to measure actin contractility changes (Wan et al. MBoC 2012; Ramachandran et al. Mol Vision 2011; Duan et al. Cell Cycle 2016; Nishimura et al. PLOS One 2020). We have another preprint showing that alterations to actin contraction as measured by immunostaining of phosphorylated myosin light chain 2 (γMLC2) determine nuclear blebbing, independent of changes in actin confinement (Pho et al., 2022 biorxiv). There, we clearly show that changes in γMLC2 immunostaining can measure changes in actin contraction due to well-established modulators. Similarly, the ROCK inhibitor Y27632 in Supplemental Figure 2 can be viewed as a positive control in that γMLC2 immunostaining is clearly decreased after treatment with the inhibitor.

3) Chromatin decompaction via H3K9ac and chromatin-based nuclear rigidity are not rescued by transcription inhibition. New data also shows that levels of heterochromatin H3K9me2,3 does not change upon transcription inhibition (Figure 3B). The new data presented in this manuscript shows that transcription inhibition also suppresses blebbing in DZNep-treated cells (Figure 2D), where chromatin compaction by heterochromatin formation is inhibited (Stephens et al. MBoC 2019). Together, these experiments suggest that transcription inhibition is not suppressing nuclear blebs through increases in heterochromatin-based chromatin compaction.

Furthermore, the lack of change in the measurement of nuclear stiffness via micromanipulation (Figure 3G) provides a complementary metric suggesting that chromatin compaction is unchanged, at least in the case of VPA + alpha-amanitin.

Altogether, these results are inconsistent with transcription inhibition suppressing blebs through alterations to chromatin compaction.

4) Osmotic pressure is the least or not at all established of the four “traditional” mechanisms. The Reviewer proposes that transcription inhibitors, such as alpha-amanitin, could relieve osmotic pressure within the nucleus. We disagree with this explanation in that it is implausible for the nucleus to maintain an osmotic pressure imbalance in VPA-treated cells over long periods of time. Fluid, ions, and small biomolecules likely can flow through nuclear pores to maintain osmotic balance between the nucleoplasm and cytoplasm, especially over the hours long duration of VPA treatment. Furthermore, we are skeptical that VPA treatment, even with its chromatin-decompacting effects, significantly increases osmotic pressure because nuclear stiffness actually decreases after VPA treatment (Stephens et al. MBoC 2017, 2018, 2019; Krause et al. Phys Bio 2013; Shimamoto et al. MBoC 2017; Hobson et al. MBoC 2020) . Increased osmotic pressure should cause the nucleus to be stiffer. Moreover, nuclei in VPA-treated cells consistently undergo blebbing and rupture, which would naturally relieve any pressure imbalance. Thus, the notion that the measurements after hours VPA or VPA+aam treatment (Figures 2-5) are the result of a steady-state change in osmotic pressure is simply inconsistent with the experimental data.

We note that in cases of acute osmotic shock, where the osmotic pressure balance of the nucleus may be altered, the nucleus changes in size (e.g., see Finan et al., 2009 Ann Biomed Eng), which we do not observe in our experiments. Our measurements of nuclear area (Figure 6C) and height (Figure 3E) show no change nuclear size upon transcription inhibition (for more on the issue of height measurement, see the previous point).

To further address concerns about overnight treatment causing off-target effects, we have provided new data from a shorter treatment duration in the manuscript. The new data shows that within 8 hours, blebs exhibit more reabsorption after alpha-amanitin, triptolide, and flavopiridol treatment in both VPA-treated and LMNB1-/- cells (Supplemental Figure 1B). Additionally, we note that actinomycin D decreased nuclear blebbing in 1.5 hours, and thus did not require overnight treatment.

In summary, our original and new data clearly show that transcription contributes to nuclear blebbing. Transcription inhibition does not change other factors (such as actin-based confinement or contraction, changes in chromatin compaction, or osmotic pressure), that have been shown or may be thought to contribute to nuclear blebbing. The revised manuscript addresses this issue through the inclusion of new data, as discussed above.

__

Further to point 4, the data in Figure 4B and 4D both show a decrease in the mean of the % of ruptured nuclei and rupture frequency (please provide units for this frequency on the Y-axis). With more experiments, perhaps the data would have reached statistical significance?__

The Reviewer is asking for clarification on the data included in Figure 4 B and D reporting the percentage of cells that display a nuclear rupture.

We have revised the manuscript to clarify that Figure 4B is the percentage of all nuclei that show at least one nuclear rupture. The measurement unit, percent (listed as “[%]”), is shown on the y-axis. The revised manuscript also clarifies that Figure 4D reports, for the nuclei that rupture, the average number of times a nucleus ruptures during the 3-hour time-lapse.

The Reviewer stats that “with more experiments, perhaps the data would reach statistical significance?” To address this comment, we have altered the text to explain that % of all nuclei that rupture at least once does not significantly decrease by t-test but does show a non-statistically significant decrease. The data in Figure 4B shows that VPA causes 18.5 +/- 2.7 % rupture and VPA+alpha-amanitin causes 12.4 +/- 1.5 % rupture. Student’s t-test is p = 0.08 which is not statistically significant (p > 0.05) for six biological replicates each consists of n = 100-300 cells. We feel the data speaks for itself without us doing more experiments with the sole purpose of getting a lower p value. The stronger data is in Figure 4D, which clearly shows less nuclear ruptures per nucleus. We appreciate the Reviewer’s perspective and have modified the text in the Results and Discussion sections to reflect these important points (pages 8 and 14). __ __

__ Minor comments.

1. Confirmatory data, which has already been published in the same cell line in the past, could be moved if possible to supplemental information. Figure 1 seems to be a characterization of the efficacy of alpha-amanitin which is well-known, and therefore does not represent an original finding. It should perhaps be in supplemental information.__

We understand the Reviewer’s point but would like to leave Figure 1 as a main text figure to provide a clearer story for all readers of our manuscript.__ __

__ 2. Did the counting method used to collect data in Figure 4B exclude nuclei that rupture multiple times? This should be specified in the manuscript.__

No, Figure 4B is the percentage of nuclei that rupture, which includes nuclei that rupture any number of times as a single nucleus that ruptures. We have revised the Figure 4 legend to clarify this point. __ __

__ 3. This statement should be rephrased: "Since transcription is needed to form and stabilize nuclear blebs, at least some aspect of nuclear shape deformations appears to be non-mechanical" - deformation in the model in Figure 7 is clearly 'mechanical' - driven by motor force.__

We appreciate the Reviewer’s feedback and have rewritten the text changes this to “independent of the bulk mechanical strength of the nucleus”. __ __

__ 4. It is important to specify the times for which cells were treated with the various drugs in each figure (and not just in figure 2).__

We appreciate the Reviewer’s feedback and have added this information to each figure legend.__

__

__

Reviewer #3 (Significance (Required)):

This paper reports new data that nuclear blebbing induced by treatment with valproic acid can be inhibited by co-treatment with alpha-amanitin. The data provided are reproducible across different cell lines. The data suggest that inhibition of transcription inhibits blebs which are induced by valproic acid treatment, but it does not inhibit blebs in cells untreated with valproic acid. Immunostaining reveals some enrichment of RNA pol II phosphorylated at Ser5 in valproic acid-induced blebs, suggesting an enhancement of transcription-initiation (but not transcriptional elongation) in the bleb. Alpha-amanitin treatment reduces bleb formation and bleb lifetime.

While the data are clearly presented, and interesting in terms of relating transcription to blebbing, the proposed interpretation in terms of a new mechanism of blebbing is not strongly supported by the data or by the computational model. More definitive evidence is required to rule out that blebbing in valproic acid treated cells is not caused by a pressurization of the nucleus due to valproic acid treatment, which could be released by treatment with alpha-amanitin treatment for upto 24 h. The manuscript generalizes the findings to 'nuclear shape', and interprets them as suggestive of an alternative mechanism of establishment of nuclear shape; this generalization seems unsupported by the data.__

Overall, the data provided is novel and interesting to cell biologists, provided more definitive evidence can be provided to rule out other models and to establish the new proposed model for nuclear blebbing. Else, the claims of an alternative mechanism for blebbing could be toned down, and the data on the relation between transcription and blebbing, which is the novel and interesting finding in this paper, could be presented in a more focused way.

We appreciate that the Reviewer points out that “the data are clearly presented and interesting” and “reproducible across different cell lines.” The Reviewer’s main concerns appear to be with: 1) the effect of transcription inhibition on blebbing that is not induced by VPA, 2) alternatives or limitations to our proposed interpretation of the results, and 3) describing our results as applicable to “nuclear shape” in general.

We have addressed each of these concerns in detail in the above response and the revised manuscript. To summarize:

• We have included new data to show that four different transcription inhibitors combined with four different nuclear perturbations exhibit the same effects (Figure 2 and Supplemental Figure 1). Furthermore, we have clarified in the revised manuscript that even wild type (“untreated”) nuclei exhibit changes to blebbing dynamics (decreased stability, increased reabsorption) after transcription inhibition (Figure 5). Furthermore, concerns about time intervals was addressed by time lapse imaging showing that bleb reabsorption (return to normal shape) increases six-fold in the first 8 hours of transcription inhibitor treatment (Supplemental Figure 1B).
• The original manuscript, new data, and previous data from the literature provides evidence that alternative mechanisms involving “pressurization” (discussed above), the actin cytoskeleton (Figure 3E and Supplemental Figure 2), and chromatin and nuclear rigidity (Figure 3) do not explain the observed effects of transcription inhibition. We discuss this in detail in the revised manuscript and the above response. Furthermore, we have revised our presentation and discussion of the simulation model to describe its relevance more clearly to the results, support its inclusion in the manuscript, and provide appropriate caveats on our computational findings.
• We have revised the manuscript to clarify that our results primarily concern nuclear blebbing and rupture. The Reviewer is correct that the current investigation does not particularly focus on larger-scale shape such as circularity/ellipticity. In summary, our data clearly indicate that transcription contributes to nuclear blebbing and rupture. Previously suggested mechanisms of blebbing are generally inconsistent with the observed effect in combination with our other measurements. The model investigates a plausible new, complementary mechanism, which in itself represents an advance in biophysical modeling and ties the manuscript together.

We thank the Reviewer for their thorough critique, which we have now addressed. We believe that the new experimental data and analysis and computational modeling in our manuscript significantly advances our overall understanding of nuclear blebbing, even as it raises new questions to be addressed by future work.

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Referee #3

Evidence, reproducibility and clarity

This is an interesting study that shows, for the first time, that inhibition of transcription reduces the occurrence of nuclear blebs in cells that have been pre-treated with valproic acid. The data that supports this is in Figure 2, collected in two different cell types (MEFs and HT1080 cells). The effect appears robust. New data is also provided that a marker of initiation of transcription but not transcriptional elongation is enriched in valproic acid-induced blebs.

Major comments

1. The paper makes general claims about transcription and nuclear shape, when in reality, it is only reporting on the inhibition of transient, small, valproic acid-induced blebs by alpha-amanitin. This scenario under which the experiments were performed, for which there is no obvious physiological counterpart, ought not to be construed to challenge or contrast with the current understanding that the nucleus maintains its shape by resisting cytoskeletal forces. Cytoskeletal forces are well-known to establish nuclear shape; nuclear shape in this context, is generally taken to refer to the gross shape of the nucleus (e.g. elliptical, circular, etc.), and not small local blebs that may form due to F-actin based confinement or other mechanisms. Thus, this interpretation is overstated:

"Surprisingly, we find that while nuclear stiffness largely controls nuclear rupture, it is not the sole determinant of nuclear shape. This contrasts with previous studies, which suggested that the nucleus maintains its shape by resisting cytoskeletal and/or other external antagonistic forces (Khatau et al., 2009; Le Berre et al., 2012; Hatch and Hetzer, 2016; Stephens et al., 2018; Earle 12 et al., 2020)."

As an aside, the data in the paper does not appear to support the interpretation that "nuclear stiffness largely controls nuclear rupture". It is unclear what the authors mean by this statement. 2. Further to point 2, treatment with alpha-amanitin does nothing to the occurrence of blebbing in normal cells. Thus, the data are specifically applicable to valproic acid-treated cells. As such, the broad interpretations related to nuclear shape and mechanics should be tempered. 3. The motor model for RNA pol II activity assumes that the motor 'repels' nearby chromatin units. It is not clear how this is related to the mechanism of motor action of RNA pol II on chromatin during transcription. The motor model also does not seem to add conclusive insight to the manuscript, as the nuclear shapes predicted are not directly comparable to the experimental shapes which are flat and smooth with only an occasional, single, local bleb. The model offers 'proof of principle', but is not capable of ruling out alternative mechanisms (such as nuclear pressurization by confinement, chromatin decompaction, or changes to osmotic pressure). It may be more appropriate to include the model in the discussion as opposed to presenting it as a new result that can be reliably interpreted through comparisons with experiment. 4. The data in the paper is not strong enough to rule out the more conventional mechanism of nuclear pressurization, which could be caused by F-actin based confinement or chromatin decompaction, or changes to osmotic pressure. Immunostaining of myosin is not a reliable way to compare myosin activity across conditions. It is possible that the long treatment with alpha-amanitin (unto 24 h, Fig. 2) relieves the pressure in the nucleus without measurable changes in the already established cell shape and hence the nuclear shape (height changes in spread cells are small at best -- valproic acid appears to reduce height by ~0.5 microns in Figure 3E which is smaller than the optical resolution along the z-axis of a typical confocal microscope). 5. Further to point 4, the data in Figure 4B and 4D both show a decrease in the mean of the % of ruptured nuclei and rupture frequency (please provide units for this frequency on the Y-axis). With more experiments, perhaps the data would have reached statistical significance?

Minor comments.

1. Confirmatory data, which has already been published in the same cell line in the past, could be moved if possible to supplemental information. Figure 1 seems to be a characterization of the efficacy of alpha-amanitin which is well-known, and therefore does not represent an original finding. It should perhaps be in supplemental information.
2. Did the counting method used to collect data in Figure 4B exclude nuclei that rupture multiple times? This should be specified in the manuscript.
3. This statement should be rephrased: "Since transcription is needed to form and stabilize nuclear blebs, at least some aspect of nuclear shape deformations appears to be non-mechanical" - deformation in the model in Figure 7 is clearly 'mechanical' - driven by motor force.
4. It is important to specify the times for which cells were treated with the various drugs in each figure (and not just in figure 2).

Significance

This paper reports new data that nuclear blebbing induced by treatment with valproic acid can be inhibited by co-treatment with alpha-amanitin. The data provided are reproducible across different cell lines. The data suggest that inhibition of transcription inhibits blebs which are induced by valproic acid treatment, but it does not inhibit blebs in cells untreated with valproic acid. Immunostaining reveals some enrichment of RNA pol II phosphorylated at Ser5 in valproic acid-induced blebs, suggesting an enhancement of transcription-initiation (but not transcriptional elongation) in the bleb. Alpha-amanitin treatment reduces bleb formation and bleb lifetime.

While the data are clearly presented, and interesting in terms of relating transcription to blebbing, the proposed interpretation in terms of a new mechanism of blebbing is not strongly supported by the data or by the computational model. More definitive evidence is required to rule out that blebbing in valproic acid treated cells is not caused by a pressurization of the nucleus due to valproic acid treatment, which could be released by treatment with alpha-amanitin treatment for upto 24 h. The manuscript generalizes the findings to 'nuclear shape', and interprets them as suggestive of an alternative mechanism of establishment of nuclear shape; this generalization seems unsupported by the data.

Overall, the data provided is novel and interesting to cell biologists, provided more definitive evidence can be provided to rule out other models and to establish the new proposed model for nuclear blebbing. Else, the claims of an alternative mechanism for blebbing could be toned down, and the data on the relation between transcription and blebbing, which is the novel and interesting finding in this paper, could be presented in a more focused way.

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Referee #2

Evidence, reproducibility and clarity

The authors present data supporting the potential involvement of active transcription in the formation of nuclear blebs when the global deacetylase inhibitor valproic acid (VPA) has been applied to cells

Significance

The authors present data supporting the potential involvement of active transcription in the formation of nuclear blebs when the global deacetylase inhibitor valproic acid (VPA) has been applied to cells. While somewhat interesting, this is a rather specific condition that is further restricted by the limited use of experimental approaches. For example, the only deacetylase inhibitor used is VPA. Is this because VPA is the only one to trigger the effect? The authors should expand their approach to include additional inhibitors or, preferably, a directed knockdown tactic that targets the specific HDACs driving their phenomena. Moreover, the authors imply that VPA works through histone deacetylation yet do not provide direct evidence. It is equally likely that the application of VPA alters the acetylation pattern of a non-histone protein that eventually alters nuclear blebbing. Regardless, the reported findings with VPA were previously reported (Stephens et al. 2018) and the influence of alpha amanitin only represents an incremental advancement in our understanding of nuclear blebs. Adding to the concern is that actinomycin D does not have the same level of influence as alpha amanitin (Figure 2), which suggests the alpha amanitin is having a pleotropic impact on blebbing. To validate that the changes in blebbing in the presence of VPA are dependent upon active transcription, the authors should use the anchor-away technique to remove RNAP from the nucleus thereby avoiding any indirect effects of the drugs (i.e., alpha amanitin) in use. Further adding concern that it is an indirect outcome is the prolonged incubation period (16-24 hours) that is apparently needed to observe the changes (page 5 paragraph 4). If it is active transcription that is causing the change in blebbing, then this should be apparent in a much shorter time frame (<1 hour). In addition to these issues, the authors rely on immunofluorescence signals to measure the levels of various factors including the Ser5 and Ser2 phosphorylation, which is capturing the total levels of these factors and not the DNA bound forms. If the changes in blebbing actually involve transcription initiation, then the authors should include measurements on the DNA-bound factors. As reported the authors conclude that there is no changes in Ser2 and Ser5 phosphorylation yet they report that total RNA levels rise (Figure 1). How is the disconnect between RNA levels and Ser2 and Ser5 phosphorylation occurring? Comparably, they use H3K9ac immunofluorescence as a measure of euchromatin. While the authors might be gaining a view on the total levels of H3K9ac under these experimental conditions, it is not clear whether this is DNA associated or not. Minimally, the authors should perform ATAC-Seq to judge the changes in euchromatin. A final major concern is the lack of a correlation between the blebbing and nuclear ruptures (page 7 paragraph 3; Figure 4). If ruptures are not correlating with the blebbing, what is the relevance of the blebbing?

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Referee #1

Evidence, reproducibility and clarity

Summary: In this manuscript by Berg et al the authors demonstrate that RNA polymerase activity is important for the formation of nuclear blebs. This is an interesting and significant finding because prior work has suggested nuclear bleb formation is a result of changes in nuclear rigidity (lamins) or chromatin (via histone modifications). Overall I thought the manuscript was quite interesting and the data well presented. I think the inclusion of multiple mechanisms of blebbing (VPA treatment, as well as lamin B KO) helps to further support the importance of RNA polymerase/transcription activity in the blebbing process. However, I do have some concerns regarding the conclusions of the data that I think should be addressed as a revision.

Major Comments:

1. One concern I have is that the alpha-amanitin inhibitor has been shown to also inhibit RNA polymerase III. In an old study (1974 Weinmann PNAS) it appears that the inhibitor starting at 1 to 10 ug/ml. In this study the authors are using 10 uM alpha-amanitin, which is ~ 9 ug/ml and within the range of inhibiting some RNA polymerase III. Additionally, the other drug (actinomycin D) is even less specific for RNA polymerase II. I would suggest that the authors consider one of the following approaches 1) acknowledge in the manuscript the potential for RNA polymerase III to be important in the blebbing process 2) try a 10-fold lower dose of alpha-amanitin and see if that also inhibits blebbing, 3) try to find a way to demonstrate that RNA polymerase III activity is not inhibited at the 10 uM alpha-amanitin dosage, or 4) consider an alternate method to perturb RNA polymerase II activity (see Zhang Science Advances 2021 for an auxin-based approach to downregulate RNA polymerase II).
2. A second concern I have is that the inhibition of RNA polymerase is global. Thus it is difficult to know for sure the biophysical function of the polymerase occurs immediately at the bleb, or instead is somehow affecting the overall chromatin state throughout the entire nucleus. I agree that figure 3 does provide some evidence that major mechanical and biophysical properties of the nuclei are not changed in response to the inhibition of the polymerase. However, micromanipulation experiments are done with isolated nuclei, which may be somehow mechanically altered already by isolation from cells. I feel that there still must be given some consideration in the discussion of the possibility that RNA polymerase activity outside of the bleb may be having some role in the stabilization of the chromatin and blebbing propensity.
3. While I lack expertise to evaluate the basis of the model, I appreciate the model can show that motor activity can influence bulge. But it is not clear in the manuscript that RNA polymerase can generate these kinds of forces. The Liu citation is a model, and does not provide direct evidence that the RNA polymerase can generate force, or forces large enough to be meaningful. To me the model in this paper (Figure 7) felt as if it was only a possible hypothesis of why the RNA polymerase has an effect on blebbing, but I imagine there could be other hypotheses that would cause the same effect. The authors state (in the abstract) that RNA pol II can generate active forces, but I am concerned this is not sufficiently established. Since this motor/force activity of RNA polymerase is not not experimentally demonstrated in this paper the authors should either do a better job of including evidence of this from the literature or consider removing this part of the manuscript.

Minor Comments:

1. Did the authors do any analysis to see if the increased RNA transcription with VPA treatment (Figure 1B) has any spatial relationship to where the bleb occurs? Could an analysis of this be done similar to Figure 6 (with a bleb/body ratio)?
2. Is there anything known about lamin B1 KO cells as to whether or not they have increased transcription? Or could the authors do an analysis like they did with VPA treatment to check this? If they were to have increased transcription this would further support the authors' proposed mechanism of transcription itself (or RNA polymerase activity) driving blebbing).
3. Figure 1D, the VPA ser2 image appears much brighter than the untreated image. Yet the graph shows they are similar. Perhaps a more representative image should be used?
4. Can the authors comment if there is less DNA at the bleb site? In Figure 6 A this appears to be the case (based on the VPA image). If true, is the alpha-amanitin treatment rescuing this such that there is more DNA at the bleb (maybe causing the bleb to be smaller?).
5. What is the significance of bleb vs non-bleb nuclear rupture? Is there anything known in the literature as to how these ruptures may be different in terms of biophysics, impact to DNA, repair? It would be helpful to have some context, as well as to understand if non-bleb rupture is something that may have been previously missed in other contexts.

Significance

General assessment:

This study is a careful analysis of how RNA polymerase inhibition reduces nuclear blebbing. The study demonstrates this very well, using a variety of approaches. However, some limitations are the overstatement of some conclusions (specifically that it is RNA polymerase II when the inhibitor may also affect RNA polymerase III; that the RNA polymerase activity is important at the bleb and involves motor activity).<br /> Advance: This paper is a significant advancement because it shows the role of transcription in the biophysics of the nuclear shape. To my knowledge this is the first report of this phenomena, and thus will be impactful to the nuclear mechanics field. Audience: I think the findings are of broad interest, including beyond the nuclear mechanics field. I think the audience would be the entire cell biology community. Expertise: My expertise is in cell mechanics, including forces at the the nuclear LINC complex. While I do not work in the field of nuclear blebbing and rupture, I follow this field quite closely.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their positive statement and the significance of our work.

2. Point-by-point description of the revisions

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

This paper contains a set of highly valuable information on the physicochemical parameteters of betain lipids - which are synthesized in microalgae and some other lower eukaryotic organisms.

The authors, using advanced biophysical techniques - neutron diffraction and small-angle scattering (SANS) as well as molecular dynamics (MD) simulations - established key physicochemical parameters of synthetic betaine lipid DP-DGTS, and compared it with those of the DPPC phospholipid. They "show that DP-DGTS bilayers are thicker, more rigid, and mutually more repulsive than DPPC bilayers". These are important findings.

The authors also analyzed the phylogenetic tree of the appearance and disappearance of DGTS biosynthesis enzymes, which - together with the observed "different properties and hydration response of PC and DGTS" led them to explain "the diversity of betaine lipids observed in marine organisms and for their disappearance in seed plants". The authors tentatively suggest "A physicochemical cause of betaine lipid evolutionary loss in seed plants" (Title with "?")

We put a question mark because our work suggests that the difference of sensitivity to hydration between DGTS and PC bilayers could be an explanation for the betaine lipid disappearance in seed plants due to the dry stage of the seed. In our hands, we never managed to obtain 35S-BTA1 overexpressing plant that produce seed. However, we do not have a formal evidence for this fact. We propose to change the title into: “The possible role of lipid bilayer properties in the evolutionary disappearance of betaine lipids in seed plants.”

May major concerns with this suggestion are:

• In thylakoid membranes (TMs) the only phospholipid, PG, plays key roles in PSII and PSI functions (Wada and Murata 2007 Photosynth Res, Hagio et al. Plant Physiol 2000, Domonkos et al. 2004 Plant Physiol; it is difficult to explain how these roles would be overtaken by betaine lipids. In fact, data of Huang et al. (https://www.sciencedirect.com/science/article/pii/S2211926418309366) indicate betaine lipids constitute the major compounds of non-plastidial membranes" and compensation mechanism operate according to which "by the increase of PG in thylakoid membranes, suggesting a transfer of P from non-plastidial membranes to chloroplasts that would maintain a stable lipid composition of thylakoid membranes".
• Although neutron diffraction and SANS data, as well as MD simulationa might indicate important differences, the behavior of membranes (e.g. stacking interactions, overall structure and structural dynamics of TMs, protein embedding conditions / membrane thickness etc), TMs are more dominantly determined by protein-protein interactions, mainly because these membranes, contain only small areas occupied by the bilayer phase. Similar arguments hold true for the inner mitochondrial membranes (IMMs). I suggest to take into account these severe limitations when extrapolating the data and trying to reach general conclusions. In general, I suggest a more cautious interpretation of data.

We fully agree with the reviewer’s comments. We indeed wrote in the introduction: “In algae, under phosphate starvation, a situation commonly met in the environment, betaine lipids replace phospholipids in extraplastidic membranes. Because betaine lipids are localized in these membranes [11, 12] and share a common structural fragment with the main extraplastidic phospholipid phosphatidylcholine (PC) (Figure 1A and B), it can be speculated that these two lipid classes are interchangeable, but this was never demonstrated.”

Plastidial membranes are mainly composed of the non-phosphorus glycerolipids MGDG, DGDG and SQDG. It is well known that in phosphate starvation, in plants and algae, the main phospholipid present in thylakoid membranes, PG, is replaced by SQDG because they are both anionic and bilayer forming lipids (Hölzl G, Dörmann P. Chloroplast Lipids and Their Biosynthesis. Annu Rev Plant Biol. 2019 Apr 29;70:51-81. doi: 10.1146/annurev-arplant-050718-100202; Endo K, Kobayashi K, Wada H. Sulfoquinovosyldiacylglycerol has an Essential Role in Thermosynechococcus elongatus BP-1 Under Phosphate-Deficient Conditions. Plant Cell Physiol. 2016 Dec;57(12):2461-2471; Van Mooy BA, Rocap G, Fredricks HF, Evans CT, Devol AH. Sulfolipids dramatically decrease phosphorus demand by picocyanobacteria in oligotrophic marine environments. Proc Natl Acad Sci U S A. 2006 Jun 6;103(23):8607-12.; Kobayashi K, Fujii S, Sato M, Toyooka K, Wada H. Specific role of phosphatidylglycerol and functional overlaps with other thylakoid lipids in Arabidopsis chloroplast biogenesis. Plant Cell Rep. 2015 Apr;34(4):631-42.). We recently showed by the same kind of neutron diffraction approaches that PG and SQDG share similar physicochemical properties that can explain their conserved replacement by each other in plastidial membranes (Bolik S, Albrieux C, Schneck E, Demé B, Jouhet J. Sulfoquinovosyldiacylglycerol and phosphatidylglycerol bilayers share biophysical properties and are good mutual substitutes in photosynthetic membranes. Biochim Biophys Acta Biomembr. 2022 Dec 1;1864(12):184037. ). However, nothing is known about mitochondrial membranes and DGTS localization. Because PC is a major lipid component of mitochondria in plants and fungi and PC is absent in Chlamydomonas reinhardtii, mitochondria membranes could contain DGTS at least in Chlamydomonas.

To clarify this statement, we added in the introduction the sentences: “Betaine lipid synthesis is located in the ER [13,14] and betaine lipids are expected to be absent in photosynthetic membranes [12]. Therefore, this PC-betaine lipid replacement is not expected to occur in photosynthetic membranes. However, it might occur at the surface of the chloroplast envelope where PC might be present [15–17]. Nothing is known about the composition of mitochondrial membranes in algae but because PC is a major lipid component in plant and fungal mitochondria, this replacement might also occur in mitochondria.” In the discussion, we replaced “cellular membrane” with “extraplastidial membrane”.

A minor point - just to avoid possible misunderstanding: betaine can be present in large quantities in many photosynthetic organisms. A short statement on betaine would help.

To avoid any confusion with betaine as a soluble molecule and betaine lipid, we added this sentence in the introduction: “The presence of betaine lipids is not linked to the synthesis of betaine, a soluble compound present in almost every organism including most animals, plants, and microorganisms, acting as protectant against osmotic stress [22].”

**Referee cross-commenting**

I agree with the evaluation of Reviewer #2 - while keeping mine

Reviewer #1 (Significance (Required)):

The physico-chemical properties of betaine lipids have not been established. These lipids - under P starvation of microalgae - accummulate in large quentites. Thus, their detailed characterization and comparison to (otherwise similar) phospolipids are of high importance and advance our knowledge about the roles of these lipids and the organization and structural / functional plasticity of biological membranes.

As outlined above, I suggest a more cautious interpretation of the data and conclusions regarding e.g. the energy-converting membranes.

I think the audience is relatively broad: (i) basic research of lipid models and (ii) methodology as well as calling the attention of membrane biologists to the scarcely studied betaine lipids.

My field is the biophysics photosynthesis - the stability and plasticity of the oxygenic photosynthetic machinery at different levels of complexity; the and closest to this topic is the polymorphic lipid phase behavior of plant TMs.

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

This manuscript nicely presents the effect of phosphate depletion on how betaine lipids function as effective replacements in a water-rich environment. The mix of computational and wet lab experiments provides details on membrane structure and general effects when phospholipids are changed to betaine lipids. I found this manuscript easy to read and understand and is worthy of publishing. However, I do have a few minor comments below to improve the manuscript.

Minor Comments:

1. Phases in PC lipids with saturated tails: The authors present a gel to liquid crystalline phase change for DPPC at 40oC. However, this is at the ripple-liquid crystalline phase transition and the gel doesn't occur until about 34-35oC. This should be noted in the manuscript.

We indeed completed the sentence in the first result section by : “The DSC data show a sharp phase transition at 40.2 ± 0.1°C for DPPC corresponding to the transition between the ripple phase and the fluid phase, which is consistent with earlier reports on DPPC large unilamellar vesicles [25].”

Page 4: I am confused with the following phase: "indicating either weak cooperativity between lipid bilayers or that phase co-existence is not a thermodynamic disadvantage, while this phenomenon is not observed for DPPC bilayers." What is meant by phase co-existence is not a thermodynamic disadvantage? Could this also be due to some frustration in phase coexistence and the presence of a ripple phase that kinetically is inhibited and thus a sharp transition is not observed?

We did not observe a ripple phase in DP-DGTS as it is defined in DPPC bilayer either by DSC, neutron diffraction or SANS experiments. We don’t know if it exists in DP-DGTS bilayers. What we observe in neutron diffraction is a coexistence of gel phase and fluid phase domains in oriented multilayer films of DP-DGTS over a wide range of humidity whereas for DPPC we observe only a gel phase or a fluid phase. Because the thicknesses of the DP-DGTS bilayers are not so different between the gel phase and the fluid phase, we suppose that the free energy difference between the two phases is very small over a wide osmotic pressure range and that could explain the broad phase transition.

To further clarify our point, we have reworded the sentence in the following way: “As seen in Figure 2A , by increasing the humidity, DPPC molecules transit from the gel to the fluid phase via a ripple phase through a narrow window of osmotic pressures as previously reported [30,31]. In contrast, DP-DGTS bilayers show a phase coexistence that can be observed over a wide P-range and without the appearance of a third phase that could be attributed to a distinct ripple phase (Figure 2B) before forming a single fluid phase at high humidity (i.e., at low P). Based on DSC and neutron diffraction as two independent techniques, we can safely conclude that the phase transition for DP-DGTS is broad. This observation indicates that the free energy difference between the two phases is very small over a wide osmotic pressure range and may be connected to the shapes of the pressure-distance relations in the two phases, which are discussed further below.” We also added in the legend of figure 4 (SANS experiment): “No ripple phase Pb was detected for DP-DGTS bilayers.”

DOI for computational methods: The DOI listed computational files (https://doi.org/10.18419/darus-2360) does not work.

Unfortunately, we did not ask for publication of the URL upon submission of the manuscript and thank the reviewer for carefully checking this. Since DaRUS is a peer-reviewed repository ensuring high quality data sets according to the FAIR principle, peer review is still ongoing. The provided link will work definitely only when the manuscript will be published. In the meantime, we provide a temporary link for reviewing :

https://darus.uni-stuttgart.de/privateurl.xhtml?token=cbfac341-0e4a-4403-8f73-87bce31ca805

Reviewer #2 (Significance (Required)):

This work has broad significance and would be of general interest to those in membrane biophysics to plant biology and evolution. The work nicely touches on all these topics, and I find this fills a gap in details of these betaine lipids structure and relation to evolution in terrestrial vs. marine plants.

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Referee #2

Evidence, reproducibility and clarity

This manuscript nicely presents the effect of phosphate depletion on how betaine lipids function as effective replacements in a water-rich environment. The mix of computational and wet lab experiments provides details on membrane structure and general effects when phospholipids are changed to betaine lipids. I found this manuscript easy to read and understand and is worthy of publishing. However, I do have a few minor comments below to improve the manuscript.

Minor Comments:

1. Phases in PC lipids with saturated tails: The authors present a gel to liquid crystalline phase change for DPPC at 40oC. However, this is at the ripple-liquid crystalline phase transition and the gel doesn't occur until about 34-35oC. This should be noted in the manuscript.
2. Page 4: I am confused with the following phase: "indicating either weak cooperativity between lipid bilayers or that phase co-existence is not a thermodynamic disadvantage, while this phenomenon is not observed for DPPC bilayers." What is meant by phase co-existence is not a thermodynamic disadvantage? Could this also be due to some frustration in phase coexistence and the presence of a ripple phase that kinetically is inhibited and thus a sharp transition is not observed?
3. DOI for computational methods: The DOI listed computational files (https://doi.org/10.18419/darus-2360) does not work.

Significance

This work has broad significance and would be of general interest to those in membrane biophysics to plant biology and evolution. The work nicely touches on all these topics, and I find this fills a gap in details of these betaine lipids structure and relation to evolution in terrestrial vs. marine plants.

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

This paper contains a set of highly valuable information on the physicochemical parameteters of betain lipids - which are synthesized in microalgae and some other lower eukaryotic organisms.

The authors, using advanced biophysical techniques - neutron diffraction and small-angle scattering (SANS) as well as molecular dynamics (MD) simulations - established key physicochemical parameters of synthetic betaine lipid DP-DGTS, and compared it with those of the DPPC phospholipid. They "show that DP-DGTS bilayers are thicker, more rigid, and mutually more repulsive than DPPC bilayers". These are important findings.

The authors also analyzed the phylogenetic tree of the appearance and disappearance of DGTS biosynthesis enzymes, which - together with the observed "different properties and hydration response of PC and DGTS" led them to explain "the diversity of betaine lipids observed in marine organisms and for their disappearance in seed plants". The authors tentatively suggest "A physicochemical cause of betaine lipid evolutionary loss in seed plants" (Title with "?")

May major concerns with this suggestion are:

• (i) In thylakoid membranes (TMs) the only phospholipid, PG, plays key roles in PSII and PSI functions (Wada and Murata 2007 Photosynth Res, Hagio et al. Plant Physiol 2000, Domonkos et al. 2004 Plant Physiol; it is difficult to explain how these roles would be overtaken by betaine lipids. In fact, data of Huang et al. (https://www.sciencedirect.com/science/article/pii/S2211926418309366) indicate betaine lipids constitute the major compounds of non-plastidial membranes" and compensation mechanism operate according to which "by the increase of PG in thylakoid membranes, suggesting a transfer of P from non-plastidial membranes to chloroplasts that would maintain a stable lipid composition of thylakoid membranes"
• (ii) Although neutron diffraction and SANS data, as well as MD simulationa might indicate important differences, the behavior of membranes (e.g. stacking interactions, overall structure and structural dynamics of TMs, protein embedding conditions / membrane thickness etc), TMs are more dominantly determined by protein-protein interactions, mainly because these membranes, contain only small areas occupied by the bilayer phase. Similar arguments hold true for the inner mitochondrial membranes (IMMs).

I suggest to take into account these severe limitations when extrapolating the data and trying to reach general conclusions. In general, I suggest a more cautious interpretation of data.

A minor point - just to avoid possible misunderstanding: betaine can be present in large quantities in many photosynthetic organisms. A short statement on betaine would help.

Referee cross-commenting

I agree with the evaluation of Reviewer #2 - while keeping mine

Significance

The physico-chemical properties of betaine lipids have not been established. These lipids - under P starvation of microalgae - accummulate in large quentites. Thus, their detailed characterization and comparison to (otherwise similar) phospolipids are of high importance and advance our knowledge about the roles of these lipids and the organization and structural / functional plasticity of biological membranes.

As outlined above, I suggest a more cautious interpretation of the data and conclusions regarding e.g. the energy-converting membranes.

I think the audience is relatively broad: (i) basic research of lipid models and (ii) methodology as well as calling the attention of membrane biologists to the scarcely studied betaine lipids.

My field is the biophysics photosynthesis - the stability and plasticity of the oxygenic photosynthetic machinery at different levels of complexity; the and closest to this topic is the polymorphic lipid phase behavior of plant TMs.

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Reply to the reviewers

Our reply to reviewers contain figures that has been uploaded as a word file with the rest of the files. Here, we cannot past figures into the reply box, and because we don't wish to submit an incomplete response, we cannot provide a response in this format.

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Referee #2

Evidence, reproducibility and clarity

Lateral root production is a process regulated by auxin, among others. The expression of auxin-dependent genes requires the activity of transcription factors of the ARF family. In this study by Ebstrup et al., the authors suggest that selective autophagy would be involved in the degradation of the ARF7 factor involved in lateral root initiation and production in Arabidopsis thaliana, even though the accumulation of ARF7 in autophagy-deficiency mutant may not affect lateral root initiation.

Major remarks and comments:

1. In general, some experimental data do not facilitate appropriate comparisons due to lack of statistical analysis. This is particularly the case for Figures 1-a,b,c and 4-a,b,c,d.
2. Confocal microscopy images are not always convincing, due to a lack of necessary controls and also qualitatively. It would be useful, for example, to clearly indicate the objects of interest that the reader can use for comparisons. It is for example difficult to understand that chlorophyll fluorescence and GFP fluorescence (from the BiFC signal) colocalize almost in the same organelles (fig. 2c). The parent lines expressing the Venus and mCherry fusions should also serve as controls for figure EV3. Another point concerning fig. 2 a, b (IP): how do the authors explain the "GFP" signal, especially the apparent size and the doublet present only in one of the "YFP" controls after IP?
3. It would be important for the authors to clarify whether the different fluorescent fusions used are indeed functional or not. This is particularly important in the context of the proteins being studied and the possible regulatory process(es).
4. Apparently ARF7 would be degraded by the UPS system and the selective autophagy pathway. Would autophagy-deficient mutants, including atg2-1 and atg5-1 be more or less sensitive to MG132 (relative levels of ARF7 accumulation)? This is not clear from the data and its discussion.
5. The authors seem to insist that NBR1-mediated degradation of ARF7 by selective autophagy would be observable only preferentially in mature root tissues (probably to prevent them from forming lateral roots?). If this is the case, the title of their paper should reflect this conclusion. The authors have the tools (described in their manuscript) to unambiguously clarify this important point. Just as it would be important to demonstrate that the ARF7 proteins that accumulate would indeed be ubiquitylated.

Minor comments:

1. Some of the figures would benefit from qualitative improvement, especially the photographs and micrographs.
2. The authors' attention is drawn to the existence of several typos in the text and the absence of certain references cited in the bibliography.

Significance

Although the biological question is of unquestionable interest and importance, the data presented in this manuscript unfortunately do not allow us to rightly assess the contribution of this work to the state of our knowledge.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This manuscript shows the involvement of both the proteasome and autophagy pathways in the turnover and therefore regulation of ARF7, an auxin-responsive factor involved in lateral root formation. The authors bring crucial information for the understanding of how autophagy is involved in auxin-signaling.

Major comments:

The key conclusions appear overall convincing yet this reviewer would strongly advise to take into account the following remarks for a clearer and more convincing line of inquiry. This reviewer also believes that the additional experiments could be performed relatively fast apart for the point 9) where the establishment of a homozygous line could take 6 months or more.

1. Figure 1 & Figure EV1: The nature of the loading control should be stated as it appears to be a specific protein detected by immunoblotting. Furthermore, if the authors wish to make a stronger point as to whether ARF7 is degraded by the proteasome (considering the reserves mentioned in the Discussion section), I would recommend to perform the same assays as in Figure 1 but using an alternative proteasome inhibitor such as Bortezomib and to include a proteasome subunit KO mutant such as rpt2a-2.
2. The statement "The experiment revealed that both NBR1 (Fig 2A) and ATG8a (Fig 2B), but not free YFP, co-immunoprecipitated with ARF7-Venus." Is false as the authors did not try to co-immunoprecipitate free YFP with ARF7-Venus, they used a free YFP expressing line as a negative control for their GFP-immunoprecipitation (IP). It should further be noted that although NBR1 is detected in their free YFP IP, ATG8 is at very low levels so it should be stated that they see an enrichment of ATG8 in their ARF7-Venus IP.
3. Authors state "we were unable to detect ARF7-Venus in the input of both Co-IPs which can likely be explained by the fact that ARF7-Venus is under the control of its native promoter and thus lowly expressed.", yet putative degradation products (i.e. a smear) can be observed in the input of Figure 2A, similarly to the bands observed in both IP blots. It would be interesting to repeat these co-IPs with proteolysis inhibitors such as MG132 or Pepstatin & E64-d to pinpoint the proteolytic machinery at the origin of ARF7-Venus degradation in the IPs.
4. Figure 2: The use of multicolor BiFC "mcBiFC" should be stated as such for an easier understanding of the reader. It would be helpful for the reader if the "GFP" signal resulting from the complementation would be highlights thanks to some arrows. Moreover, a western blot to verify the expression levels should be performed since every construct has an epitope tag as stated in Gehl et al. 2009.
5. General remark: all drug/chemical treatments performed in this study use a "non-treated" negative control, yet it should be pointed out that the correct corresponding negative controls should have the solvent used to dissolve the respective drug/chemical in order to exclude any effect of the solvent or vehicle.
6. Figure 4, Figure EV4: Considering the variability in size and staining of the Rubisco large-subunit in the 4 immunoblot panels, I would suggest blotting with another antibody such as anti-tubulin or anti-histone 3 as a loading control for a more convincing quantification. Moreover, the nature of the staining used to stain the Rubisco large-subunit should be stated. The authors also state "differences in ARF7 accumulation in atg5 compared to Col-0" yet no immunoblot is shown where both genotypes are present on the same membrane, in order to verify this statement.
7. Figure 5: In regards to LR density measurements, I recommend reading "Quantitative Analysis of Lateral Root Development: Pitfalls and How to Avoid Them" by Dubrovsky & Forde (Plant Cell, 2012) for a more robust method of evaluating lateral root density.
8. Discussion: The authors state that "autophagy blockage leads to increased ARF7 cytoplasmic condensates". To support this statement, I recommend crossing pARF7::gARF7-Venus into atg mutants and analysing the localization and the fluorescence intensity of ARF7-Venus in specific parts of the root, as well as performing immunoblotting in order to assess overall ARF7 accumulation in autophagy deficient genetic backgrounds.

Minor comments

1. The following statement: « In contrast, plants are able to tolerate disruption of autophagy activity without major penalties" holds true to A. thaliana of some other plants but it must be noted that in O. sativa, autophagy-deficiency may lead to male sterility, which should be considered a major penalty for evolutionary fitness. For review see Norizuki et al. 2020 (Front. Plant Sci.).
2. Figure 2: The molecular weights appear to be potentially misannotated as free YFP aligns with the 35 kDa marks although it should appear around 27 kDa.
3. Figure EV3: There are 2 merged image columns, the furthest one to the right appears to include a DIC or Trans image on top of both fluorescence channels. It would be more helpful for the reader if the DIC or Trans image was shown with the overlay of fluorescent channels in order to assess the effect of 10% 1,6-hexandiol on the plant tissue. Moreover, demonstrating the absence of tissue damage or cell-death after 1,6-hexandiol treatment would be a plus.
4. There is a typo throughout the manuscript: ZT should be "Zeitgeber" not "zeitberg".

Significance

This manuscript has the quality of describing the proteolytic balance of ARF7 and thereby, the involvement of the autophagy pathway in regulating auxin-signaling components. This research adds on to the growing interest in how autophagy participates in developmental cues, and how hormonal signaling is regulated throughout the plant.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors performed an arrayed CRISPR loss-of-function screen targeting 18,253 genes with the goal of uncovering gene products that regulate cytoplasmic dynein-1 motor function. In order to assess the impact of gene knockout, the authors optimized a protocol for transfecting pools of cells with mRNA encoding Cas9 and scalably delivering arrayed pools of synthetic guides targeting a single gene to knock-out. In order to link gene knockouts to dynein-1 function the authors employed (1) a previously developed cell model U-2 OS PEX and (2) anti-EEA1 and anti-a-Tubulin antibodies and (3) hoechst as high-content fluorescent readouts for their genome-wide screen.

The authors then picked a subset of genes to move forwards with that were deemed as hits. A secondary round of screening was performed on these hit genes and unsupervised phenotypic clustering was performed on the feature vectors derived from the high-content images. These analyses revealed several distinct phenotypic clusters that can be categorized by the dynein cargoes or other functional categories including proteostasis related functions. The authors identified the gene SUGP1, which has never previously been linked to dynein-dynactin functionality.

The authors then show that targeting SUGP1 reduces the mRNA of both LIS1 and DYNC1l2 and the subsequent protein abundance of only LIS1.

In summary, the authors provide an optimized method for performing what they have termed 'one-shot' genome wide arrayed screening with pools of synthetic guides. They additionally have generated a data resource for others interested in understanding early endosome pathways and dynein-dynactin functionality.

The technical feat of generating such a large dataset and optimizing the protocol for arrayed synthetic guide pools will undoubtedly be useful for the community. However, this work has several limitations including (1) lack of adequate documentation for reproducing the analyses and (2) minimal mechanistic insight into the function of SUGP1.

Major Comments:

• The authors do not provide code or even pseudocode for the algorithms used to generate the features from the high-content images. If the authors are claiming that this would be a resource for the community to use then the authors need to provide an easy way for others to recreate their analysis.
• The authors mention that they will make the images from their screen publicly available, which is an essential part of making their work a useful resource for the community. However, more details need to be provided about how they will share the results. While a "data dump" of images will be useful to a narrow group of computationally savvy scientists, the broader community will require an interactive interface to enable browsing of the data. The authors should establish such a platform and make it available to reviewers of the revised manuscript to evaluate its usefulness.
• The authors highlight SUGP1 as an example for "novel mechanistic insights" - but the insights they provide are really minimal. If they authors want to claim mechanistic insights, they should experimentally address questions such as: Does SUGP1 physically interact with LIS1 mRNA? Which region of LIS1 mRNA confers regulation by SUGP1? Can the authors generate a version of LIS1 resistant to SUGP1 regulation to show that the effect of SUGP1 loss is mediated by LIS1 (and not additional factors?).

Minor Comments:

• Primary and Secondary antibody pairs are described nowhere in this paper. This would be impossible for anyone to recreate with just the list of primary and secondary antibodies used here.
• The authors provide no description of how the segmentation was performed or any reference to the code that they used for segmentation regarding the definition of perinuclear region. Considering so many of the results are based on these values it is important that others are able to recreate these values.
• Line 132: The authors do not explain what a min-max analysis is anywhere in the paper. This should be explained.
• There is no discussion of how the authors quantify micronuclei formation. If they state that they are the first to do this and that this is a novel technique they at the minimum need to explain the methods for quantifying micronuclei.
• Supplemental Fig 4C if a per cell intensity quantification is done I would like to see a metric for the segmentation accuracy on these cells overlaid with a cytoskeletal stain.
• It would be nice to have examples of nuclei or morphology that were excluded from downstream analysis, perhaps in a supplemental figure.
• Nowhere in the manuscript is it explained how the SUGP1 intensity measurement in Figure 6D is calculated, is this one a per well basis or a per cell basis?

Significance

The generation of the dataset described in this manuscript is impressive. However, to reach its full significance and usefulness for the scientific community, the authors should provide relevant technical details, in particular of their analysis pipeline, and share the screen results in an accessible, interactive interface. If they want to claim mechanistic insights into SUGP1, more mechanistic work is required.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript the authors have conducted a genome-wide CRISPR loss-of-function screen in human cells to find regulators of cytoplasmic dynein, a microtubule-based motor that plays a major role in the transport of cargo towards microtubule minus ends. The screen was carried out to address how dynein is synthesised and assembled, and how its activity is controlled to enable the motor to selectively transport a wide variety of cargoes. Cells were fixed cells 72 hours after transfection and fluorescently stained for intracellular markers. Several read-outs were used in the screen, of which the major ones were the distribution of dynein-tethered peroxisomes and early endosomes. The authors used a 384 well format (61 unique 384-well plates) and a fluorescence microscopy-based imaging readout to gauge dynein activity. From a guide RNA library targeting 18,253 genes, the authors recovered 195 validated hits. For one gene (SUGP1) follow-up studies demonstrate that the protein encoded by this gene controls the levels of the dynein activator LIS1 and thereby promotes cargo trafficking by dynein. The dataset reported here represents a source for investigating proteins that might be involved in minus-end microtubule-based transport, as well as in other aspects of cellular organisation that were captured in the high-content imaging approach.

I find this an interesting and well written resource manuscript, both from the perspective of how to conduct and analyse a high-content imaging screen, as well as from the dynein biology view. Results presented in this manuscript deserve follow-up studies. I do have a number of comments.

Major comments

1. On page 6 the authors state they used 61 x 384 wells. This equals 23,424 wells, but the authors state they analysed (8,150,065 cells from) 24,576 wells. What causes this difference in number? More importantly, the authors target 18,253 genes with four guides per gene. If I understand correctly these four guides per gene are present in a single well and the high-content imaging experiment was only done once. Although many cells were analysed per well (four fields of view per well; median of 345 cells analysed per well) and results are interesting and appear solid, I do think a replicate experiment is necessary.
2. The screen was developed based on the U-2 OS PEX line, in which tethering of dynein to peroxisomes is achieved by addition of rapamycin acting via a split BICD2 protein. Thus, the assay depends on the BICD2 adapter. Is this limiting when one is looking for dynein regulators?
3. Related to the question above, the authors do not recover BICD1 in their screen. Is this because BICD1 is not expressed in the cell systems used or is there another reaosn?
4. It has very recently been shown (doi.org/10.1038/s41467-023-38116-1) that BICD2 phosphorylation by CDK1 in the G2 phase of the cell cycle promotes its interaction with PLK1. This is followed by PLK1 phosphorylation in the N-terminus of BICD2, which in turn facilitates interaction with dynein and dynactin, allowing the formation of active motor complexes. Thus, adaptor activation through phosphorylation regulates dynein activity. In the present manuscript the authors use PLK1 as a read-out of cell viability. However, PLK1 also appears to regulate dynein via BICD2 phosphorylation. Given the latest results would the authors interpret their PLK1 data differently? Would it be preferable to screen for regulators of dynein activity in non-dividing cells?
5. Using the 377 genes listed in Supplementary Table 4 I performed a Metascape analysis. The results suggest that many of the hits are proteins involved in RNA metabolism or the cell cycle and that many of the encoded proteins form complexes. Based on this I wonder whether the screen yielded many proteins that are involved in controlling the steady state levels of dynein, microtubules, or of the dynein regulators. SUGP1 is an example of this. I suggest that the authors include an extensive Metascape analysis in a new version of the manuscript.
6. On page 11 a UMAP plot is described, which is shown in Figure 4B. How were the "members of the same protein complexes, such as histones, ribosomal proteins, RNA polymerase II, the RUVBL and TRiC/CCT chaperonins, FAM160A2- AKTIP-HOOK3 and dynein-dynactin" identified?
7. How do the complexes identified in Figure 4B relate to the MCODE-based complexes identified in Metascape?

Significance

I think the present manuscript is an interesting resource paper for the dynein community. The advance is technical rather than conceptual.

I am a cell biologist with an interest in microtubules and how this cytoskeletal network controls cell shape and function. I analyse this using fluorescence microscopy and -omics approaches. I am not an expert in high-content imaging screens and analyses but the data presented here seem solid and novel to me.

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Referee #1

Evidence, reproducibility and clarity

Cytoplasmic dynein-1 (dynein) is the predominant minus-end directed microtubule-based motor involved in the transport of numerous cellular cargoes in addition to mitotic functions. Although in vitro analysis of dynein assembly and interactions are becoming more common, cell biological studies that aim at identifying different dynein cargoes and functions are lacking. To shed light on dynein's function, Wong et al., performed a genome-wide CRISPR loss-of-function screen using peroxisome-tethered and endosome localization assays as readouts. Detailed data analysis and supervised and unsupervised phenotypic clustering of targets from an extensive RNA gene library (~20,000 genes) revealed ~200 genes disrupted in cargo trafficking processes. The authors also showed that a novel gene SUGP1, identified in their screen, promotes the expression of a critical dynein activator, LIS1. The generated datasets provide a rich library of genes that can be further mined by other researchers in the field.

Major comments:

This manuscript reads well, and the conclusions are mostly supported by experimental data. The authors went to great lengths to optimize their high throughput assay setup by testing different cell lines and transfection conditions and included different positive and negative controls, which is a strength of the study. The use of two functional readouts (early endosome and BICD2-driven peroxisome distribution) in the initial screen followed up by a validation screen of a smaller subset of genes using readouts for dynein disruption phenotypes (Golgi fragmentation, lysosome clustering) is another strength. In addition, the follow-up identification of an RNA-binding protein SUGP1 as a regulator of LIS1 mRNA levels provides an interesting new way of regulating dynein function.

I have a few concerns about the experimental design and conclusions.

1. The images in Fig. 1E and 1G for the dynein control (crDYNHC1) show some clustering around the cell nucleus while crLIS1 knockout shows no perinuclear clustering. Is this expected? Shouldn't dynein knockout prevent perinuclear clustering? Is it possible that crDYNHC1 does not lead to a complete knockout? Given that this is a proof-of-principle control in the assay, a more detailed validation of DYNHC1 knockout using western blotting and RT-qPCR, in addition to the validation shown in Fig. 1C would strengthen the claim that this control works as expected. These experiments should be fast and easy to do.
2. The use of multiple crRNAs together to target a single gene can increase off-target effects, however, the authors never test for off-target phenotypes or address the possibility of off-targeting. Can the authors show using a few examples that their approach does not lead to significant off-targeting? This should also be addressed in the text.
3. It is unclear to me how the authors established the limits for the quantification of localization ratios. As described in methods, the perinuclear region was defined as having an outer limit of 7 μm from the nuclear envelope. However, the cells are not the same size (also seen in representative images), which could skew the calculation of ratios solely based on fixed distance limits. Have the authors considered taking into account cell size? Perhaps a more accurate calculation would be to measure the distance from the nucleus to the cell periphery for each cell and normalize this value to the cell size to account for cell size differences. The perinuclear region could then be defined as the percentage of the distance from the nuclear envelope of the normalized cell radius. It is also unclear how the size and intensity of each "spot" are accounted for in the analysis as this is an important aspect of the quantification given that the "spots" are not the same size/intensity. Redoing this analysis would not require the authors to collect any new data but could help in gene identification, especially given that the authors only identified ~50% of the known dynein-dynactin complex components to be disrupted in their assay. These genes might have more subtle phenotypes that could be amplified by doing more precise image analysis and quantification.

Minor comments:

1. It would be helpful if the authors could change gene names to a bold or brighter font in scatter plots in all figures. It is hard to read the names the way they are right now.
2. Line 185 the authors say: "We also analysed the induction of micronuclei (Supplementary figure 6B), which to our knowledge has not been assessed in earlier screens." What screens are the authors referring to? Could you add references here?
3. Line 256: "Each cargo was assayed in two independent screens, in which there was good agreement in general between the effects of the crRNA pools (Supplementary figure 8)." The authors also indicate in the legend for Supplementary figure 8 that "The only metric with a poor R2 score (proportion of cells with two γ- Tubulin puncta) was not used for hit calling." However, the EEA1 localization ratio also shows poor R2 score, shouldn't this screen also be excluded? In general, what was the cutoff for R2 score? This information should be included.

Significance

This work is the first genome-wide loss-of-function CRISPR study (to my knowledge) aimed at identifying dynein-driven trafficking disruption phenotypes. In general, the data generated in this study will enrich the field's understanding of how dynein is regulated and how it achieves its broad cargo and functional specificity.This manuscript will also provide a resource and experimental setup for the design of other genome-wide loss-of-function CRISPR studies.

I have broad expertise in the cytoskeleton field with a detailed understanding of dynein's function from a mechanistic and functional perspective. I have minimal experience with high throughput screening, but I am experienced with CRISPR-based assays and cell imaging techniques.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity____:

Summary: the paper suggested a new approach to study in vivo possible interaction between glioblastoma cells and glioblastoma associated macrophages. By using single cells transcriptome profiling and in vitro and in vivo functional experiments the authors also suggested LGALS1 as possible key factor in the suppression of the immune system and a new target for immune modulation in glioma patients. The experimental plan is well described, and the results are beautifully presented using images, clear drawings, and videos.

Major comments: none

Minor comments:

• The number of zebrafish embryos analyzed after the xenograft is highly variable (e.g. 3-18; 4-22 in Figure 6). These numbers can be reported in the results section (not only in the legends) and the authors may comment on them in the discussion. The reproducibility of thexenotransplant experiments is always challenging as it is quite difficult to inject the same number of cells in every embryo and to have the same survival rate of injected cells and of transplanted embryos. For these reasons the volume of each xenograft can vary significantly in different embryos and in different experimental session. Accordingly, the number of macrophages associated to the tumor can vary and the statistical analysis can be deeply influenced by the number of replicates for each experimental group (a group with 3 embryos is very different in term of quality and quantity of information in respect to a group of 18 embryos). It could be useful for the reader, who has no experience in this technique, be aware of the advantages and disadvantages of the procedure including the possible influence of the temperature (34°C instead of 37°C) on the embryo survival and the replication rate of glioma cells or macrophages behavior. Comment on these aspects does not weaken the power and the relevance of the model but unveil the critical aspects that every scientist has to evaluate before planning these kinds of experiments.

__Response: __We agree with Reviewer #1 that the zebrafish avatar model is challenging, and it is difficult to obtain reproducible tumor sizes and survival rates. To be even more transparent about this, we have added a few sentences about the variable n number in the Results section and a critical comment about it in the Discussion section.

• An aspect that could be interesting to address, to further validate the avatar model, is to monitor the level of pro-inflammatory cytokines (Tumor Necrosis Factor and Interleukin 1, 6, and 8) that are expressed at basal level in the early developing zebrafish embryos. Do their expression level increase after the xenotransplantation? Can the zebrafish cytokines affect the behavior of glioma associated macrophages (i.e. macrophages polarization)?

__Response: __This is an interesting point, indeed. We have injected murine melanoma (B16) cells into Tg(mpeg1:mCherry-F); Tg(TNFa:eGFP-F) embryos, a TNFa reporter line. Some (but not all) macrophages expressed TNFa and their expression decreased over time, which is consistent with previous reports (Póvoa et al, 2021). We further observed that TNFa-expressing macrophages mostly had a round, “tumor-attacking” phenotype. This is in line with our hypothesis that the tumor induces a phenotype switch in GAMs. Of note, we did not see TNFa expression in the rest of the brain tissue. We would be happy to add this data if deemed useful.

We did not investigate other cytokines in the developing zebrafish, but we believe this is not essential for the following reasons: We are mainly interested in the differences between the patient-derived GBM stem cell cultures (GSSCs), and since they are all used in the same avatar model, we expect that if zebrafish cytokines would have an effect on GAMs and their polarization, this effect would be consistent in all avatars, and can thus be ignored when comparing different GSCCs. More importantly, our findings in the zebrafish avatar model were consistent with those in the in vitro model. We observed the same phenotype switch in the co-culture model, indicating that the key interaction is between tumor cells and macrophages.

Significance____:

Strengths and limitation. The manuscript is the result of a well-orchestrated effort to dissect a biological problem by complementary approaches and provide new data with high impact translational value. The image processing pipeline developed by the authors is a step forward in the in vivo analysis of cells interaction in living embryos. The identification of LGALS1 as a potential target for immune modulation can support the development of new therapeutical strategy implementing chemo- or immunotherapy protocols. The described zebrafish avatar can represent a new tool for personalized drug testing recapitulating in a in vivo model the heterogeneity of GBM found in patients.

Audience: All the scientist interested in cell biology, cancer cell biology, imaging techniques, translational medicine, in vivo models for cancer research, precision medicine.

Reviewer expertise: applied developmental biology

Reviewer #2

Evidence, reproducibility and clarity____:

Finotto et al aim to address the polarisation of macrophages within GBM in their study. To do this, they have developed two different models. The first model is an in-vitro co-culture model of patient derived GSC lines and human monocyte derived macrophages. This model was used for single cell sequencing to understand the transcriptomic changes of macrophages upon contact to GBM cells. The second model is a zebrafish xenograft model. Here GFP labeled GBM cells were transplanted into the larval zebrafish ventricle. These experiments were done in the transgenic mpeg zebrafish which allowed to monitor responses of macrophages in vivo.

In my opinion both models are not sophisticated enough to draw solid conclusions on macrophage polarisation in GBM. The in vitro model is highly artificial and is far from the complex situation in GBM. Within GBM the GAM population represents a heterogenous mix of resident microglia and infiltrating macrophages. These are influenced by the heterogeneous environment (which consists of tumour cells but also other host cells) and show diverse transcriptomic adaptations as shown in rodent models as well as sequencing studies of patient derived tumour samples. Studying monocyte derived macrophages in vitro does not provide any reliable insight.

Response: We understand the reviewer’s concern about the complexity of our in vitro model. However, these simple models are needed to gain more insight into the complex in vivo situation. Others have demonstrated their usefulness in the past (C. Jayakrishnan et al, 2019; Zhou et al, 2022; Hubert et al, 2016; Chen et al, 2020; Coniglio et al, 2016; Li et al, 2022). Moreover, it may be advantageous to look at only two different cell types and unravel their reciprocal interaction, without the influence of other cell types, making it too complex to draw conclusions. We acknowledge that GAMs are a heterogeneous mix of both microglia and bone marrow-derived macrophages. Considering that bone marrow-derived macrophages have been shown to play an important role in tumor progression and are by far the most abundant immune cell population in GBM tumors (which even increases in recurrent GBM) (Pombo Antunes et al, 2021; Abdelfattah et al, 2022), we chose to focus initially on bone marrow-derived macrophages. Notably, it has already been reported that microglia were associated with significantly better survival, suggesting that they are anti-tumorigenic, whereas macrophages were associated with worse survival, suggesting that they are pro-tumorigenic (Pombo Antunes et al, 2021; Abdelfattah et al, 2022). This justifies our approach to focus on this cell type. Furthermore, although this model may be rather simplistic, it allowed us to screen different GSCCs side by side in a standardized way, through which we found an apparent phenotype switch within the macrophages, even without the complex interplay with other cell types. Because the results obtained using the in vitro model were also confirmed in GBM patient material and KO experiments in the zebrafish avatar model, our work shows that reliable and important insights can be derived. This, combined with its simplicity, makes our co-culture model an exceptionally relevant model that is scalable, screenable and allows us to study the effect of perturbations. Finally, the immunosuppressive role of the target we identified using this model, LGALS1, has been previously demonstrated by others (Verschuere et al, 2014; Van Woensel et al, 2017; Chen et al, 2019), which proves our approach is valid.

Although the zebrafish can be a great model to understand the progression of tumours and the role of immune cells, I don't think that the model developed by the authors is suitable to address their questions. Transplantation of GBM cells into the the ventricle of larval zebrafish doesn't seem to be the right approach here. The poor survival of the transplanted cells is a clear indication of that. Many other groups have reported growth and proliferation of human cancer cells in the larval zebrafish. Direct transplantation into the brain parenchyma would be the better approach here. The brain parenchyma would provide the right environment for the GBM cells including a resident microglial population. This would also allow to study the complex mix of microglia and infiltrating macrophages in the context of GBM.

Response: The reviewer does not specify which articles have reported growth and proliferation of human cancer cells in zebrafish larvae. Most research groups reporting this, did not follow tumor growth/proliferation over time or used immortalized cell lines (Vargas-Patron et al, 2019; Pan et al, 2020; Pudelko et al, 2018; Breznik et al, 2017; Vittori et al, 2017; Hamilton et al, 2016), which obviously have a much higher proliferation rate than the patient-derived cell lines used in this work. Second, although the number of patient-derived tumor cells decreases over time, we observed a clear invasive and migratory behavior, indicating that the human tumor cells reside well in the zebrafish microenvironment. Furthermore, it is important to note that the zebrafish avatars are grown at 34°C, a temperature that is suboptimal for tumor cell growth. The tumor cells still proliferate, albeit at a lower rate than at 37°C.

To our knowledge, there is only one publication that reports the growth of patient-derived GBM tumors over time (Almstedt et al, 2022). However, here, zebrafish embryos were grown at 33°C. Also, prior to injection, patient-derived GBM cells were resuspended in medium containing polyvinylpyrrolidone, a polymer that enhances extracellular matrix deposition and cell proliferation. Furthermore, the authors observed substantial differences in proliferative capacity, ranging from growth to decline of signal, and represented only two patient-derived cell lines with growing tumors. Similar to our findings, another article has demonstrated that injected patient-derived GBM tumor cells progressively underwent mitotic arrest, while maintaining an invasive and aggressive growth pattern (Rampazzo et al, 2013).

Although the tumor cells are injected into the hindbrain ventricle, they end up in the brain parenchyma, as evidenced by the presence of the typical brain vasculature of the zebrafish embryo. Notably, in Tg(mpeg1:mCherryF)ump2 zebrafish embryos, both macrophages and microglia are labeled with mCherry, meaning that we have studied both cell types in our zebrafish avatar model. Therefore, we consider the reviewer’s comment to be unfounded.

Reviewer #3

__ Evidence, reproducibility and clarity: __

In this study, Finotto and colleagues developed patient-derived Glioblastoma (GBM) stem cell cultures from 7 patients. These GBM stem cell cultures were either co-cultured in vitro with human macrophages combined with single-cell RNA sequencing or injected into the orthotopic zebrafish xenograft to study live GBM-macrophage/microglia interactions. Authors aimed at studying tumor heterogeneity and GBM-associated macrophages (GAMs) which often exhibit immunosuppressive features that promote tumor progression. Their analyses revealed substantial heterogeneity across GBM patients in GBM-induced macrophages polarization and the ability to attract and activate GAMs - features that correlated with patient survival. Also authors show 3 distinct macrophage subclusters (MC1-3), highlighting that the simple M1/M2 polarization phenotypes is too reductive and there are no clear "markers". Authors associate these profiles with morphology and macrophage behaviour. Differential gene expression analysis, immunohistochemistry on original tumor samples, and knock-out experiments in zebrafish subsequently identified / confirmed that LGALS1 as a primary regulator of immunosuppression.

Cheng et ( DOI: 10.1002/ijc.32102) had previously shown the immunosuppression effect of LGALS1 - but this work shows as a proof of concept that the authors approach is a valuable and interesting approach to find immune regulators.

Response: We fully agree with Reviewer #3. In fact, the immunosuppressive role of LGALS1 has already been described by several research groups (Van Woensel et al, 2017; Verschuere et al, 2014), which indeed proves that our approach is valid. The reference cited by the reviewer was already included in the manuscript, along with other references.

Major comments:

In general claims are supported by date - very carefully presented and well characterized data with numbers, stats. It is an interesting descriptive study that illustrates the complexity and diversity of glioblastoma and the induced TME. I just have a few comments or clarifications that I would like to have elucidated:

• I did not understand why not single cell sequence the original tumor - without in vitro passaging and have the original patient population of MACs/microglia and monocytes sequenced? In other words why sequence the in vitro system-with its inherent caveats of in vitro culturing and not the original tumor? Can you please clarify.

Response: We agree with Reviewer #3 that our in vitro model does indeed have caveats inherent to patient-derived cell culture models. However, we chose this model to specifically focus on the reciprocal interaction between GBM tumor cells and macrophages in a way that also allows us to investigate how perturbations affect these interactions. This is not possible when using original tumors (e.g. we cannot make KO cells, as we did for LGALS1, and study the effects of genes of interest). (See also the response to the comment of Reviewer #2)

We do have scRNAseq data from one original tumor sample (LBT123) that is currently being analyzed. Unfortunately, scRNAseq is not available for the other tumor samples. Also, for some of the patients, there is no original material left to use for sequencing. For LBT123, we will compare the scRNAseq data from the original tumor with the in vitro data from the co-culture model.

• Mac signatures - out of curiosity- authors could not find TNFa and IFN signatures in any population?

Response: Our analyses did not reveal TNF or IFN as cluster signature genes. However, we did find that TNF expression was slightly higher in MC2, the pro-inflammatory macrophages, although still at low levels. We did not find IFN expression in the macrophage subclusters, but we did find low expression of some IFN receptors. We found a gradient for IFNGR1 with the highest expression in MC3, followed by MC1 and the lowest expression in MC2. IFNGR2 was expressed at slightly higher levels in MC1 compared to the other subclusters. IFNAR1 and IFNAR2 were expressed at comparable low levels in all subclusters. Finally, IFNLR1 expression was higher in MC3 compared to the other two macrophage subclusters. Considering the overall low expression of IFN receptors, we believe that the differences in expression are rather negligible. Furthermore, it has been previously shown that IFN exerts its anti-tumor effect primarily through the responsiveness of endothelial cells and not of myeloid cells, such as macrophages (Kammertoens et al, 2017). Since vascular cells were not present in the co-culture model, low IFN receptor expression is not surprising. We are happy to investigate this in more detail and include it if deemed useful.

• 8 please show controls side by side with the KO

Response: We thank Reviewer #3 for this comment. We are not quite sure which panel the reviewer is referring to. If it is panel F, we agree with Reviewer #3 and have changed the order of the bars in the revised version. If it is panel E, the corresponding control images are shown in Figure 5I. Since we believe that these images should not be repeated, we have added a figure reference to Figure 5I in the figure legend of Figure 8, in addition to the figure reference already provided in the text. Furthermore, images of all embryos are presented side by side in Figure S8D-E.

• Figure 5: if each pair of images are separated and have the legend on top would be easier to *read and follow. *

Response: We appreciate the comment that the figure should be intuitively easy to read and follow. However, we have chosen a compromise between overview and visibility of details (e.g. morphological features of GAMs). Since this figure already has the maximum width, the images would become smaller if they needed to be separated. Reducing the size would compromise the visibility of important details.

Significance:

It is a very interesting study, carefully designed and performed that highlights the heterogeneity of glioblastoma and how GBM can modulate the macrophage population into 3 different subsets. This study constitutes a proof of concept of the combination of and in vitro approach and an in vivo approach to find new players and treatments in glioblastoma. I believe that it would be important and interesting to have a the original tumor sequenced to compare to the in vitro platform and understand how the in vitro selection impacts on the tumor biology and even if it changes the heterogeneity and differential composition of the tumor and macrophage profiles.

References:

Abdelfattah N, Kumar P, Wang C, Leu JS, Flynn WF, Gao R, Baskin DS, Pichumani K, Ijare OB, Wood SL, et al (2022) Single-cell analysis of human glioma and immune cells identifies S100A4 as an immunotherapy target. Nat Commun13

Almstedt E, Rosen E, Gloger M, Stockgard R, Hekmati N, Koltowska K, Krona C & Nelander S (2022) Real-time evaluation of glioblastoma growth in patient-specific zebrafish xenografts. Neuro Oncol 24: 726–738

Breznik B, Motaln H, Vittori M, Rotter A & Turnšek TL (2017) Mesenchymal stem cells differentially affect the invasion of distinct glioblastoma cell lines. Oncotarget 8: 25482–25499

Jayakrishnan P, H. Venkat E, M. Ramachandran G, K. Kesavapisharady K, N. Nair S, Bharathan B, Radhakrishnan N & Gopala S (2019) In vitro neurosphere formation correlates with poor survival in glioma. IUBMB Life 71: 244–253

Chen JWE, Lumibao J, Leary S, Sarkaria JN, Steelman AJ, Gaskins HR & Harley BAC (2020) Crosstalk between microglia and patient-derived glioblastoma cells inhibit invasion in a three-dimensional gelatin hydrogel model. J Neuroinflammation 17

Chen Q, Han B, Meng X, Duan C, Yang C, Wu Z, Magafurov D, Zhao S, Safin S, Jiang C, et al (2019) Immunogenomic analysis reveals LGALS1 contributes to the immune heterogeneity and immunosuppression in glioma. Int J Cancer145: 517–530

Coniglio S, Miller I, Symons M & Segall JE (2016) Coculture assays to study macrophage and microglia stimulation of glioblastoma invasion. Journal of Visualized Experiments 2016

Hamilton L, Astell KR, Velikova G & Sieger D (2016) A zebrafish live imaging model reveals differential responses of microglia toward glioblastoma cells in vivo. Zebrafish 13: 523–534

Hubert CG, Rivera M, Spangler LC, Wu Q, Mack SC, Prager BC, Couce M, McLendon RE, Sloan AE & Rich JN (2016) A three-dimensional organoid culture system derived from human glioblastomas recapitulates the hypoxic gradients and cancer stem cell heterogeneity of tumors found in vivo. Cancer Res 76: 2465–2477

Kammertoens T, Friese C, Arina A, Idel C, Briesemeister D, Rothe M, Ivanov A, Szymborska A, Patone G, Kunz S, et al(2017) Tumour ischaemia by interferon-γ resembles physiological blood vessel regression. Nature 545: 98–102

Li H, Yan X & Ou S (2022) Correlation of the prognostic value of FNDC4 in glioblastoma with macrophage polarization. Cancer Cell Int 22

Pan H, Xue W, Zhao W & Schachner M (2020) Expression and function of chondroitin 4-sulfate and chondroitin 6-sulfate in human glioma. FASEB Journal 34: 2853–2868

Pombo Antunes AR, Scheyltjens I, Lodi F, Messiaen J, Antoranz A, Duerinck J, Kancheva D, Martens L, De Vlaminck K, Van Hove H, et al (2021) Single-cell profiling of myeloid cells in glioblastoma across species and disease stage reveals macrophage competition and specialization. Nat Neurosci 24: 595–610

Póvoa V, Rebelo de Almeida C, Maia-Gil M, Sobral D, Domingues M, Martinez-Lopez M, de Almeida Fuzeta M, Silva C, Grosso AR & Fior R (2021) Innate immune evasion revealed in a colorectal zebrafish xenograft model. Nat Commun12

Pudelko L, Edwards S, Balan M, Nyqvist D, Al-Saadi J, Dittmer J, Almlöf I, Helleday T & Bräutigam L (2018) An orthotopic glioblastoma animal model suitable for high-throughput screenings. Neuro Oncol 127: 415

Rampazzo E, Persano L, Pistollato F, Moro E, Frasson C, Porazzi P, Della Puppa A, Bresolin S, Battilana G, Indraccolo S, et al (2013) Wnt activation promotes neuronal differentiation of glioblastoma. Cell Death Dis 4

Van Woensel M, Mathivet T, Wauthoz N, Rosière R, Garg AD, Agostinis P, Mathieu V, Kiss R, Lefranc F, Boon L, et al(2017) Sensitization of glioblastoma tumor micro-environment to chemo- and immunotherapy by Galectin-1 intranasal knock-down strategy. Sci Rep 7: 1–14

Vargas-Patron LA, Agudelo-Dueñãs N, Madrid-Wolff J, Venegas JA, González JM, Forero-Shelton M & Akle V (2019) Xenotransplantation of human glioblastoma in zebrafish larvae: in vivo imaging and proliferation assessment. Biol Open 8

Verschuere T, Toelen J, Maes W, Poirier F, Boon L, Tousseyn T, Mathivet T, Gerhardt H, Mathieu V, Kiss R, et al (2014) Glioma-derived galectin-1 regulates innate and adaptive antitumor immunity. Int J Cancer 134: 873–884

Vittori M, Breznik B, Hrovat K, Kenig S & Lah TT (2017) RECQ1 helicase silencing decreases the tumour growth rate of U87 glioblastoma cell xenografts in zebrafish embryos. Genes (Basel) 8

Zhou F, Shi Q, Fan X, Yu R, Wu Z, Wang B, Tian W, Yu T, Pan M, You Y, et al (2022) Diverse macrophages constituted the glioma microenvironment and influenced by PTEN status. Front Immunol 13

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Referee #3

Evidence, reproducibility and clarity

In this study, Finoto and colleagues developed patient-derived Glioblastoma (GBM) stem cell cultures from 7 patients. These GBM stem cell cultures were either co-cultured in vitro with human macrophages combined with single-cell RNA sequencing or injected into the orthotopic zebrafish xenograft to study live GBM-macrophage/microglia interactions. Authors aimed at studying tumor heterogeneity and GBM-associated macrophages (GAMs) which often exhibit immunosuppressive features that promote tumor progression. Their analyses revealed substantial heterogeneity across GBM patients in GBM-induced macrophages polarization and the ability to attract and activate GAMs - features that correlated with patient survival. Also authors show 3 distinct macrophage subclusters (MC1-3), highlighting that the simple M1/M2 polarization phenotypes is too reductive and there are no clear "markers". Authors associate these profiles with morphology and macrophage behaviour.

Differential gene expression analysis, immunohistochemistry on original tumor samples, and knock-out experiments in zebrafish subsequently identified / confirmed that LGALS1 as a primary regulator of immunosuppression. Cheng et ( DOI: 10.1002/ijc.32102) had previously shown the immunosuppression effect of LGALS1 - but this work shows as a proof of concept that the authors approach is a valuable and interesting approach to find immune regulators.

Major comments

In general claims are supported by date - very carefully presented and well characterized data with numbers, stats. It is an interesting descriptive study that illustrates the complexity and diversity of glioblastoma and the induced TME. I just have a few comments or clarifications that I would like to have elucidated: 1. I did not understand why not single cell sequence the original tumor - without in vitro passaging and have the original patient population of MACs/microglia and monocytes sequenced? In other words why sequence the in vitro system-with its inherent caveats of in vitro culturing and not the original tumor? Can you please clarify 2. Mac signatures - out of curiosity- authors could not find TNFa and IFN signatures in any population? 3. Fig. 8 please show controls side by side with the KO 4. Figure 5 if each pair of images are separated and have the legend on top would be easier to read and follow.

Significance

It is a very interesting study, carefully designed and performed that highlights the heterogeneity of glioblastoma and how GBM can modulate the macrophage population into 3 different subsets. This study constitutes a proof of concept of the combination of and in vitro approach and an in vivo approach to find new players and treatments in glioblastoma.

I believe that it would be important and interesting to have a the original tumor sequenced to compare to the in vitro platform and understand how the in vitro selection impacts on the tumor biology and even if it changes the heterogeneity and differential composition of the tumor and macrophage profiles.

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Referee #2

Evidence, reproducibility and clarity

Finotto et al aim to address the polarisation of macrophages within GBM in their study. To do this, they have developed two different models. The first model is an in-vitro co-culture model of patient derived GSC lines and human monocyte derived macrophages. This model was used for single cell sequencing to understand the transcriptomic changes of macrophages upon contact to GBM cells. The second model is a zebrafish xenograft model. Here GFP labeled GBM cells were transplanted into the larval zebrafish ventricle. These experiments were done in the transgenic mpeg zebrafish which allowed to monitor responses of macrophages in vivo.

In my opinion both models are not sophisticated enough to draw solid conclusions on macrophage polarisation in GBM. The in vitro model is highly artificial and is far from the complex situation in GBM. Within GBM the GAM population represents a heterogenous mix of resident microglia and infiltrating macrophages. These are influenced by the heterogeneous environment (which consists of tumour cells but also other host cells) and show diverse transcriptomic adaptations as shown in rodent models as well as sequencing studies of patient derived tumour samples. Studying monocyte derived macrophages in vitro does not provide any reliable insight.

Although the zebrafish can be a great model to understand the progression of tumours and the role of immune cells, I don't think that the model developed by the authors is suitable to address their questions. Transplantation of GBM cells into the the ventricle of larval zebrafish doesn't seem to be the right approach here. The poor survival of the transplanted cells is a clear indication of that. Many other groups have reported growth and proliferation of human cancer cells in the larval zebrafish. Direct transplantation into the brain parenchyma would be the better approach here. The brain parenchyma would provide the right environment for the GBM cells including a resident microglial population. This would also allow to study the complex mix of microglia and infiltrating macrophages in the context of GBM.

Significance

In my opinion both models are not sophisticated enough to draw solid conclusions on macrophage polarisation in GBM.

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Referee #1

Evidence, reproducibility and clarity

Summary: the paper suggested a new approach to study in vivo possible interaction between glioblastoma cells and glioblastoma associated macrophages. By using single cells transcriptome profiling and in vitro and in vivo functional experiments the authors also suggested LGALS1 as possible key factor in the suppression of the immune system and a new target for immune modulation in glioma patients. The experimental plan is well described, and the results are beautifully presented using images, clear drawings, and videos.

Major comments: none

Minor comments: The number of zebrafish embryos analyzed after the xenograft is highly variable (e.g. 3-18; 4-22 in Figure 6). These numbers can be reported in the results section (not only in the legends) and the authors may comment on them in the discussion. The reproducibility of the xenotransplant experiments is always challenging as it is quite difficult to inject the same number of cells in every embryo and to have the same survival rate of injected cells and of transplanted embryos. For these reasons the volume of each xenograft can vary significantly in different embryos and in different experimental session. Accordingly, the number of macrophages associated to the tumor can vary and the statistical analysis can be deeply influenced by the number of replicates for each experimental group (a group with 3 embryos is very different in term of quality and quantity of information in respect to a group of 18 embryos). It could be useful for the reader, who has no experience in this technique, be aware of the advantages and disadvantages of the procedure including the possible influence of the temperature (34{degree sign}C instead of 37{degree sign}C) on the embryo survival and the replication rate of glioma cells or macrophages behavior. Comment on these aspects does not weaken the power and the relevance of the model but unveil the critical aspects that every scientist has to evaluate before planning these kinds of experiments. An aspect that could be interesting to address, to further validate the avatar model, is to monitor the level of pro-inflammatory cytokines (Tumor Necrosis Factor and Interleukin 1, 6, and 8) that are expressed at basal level in the early developing zebrafish embryos. Do their expression level increase after the xenotransplantation? Can the zebrafish cytokines affect the behavior of glioma associated macrophages (i.e. macrophages polarization)?

Significance

Strengths and limitation. The manuscript is the result of a well-orchestrated effort to dissect a biological problem by complementary approaches and provide new data with high impact translational value. The image processing pipeline developed by the authors is a step forward in the in vivo analysis of cells interaction in living embryos. The identification of LGALS1 as a potential target for immune modulation can support the development of new therapeutical strategy implementing chemo- or immunotherapy protocols. The described zebrafish avatar can represent a new tool for personalized drug testing recapitulating in a in vivo model the heterogeneity of GBM found in patients.

Audience: All the scientist interested in cell biology, cancer cell biology, imaging techniques, translational medicine, in vivo models for cancer research, precision medicine.

Reviewer expertise: applied developmental biology

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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:

Extracellular vesicles (EV) from three different phylotypes (A1, H1, H2) of Cutibacterium acnes were analyzed for size distrubution, protein content and inflammatory effects on cellular systems in vitro. Main findings were that EV composition differs between the the phylotypes that by other have been suggested to have pathogenic or more beneficial properties. Furthermore, A1 EVs induce more proinflammatory signals than H1 EVs. The conclusion are that EVs are key modulators of during skin alterations, and H1 EVs are suggested as a treatment of acne vulgaris symptomatology.

Major comments:

1. The purpose is stated as "to study the role of EVs secreted by three different phylotypes of C. acnes (A1 as 25 pathogenic, H1 as beneficial and H2 as commensal)". This is in my mind a quite vague purpose that needs to be sharpened. What role are you talking about and where is it relevant? During infection, in experimental systems or as potential treatment?
2. The result section in the abstract is very short. At present it is not possible to understand what you have done by reading this. I suggest reducing the introduction part of the abstract and focus on your detailed results instead.
3. The conclusions in the abstract is a bit difficult to understand a potentially very far reaching. You have not in my mind shown that EVs are "key modulators during skin alterations". You have shown that EVs can modulate cellular responses in vitro which is far from skin alterations, but important in its own right.

Furthermore, "EVs as an alternative based-natural treatment to fight acne vulgaris symptomatology" is not really a supported conclusion but rather a potential future implication. The wording is also very odd; what does "alternative based-natural treatment" mean? You also come back to this in the main conclusion in the end. This needs to be clarified! 4. Line 465. You assume that your strains have lost virulence factors during evolution. This is just a wild guess without genetic analysis. It could be anything from real gene loss, via gene regulation, to post-translational regulation. 5. Line 510. You should tone done your claims about a closer picture of real skin in acne vulgaris. You are using models! 6. Since you are claiming an essential role for EVs during skin alterations, you are missing essential controls in your system. What happens if you add just washed bacteria to your systems? If you get the same signals, EVs are not essential but can have the same effects as the parent bacteria.

Minor comments:

Reference list All species should be in italics, No Upper Case Within Article Titles, and journals should be abbreviated consistently.

Significance

General assessment:

The most important aspect of this study is that EVs from different phylotypes of C. acnes have cellular effects that correlates with the pathogenic or beneficial profile of the parent bacteria. The major limitations are that the EVs are not compared with the parental bacteria in the systems and unsupported far reaching conclusions about using EVs as treament.

Advance:

The study is the first one looking at detailed protein patterns in different phylotypes of C. acnes and trying to link this to biological activity.

Audience:

Basic researchers in microbiology will read this with interest. At the moment, the translational/aspects are just suggested and not tested.

Expertise:

Infection medicine, experimental treatment, development of biological drugs, inflammatory diseases, anaerobic bacteria, antimicrobials, bacteriophages, commensals

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Referee #2

Evidence, reproducibility and clarity

The work by Pol et al. describes the proteome and the in vitro effect, in four different cell culture models, of extracellular vesicles (EVs) isolated from Cutibacterium acnes of three different phylotypes found in acneic (A1) and normal skin (H1 and H2). They found that the EVs from H1 and H2 strains seem to evoke less pro-inflammatory effector mechanisms and even anti-inflammatory cytokines. A1 EVs apparently carry a higher number of proteins that include virulence factors and possible pro-inflammatory molecules that have not been specified. Although the number of proteins tends to be quite high in microorganism EVs, the presence of other groups of molecules can not be ignored when drawing conclusions, however. Their results seem to support the conclusions that should anyway be softened, however some points related to the EV concentrations used in the analysis should be cleared, besides other details, in order to make the results stronger to the eyes of expert readers. 1. The abstract needs improvement. You can decrease the background information to a minimum necessary and give more result information.2. In introduction and throughout the text be careful to cite highly updated works when starting with "recent data..." - for e.g., in lines 39-43 the reference cited dates to 2017.3. The Brucella culture medium was chosen to grow C. acnes for isolation of EVs. This is a complex rich medium whose components could eventually associate to the bacteria and EV surfaces, resulting in proteome artifacts. How was that controlled? On the other hand, culture time was long (7 days) for that species. By 7 days in that medium, in which phase of the growth curve are the bacteria, considering that at stationary phase membranes from dead cells could co-precipitate with EVs? 4. EV preps were kept at -20oC. For how long? Are the properties of these EVs maintained fairly intact at these conditions?5. l. 317: I suppose NTA is a more quantitative imaging technique, but not more precise.6. l. 321: Can you present the EV yield/bacteria for each sample? Do the phylotypes grow at similar speed rates? 7. l. 328-331: There seems to be some artifactual effect in the Qubit protein estimation because it's clear from the SDS-PAGE gel that the 3 samples do not have the same 7 micrograms that they should according to the dosage methodology. Sample A1 possibly does considering that many of the protein bands are quite fat. Therefore, you can not compare the samples in terms of diversity or amount if there is not an internal quantity control in the proteome analysis. All the experiments that compared different concentrations of EVs among phylotypes could be compromised by an artifactual protein estimation. Please comment and justify.8. Gene ontology analysis refers to total EV proteins analyzed in each phylotype, is that correct? Supporting information Tables 1, 2, 3: The table headlines should specify that those identified proteins were found EXCLUSIVELY in each of the haplotypes. 9. l. 356: The extension of red staining within the cells seems to reflect that many EVs were internalized. Could you estimate the number of internalized EVs/cell? Please change "positive control" in the figure for EV or anything you choose, considering that this is your experimental result and not a positive control.10. l. 406 and others: the EVs induced or stimulated (not displayed) secretion of mediators.11. In Discussion, please exploit even further the individual proteins found in the proteome to suggest their presumed function in the  various effects observed in the work. In l. 555-556, please rephrase the sentence to make it clear, also softening the conclusion by using "suggested" instead of "proved". Although English is readable throughout the text, edition is needed to improve grammar specially in Discussion where there are numerous inadequacies.

Significance

The characterization of the microorganism EVs and their role in pathogenesis and eventual protection of the diseases they cause has incresed significantly and any new investigation brings new light to the subject. With the present work, the authors claim that EVs isolated H1 strains from normal skin could be useful in the treatment of acne based on their set of results.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This manuscript describes differences between three different C. acnes strains in their proteomics, internalization, and induction of host cell gene expression. These differences are assessed through what the manuscript reports to be extracellular vesicles, but the relevance of these particles is not clear. The strong differences in immunomodulatory phenotypes across strains is of potential interest, but more work needs to be done to demonstrate rigor, relevance, and clear interpretation.

Major concerns:

My primary concern is the relevance of these purported extracellular vesicles, which could have been produced by the filtering and centrifugation process. Can these particles be observed without this processing? Alternatively, can the authors demonstrate that these particles have distinct proteomic properties from the cells from which they were isolated?

A second major concern is the framing of these 3 strains. The evidence of association of type I strains and acne is weak. Most papers making this claim have not compared the same sampling sites on subjects of similar ages, or at least have not reported subject information well enough for this evidence to be clear. Moreover, it is not clear if the difference across 3 strains here are generalizable to these large clades or specific to these chosen strains. Notably, H1 strains are much more closely related to H2 strains than either is to A1 strains, challenging the meaning of the distinction between H1 and H2 strains and more generally the classification as probiotic, commensal, and pathogen. Type IB strains (which includes H1 and H2) have even been suggested to be more harmful in prosthetic infections [PMID: 34361935]. Regardless of the naming, a comparison between A strains and H strains is of interest - but a second A strain is required to make this evolutionary comparison.

• Line 321: A claim is made about EV production rate across strains, but no statistics are performed and a number is only provided for one of the three strains.
• Line 332: H1 and H2 are much more similar in their genomic content. Do the authors have a proposed reason for A1 and H1 sharing more proteomic similarity than H1 and H2?
• Which genome was chosen for analysis of the proteomic data? Might classification be biased towards strains for which the reference genome more closely matches the amino acid content of the analyzed strains?
• Line 341: For the biological function analysis, it is not clear if enrichment presented is relative to other strains or to the reference genome.
• Figure 6 needs to show individual dots of experimental replicates to enable assessment of variation.
• How were the probes for qPCR chosen? This is important for understanding multiple hypothesis correction. Were any others tested?

Minor concerns:

• Line 39: What about the vaginal microbiome?
• Line 51: Context for this depth is needed. How deep is a pilosebaceous unit?
• Line 56: It would be more correct to say that microbiome alterations are associated with the development of acne.
• Line 62: C acnes is known to break down sebum, so why is it assumed that sebum is a barrier for C acnes contact with host cells? What about secreted products that aren't in EVs?
• Line 64: 500 nm is getting close to the size of a bacterial cell
• Line 66: Citation needed.
• Line 92: Is this also done inside of a bag system as in the above section or in an anaerobic chamber?
• Line 96: The point of a 75 mm filter is not understood by this reviewer.
• Line 371: I could not locate a p-value in this entire section around gene expression induction in host cells. I see that there are statistics in the figures, but this needs to be indicated in the text as well.

Significance

This manuscript describes differences between three different C. acnes strains in their proteomics, internalization, and induction of host cell gene expression. These differences are assessed through what the manuscript reports to be extracellular vesicles, but the relevance of these particles is not clear. The strong differences in immunomodulatory phenotypes across strains is of potential interest to those studying C acnes biology, but more strains would need be tested to understand the relevance of these differences evolutionarily and more work would have to be done to understand the relevance of these EV particles. Claims about relevance to acne overstate the knowledge and consensus in the filed.

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Reply to the reviewers

Manuscript number: RC-2023-01899

Corresponding author(s): Laia Querol Cano

1. General Statements [optional]

We thank the reviewers for their positive evaluation and constructive feedback and appreciate the reviewers’ assessment that our findings are highly interesting and novel. We have already addressed some of their questions (see section 3 below and highlighted changes in the manuscript text) and initiated experiments to address the reviewers’ suggestions. We anticipate these experiments can be completed within three months.

2. Description of the planned revisions

Reviewer #1

Summary This paper is focused on the role of galectin-9 in dendritic cells using monocyte-derived DCs. To study the functional characteristics of galectin-9, they depleted galectin-9 with the use of gal9 siRNA. They found galectin-9 is required for TNF-alpha, IL-6, IL-10 and IL-12 secretion. Galectin-9 was found to be involved in TNF trafficking and interacted with Vamp-3 to regulate the release of TNF. They concluded that galectin-9 controls cytokine intracellular trafficking and secretion through functional interaction with the SNARE protein Vamp-3 in DCs through an endosomal compartment.

The findings seem significant in understanding the role of galectin-9 in dendritic cells which has not been previously explored, and they also expand our understanding of the roles of galectins and their potential function in intracellular cytokine trafficking. However, there are some concerns about the findings and conclusions of the study.

Major comments

Supplementary Figure 2A. No obvious decrease in TNF, IL-6, or IL-12 was observed in gal9 siRNA-treated cells that were stimulated with LPS and zymosan, and results in this panel are inconsistent with those of Suppl. Fig. 2B. An explanation for this discrepancy should be provided.

*We thank the reviewer for pointing this out. The discrepancy can be explained by the different time points used in Supplementary Fig. 2A versus Supplementary Figure 2B and main Figure 1. Supplementary Figure 2A depicts the optimisation carried out to screen the best stimuli for each of the cytokines analysed after 36h, which is considerably longer than the timepoints used throughout the manuscript (4-16 h). To make this consistent, we will repeat these experiments using 16 h stimulation. *

The data is sufficient to support the notion that galectin-9 is required for cytokine secretion, but intracellular staining of an additional cytokine (IL-6, IL-10, and IL-12) would be a good addition with controls included (non-transfected cells vs WT vs galectin-9-depleted).

This is a good suggestion and we performed intracellular stainings to detect IL-6, IL-10 and IL-12 on WT and galectin-9 depleted moDCs. Whereas intracellular IL-6 or IL-12 could not be detected with any of the commercial antibodies (IL-6 clone MQ2-13A5, Biolegend #501103; IL-12 clone 20C2, BD Biosciences #557020), we set-up intracelullar IL-10 stainings in primary DCs. IL-10 intracellular accumulation was observed in gal-9 KD DCs compared to WT cells upon LPS treatment although to a lesser extent than TNFα (see figure 1 for reviewer). We are now repeating this assay on multiple donors and this data will be incorporated to the revised manuscript.

Figure 1 for reviewer. Intracellular flow cytometry showing IL-10 levels in NT siRNA (black) and gal9 siRNA (light grey) moDCs treated with LPS for 6 h. Isotype control is depicted with unfilled dashed line. Numbers represent geometric mean intensity.

Addition of an immunofluorescent experiment using Vamp-3 and TNF co-localization in gal9 siRNA-treated cells would strengthen observations regarding galectin-9 association with Vamp-3 in immunoprecipitation.

• We agree and will address this by:*

• Immunofluorescence studies with moDCs (three independent donors with galectin-9 depletion (and Non Targeting siRNA counterparts) stimulated with LPS for 2, 4 and 6 h. Staining of Vamp-3, TNF-α, galectin-9 and DAPI is already established as have used these antibodies throughout the manuscript and thus do not anticipate any issues when performing these assays.

• *Co-localisation of galectin-9 and Vamp-3 will be determined by quantifying both the Manders’ and Pearson’s correlation coefficients (See Major point #4 from reviewer #1 in section 3). *

Figure 7A. Vamp-3 does not appear to redistribute towards the cell membrane following LPS stimulation in this figure. Either a different set of images needs to be selected or the text needs to be revised.

*To address this issue, we will include an enlarged zoomed in image of a representative cell in the revised version of the manuscript. Furthermore, we will include a Golgi marker (GM130) in our staining panel to quantify Vamp-3- Golgi co-localisation in WT and Galectin-9 depleted moDCs treated with LPS. *

All findings in this study regarding galectin-9 immunoreactivity are dependent on a single goat anti-galectin-9 antibody (AF2045). Findings would be strengthened by the use of a second galectin-9-specific antibody in at least one additional experiment (either immunofluorescence or immunoprecipitation).

*We have purchased another anti galectin-9 antibody (clone 9M1-3, BioLegend #348902) that will be used for immunofluorescence experiments to confirm our findings. *

Minor comments

Figure 2D needs at least one more experiment before results can be depicted. An n=2 is not sufficient to merit publication.

• We agree and will conduct the same experiment as described in Figure 2D with one additional donor to obtain n=3. Data from panel 2E will be also updated to incorporate the new data set.*

Supplementary Figure 2 has additional small square symbols in panels A and B that should be removed.

• We apologise for this. Supplementary Figure 2A will be re-made with new donors for the revised version of the manuscript without the square symbols. Supplementary Figure 2B has been remade to include four donors for each time point and stimulation and the square symbols have been removed.*

Supplementary Figure 2 legend. This legend has repetitive text regarding representative data from one donor. How many donors were tested for these experiments?

• Please see minor comment #5 above. Only a representative donor was included for panel A but experiments are being conducted to replace this figure with a more complete one including data from at least three independent experiments. Panel B has been remade and now includes data from four independent donors.*

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

This paper shows that knock down of galectin-9 suppresses secretion of certain cytokines in activated dendritic cells. Then they show that this correlates with failure of the peripheral localization of the SNARE- protein VAMP3 and suggest that this is due to a direct interaction with galectin-9.

Most of the data consist of comparing wt and galectin-9 KD cells regarding secretion and trafficking of selected cytokines (with focus on TNFa), and of cellular localization of the vSNARE VAMP3. The cells are mainly LPS activated human dendritic cells derived from differentiation on blood monocytes from donors, but differentiated THP-1 cells are also used. These data show convincingly that cytokine secretion is inhibited in galectin-3 KD cells, and for TNFa studied on detail, this is due to failure of post-Golgi trafficking of the, shown in different ways, including a RUSH assay. The trafficking of the vSNARE VAMP3 to the periphery of the cells is also inhibited by absence of galecytin-9, leading to its retention in the Golgi nearer the nucleus. Thus this couples in a surprising the unsolved question of how SNAREs themselves are trafficked to their correct destinations, to the function of a cytosolic galectin.

The weak part of the paper is the molecular interaction between galectin-9 and VAMP3. This is based on co-immunoprecipitations followed by proteomic characterization and Western blots as summarized in Fig. 6. These data show that galectin-9 and VAMP3 occur in the same precipitated complex, but not that they interact directly. Many other proteins are also in these complexes, and the Western blot data are not very strong. Thus additional experiments would be needed to claim the direct interaction as depicted in Fig.8 for example using purified recombinant proteins, or sharpened focus using mutants of the two interactors.

• We thank the reviewer for these positive comments and agree that protein co-immunoprecipitation does not warrant direct interaction. To discern whether galectin-9 and Vamp-3 directly interact or are part of a bigger protein complex, we will use purified recombinant proteins in GST-pull down assays. Briefly, we will generate and express Vamp-3-GST constructs that will be incubated with recombinant Galectin-9 protein, which has been performed in a similar manner in Miller et al., Cell. 2011. Protein complexes will be resolved and analysed by SDS-Page. GST-only beads will be used as negative control and a known SNARE complex (Syntaxin 4 together with Snap23) will be used as positive control in these experiments. We have experience in producing recombinant proteins in HEK293 cells And GST-pull down experiments within our department. *

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

Reviewer #1:

Major Comments

1. Page 4, Results. The assertion of 90% downregulation of galectin-9 protein is not substantiated by the data shown in Supplementary Figure 1 (it is not indicated which data, the flow or Western blot, provides the source for this statement). It must be assumed it is from Western blots, as the data from flow cytometry does not show a reduction of 90%. This assertion would be strengthened by density analysis of Western blots shown as a graph beside the blots in Supplementary Figure 1C. *We thank the reviewer for addressing this point. This refers to the Western blot data. We have now quantified four independent donors and have added this graph as a new panel in Supplementary Figure 1 (new panel D). *

Mander's correlation coefficient is typically not advised for use in co-localization of immunofluorescence since it has been found to downplay associations in low intensity fluorescent staining and favors high intensity and co-occurrence. It also ignores blank pixels. What is your reasoning for using Mander's instead of Pearson's correlation coefficient in your study?

• Mander’s correlation coefficient describes co-occurrence and is used to determine the fraction of the protein of interest that co-localises with another protein (Arruda et al., 2014. Nature Medicine; Horner et al., 2011. PNAS). Our question was to quantify to what extend do cytokines (using TNFα as proof of principle) localise within a particular organelle and therefore we believe using Mander’s correlation coefficient is appropriate. The reviewer is right in saying that Mander’s calculations ignore blank pixels although Pearson coefficients are also highly dependent on pixels coming from unlabelled regions, which can be an issue when quantifying the presence of cytokines in vesicles and requires the use of a threshold to discern background from relevant signal. We have calculated the Pearson’s correlation coefficient for all the relevant figure panels, which shows similar co-localisation as the Mander’s quantification. This data can be found in new Supplementary Figure 5.*

Page 8, Discussion. It would be interesting to suggest a mechanism that explains galectin-9-mediated depletion of Vamp-3 protein levels (which is suggestive of transcriptional repression), particularly since experiments suggest that gal9 siRNA treatment did not affect transcription of cytokines.

We have modified the discussion in page 10 to further speculate on the mechanisms by which galectin-9 may reduce Vamp-3 protein levels. Based on our RNAseq data of WT and galectin-9 depleted moDCs that show no differences in Vamp-3 gene expression, we believe galectin-9 is important for Vamp-3 stabilisation rather than participating in Vamp-3 transcriptional regulation.

Page 8, Discussion. The statement that the findings from this study is in line with the report that extracellular recombinant galectin-9 enhances IL-6 and IL-8 secretion in mast cells and IL-12 secretion in moDCs is somewhat confusing. Does extracellular galectin-9 cross the cell membrane into the cytoplasm? What is the evidence that it is capable of acting intracellularly when exogenously applied?

• We regret that this explanation did not come across clearly in the manuscript. We agree with the reviewer that there is no evidence that exogenously added galectins can re-enter the cytoplasm and be functionally active. To avoid any confusion, we have rephrased the text to “in addition, other studies report…”. *

Minor Comments

1. Figure 2A needs to have better colors chosen to indicate gal9 KD_LPS and gal9 KD_LPS/BFA+Mon samples, as they show similar colors. *We agree and have modified the figure accordingly. *

Figure 6D. Vamp-3 immunoreactivity shown in the blot does not appear to diminish on gal9 siRNA treatment as suggested in Fig. 6E. A better representative blot should be shown.

*For clarification purposes, we have added the quantification of the Vamp-3 representative blot to Figure 6D. To emphasise the differences in Vamp-3 levels upon galectin-9 depletion we have also added the quantification of Snap23 to Figure 6E. *

Supplementary Figure 1 A and B need a legend to show NT and gal9 siRNA-treated samples.

• We have now added this legend to Supplementary Figure 1A and B.*

Supplementary Figure 4, is it possible to have a merged image without galectin 9 (nuclei + TNF) for better clarity of TNF localization relative to nuclei?

We addressed this point and replaced the previous merged image with one only containing the fluorescent signals corresponding to nuclei (DAPI) and TNF*α. *

Please explain more explicitly why TNF+ cell % increased in gal9 siRNA-treated cells while secretion trended downward in these cells. Presumably TNF is retained in the GM130+ Golgi apparatus following knockdown of galectin-9 but this is not clearly explained in the text on page 6.

• We have rephrased the text on page 6 to address the reviewer’s concern. The text has been modified to “Overall, these results demonstrate TNFα is retained in the GM130 positive Golgi complex following galectin-9 depletion thus establishing galectin-9 as essential for cytokine trafficking to the plasma membrane via the endosomal machinery”.*

Lack of literature/rationale support for the use of CD80, CD86, CD83, HLA-DR as markers for plasma membrane protein trafficking being unaffected by galectin 9 depletion. These require further support to explain their use as good markers for general cellular trafficking.

Dendritic cells are well-known to upregulate CD80, CD86, CD83 and HLA-DR membrane expression upon maturation (Immunobiology of Dendritic Cells., Banchereau et al., 2000. Annual Review of Immunology; Reis e Sousa., 2006. Nat Rev Immunology). In resting dendritic cells, these proteins are stored in the endosomal compartment but traffic to the membrane upon activation and are therefore well-established markers for intracellular transport and membrane re-organisation upon dendritic cell activation (Klein et al., 2005. International Immunology; Baravalle et al., 2011. Journal of Immunology). We have added a sentence to the results section (page 4) to explain the rationale for choosing these markers.

Figure 8. Please show cortical actin cytoskeleton in this figure and correct spelling for vesicle in left panel.

• We have added the actin cytoskeleton to the figure and corrected the spelling mistake. *

Reviewer #2:

A brief summary/discussion of the time aspect would also be of interest as the experimental setups are quite complex. The KD after siRNA obviously takes some hours, but after that stimulation with LPS appears to take many more hours to affect VAMP3 distribution in wt cells (Fig. 7). What is it that takes so much time? The time from ER - plasma membrane is more like 30 minutes for a constitutively secreted protein. The RUSH experiment (Fig. 5) also show a relatively fast passage of TNFa out of ER-Golgi in wt cells.

• We thank the reviewer for raising this point. It takes 36-48 h for the gal9 siRNA to be effective after which galectin-9 levels stay depleted for up to 72 h. We chose 6 h to analyse Vamp-3 redistribution based on our ELISA experiments (Supplementary Figure 2B) that show cytokine secretion peaks 16 h after LPS stimulation. We agree with the reviewer that cytokine gene transcription, translation and protein trafficking also occurs earlier but endogenous intracellular cytokine levels are not high enough to detect them using confocal microscopy. Similarly, the RUSH experiment (Figure 5) was done using an over-expression system in which much higher levels of TNFα are being produced. *

• To further clarify this we have included a schematic depicting the experimental setup and times (see figure 2 for reviewer). *

Figure 2 for reviewer. Experimental setup. Monocyte-derived dendritic cells (moDC) are obtained from blood samples and differentiated for 6 days to generate immature dendritic cells (DCs). At day 3 of the differentiation moDCs are transfected with either non-targeting (NT) or gal9 siRNA to deplete galectin-9 protein levels and obtain wild type or galectin-9 knockdown (gal-9 KD) DCs. Six days after isolation, cells were treated with LPS for 6 h (to allow sufficient endogenous cytokine to accumulate intracellularly) prior to being fixed and immunofluorescent experiments (IF) conducted.

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

*This section is not applicable. *

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Referee #2

Evidence, reproducibility and clarity

This paper shows that knock down of galectin-9 suppresses secretion of certain cytokines in activated dendritic cells. Then they show that this correlates with failure of the peripheral localization of the SNARE- protein VAMP3 and suggest that this is due to a direct interaction with galectin-9.

Most of the data consist of comparing wt and galectin-9 KD cells regarding secretion and trafficking of selected cytokines (with focus on TNFa), and of cellular localization of the vSNARE VAMP3. The cells are mainly LPS activated human dendritic cells derived from differentiation on blood monocytes from donors, but differentiated THP-1 cells are also used. These data show convincingly that cytokine secretion is inhibited in galectin-3 KD cells, and for TNFa studied on detail, this is due to failure of post-Golgi trafficking of the, shown in different ways, including a RUSH assay. The trafficking of the vSNARE VAMP3 to the periphery of the cells is also inhibited by absence of galecytin-9, leading to its retention in the Golgi nearer the nucleus. Thus this couples in a surprising the unsolved question of how SNAREs themselves are trafficked to their correct destinations, to the function of a cytosolic galectin.

The weak part of the paper is the molecular interaction between galectin-9 and VAMP3. This is based on co-immunoprecipitations followed by proteomic characterization and Western blots as summarized in Fig. 6. These data show that galectin-9 and VAMP3 occur in the same precipitated complex, but not that they interact directly. Many other proteins are also in these complexes, and the Western blot data are not very strong. Thus additional experiments would be needed to claim the direct interaction as depicted in Fig.8 for example using purified recombinant proteins, or sharpened focus using mutants of the two interactors.

A brief summary/discussion of the time aspect would also be of interest as the experimental setups are quite complex. The KD after siRNA obviously takes some hours, but after that stimulation with LPS appears to take many more hours to affect VAMP3 distribution in wt cells (Fig. 7). What is it that takes so much time? The time from ER - plasma membrane is more like 30 minutes for a constitutively secreted protein. The RUSH experiment (Fig. 5) also show a relatively fast passage of TNFa out of ER-Golgi in wt cells.

Referees cross-commenting

I agree with all the comments of REviewer 1. Especially major comment 1 and 2 about the confusion of the figures. Major comment 8 is also highlöy relevant, as I also raiused but phrased ion a different way. There is so far no evidence that externally added galectin can reenter the cytosolic compoartment; it is only taken up inside vesicles,

Significance

This is highly interesting and novel. Very few papers have coupled SNARE function to galectins before, with key exception from group of Deretic et al regarding secretory autophagy suggesting association of galectin-3 to TRIM16 (not a SNARE, but can be SNARE associated).

Many follow up questions come up which could have been addressed in this paper or in a future paper. For example, could the Galectin-9 KD phenotype be rescued by added galectin-9 from the outside, as seen for many cases with other galectins? Were any other SNAREs affected?

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Referee #1

Evidence, reproducibility and clarity

Summary

This paper is focused on the role of galectin-9 in dendritic cells using monocyte-derived DCs . To study the functional characteristics of galectin-9, they depleted galectin-9 with the use of gal9 siRNA. They found galectin-9 is required for TNF-alpha, IL-6, IL-10 and IL-12 secretion. Galectin-9 was found to be involved in TNF trafficking and interacted with Vamp-3 to regulate the release of TNF. They concluded that galectin-9 controls cytokine intracellular trafficking and secretion through functional interaction with the SNARE protein Vamp-3 in DCs through an endosomal compartment.

The findings seem significant in understanding the role of galectin-9 in dendritic cells which has not been previously explored, and they also expand our understanding of the roles of galectins and their potential function in intracellular cytokine trafficking. However, there are some concerns about the findings and conclusions of the study.

Major Comments

1. Page 4, Results. The assertion of 90% downregulation of galectin-9 protein is not substantiated by the data shown in Supplementary Figure 1 (it is not indicated which data, the flow or Western blot, provides the source for this statement). It must be assumed it is from Western blots, as the data from flow cytometry does not show a reduction of 90%. This assertion would be strengthened by density analysis of Western blots shown as a graph beside the blots in Supplementary Figure 1C.
2. Supplementary Figure 2A. No obvious decrease in TNF, IL-6, or IL-12 was observed in gal9 siRNA-treated cells that were stimulated with LPS and zymosan, and results in this panel are inconsistent with those of Suppl. Fig. 2B. An explanation for this discrepancy should be provided.
3. The data is sufficient to support the notion that galectin-9 is required for cytokine secretion, but intracellular staining of an additional cytokine (IL-6, IL-10, and IL-12) would be a good addition with controls included (non-transfected cells vs WT vs galectin-9-depleted)
4. Mander's correlation coefficient is typically not advised for use in co-localization of immunofluorescence since it has been found to downplay associations in low intensity fluorescent staining and favors high intensity and co-occurrence. It also ignores blank pixels. What is your reasoning for using Mander's instead of Pearson's correlation coefficient in your study?
5. Addition of an immunofluorescent experiment using Vamp-3 and TNF co-localization in gal9 siRNA-treated cells would strengthen observations regarding galectin-9 association with Vamp-3 in immunoprecipitation.
6. Figure 7A. Vamp-3 does not appear to redistribute towards the cell membrane following LPS stimulation in this figure. Either a different set of images needs to be selected or the text needs to be revised.
7. Page 8, Discussion. It would be interesting to suggest a mechanism that explains galectin-9-mediated depletion of Vamp-3 protein levels (which is suggestive of transcriptional repression), particularly since experiments suggest that gal9 siRNA treatment did not affect transcription of cytokines.
8. Page 8, Discussion. The statement that the findings from this study is in line with the report that extracellular recombinant galectin-9 enhances IL-6 and IL-8 secretion in mast cells and IL-12 secretion in moDCs is somewhat confusing. Does extracellular galectin-9 cross the cell membrane into the cytoplasm? What is the evidence that it is capable of acting intracellularly when exogenously applied?
9. All findings in this study regarding galectin-9 immunoreactivity are dependent on a single goat anti-galectin-9 antibody (AF2045). Findings would be strengthened by the use of a second galectin-9-specific antibody in at least one additional experiment (either immunofluorescence or immunoprecipitation).

Minor Comments

1. Figure 2A needs to have better colors chosen to indicate gal9 KD_LPS and gal9 KD_LPS/BFA+Mon samples, as they show similar colors.
2. Figure 2D needs at least one more experiment before results can be depicted. An n=2 is not sufficient to merit publication.
3. Figure 6D. Vamp-3 immunoreactivity shown in the blot does not appear to diminish on gal9 siRNA treatment as suggested in Fig. 6E. A better representative blot should be shown.
4. Supplementary Figure 1 A and B need a legend to show NT and gal9 siRNA-treated samples.
5. Supplementary Figure 2 has additional small square symbols in panels A and B that should be removed.
6. Supplementary Figure 2 legend. This legend has repetitive text regarding representative data from one donor. How many donors were tested for these experiments?
7. Supplementary Figure 4, is it possible to have a merged image without galectin 9 (nuclei + TNF) for better clarity of TNF localization relative to nuclei?
8. Please explain more explicitly why TNF+ cell % increased in gal9 siRNA-treated cells while secretion trended downward in these cells. Presumably TNF is retained in the GM130+ Golgi apparatus following knockdown of galectin-9 but this is not clearly explained in the text on page 6.
9. Lack of literature/rationale support for the use of CD80, CD86, CD83, HLA-DR as markers for plasma membrane protein trafficking being unaffected by galectin 9 depletion. These require further support to explain their use as good markers for general cellular trafficking.
10. Figure 8. Please show cortical actin cytoskeleton in this figure and correct spelling for vesicle in left panel.

Referees cross-commenting

I agree with the comments of Reviewer #2 and especially that galectin-9 and VAMP-3 co-IP does not necessarily indicate that they are bound together. I also concur that a galectin-9 rescue experiment would be valuable.

Significance

General Assessment.

Strengths of study: Novel findings showing a role for galectin-9 in regulating cytokine trafficking and release from dendritic cells. This is a new observation which has not be reported before for galectin-9.

Weaknesses: Some results need verification and additional experiments are required to confirm the findings.

Advance: There is no existing knowledge for a role for galectin-9 in cytokine trafficking and this study fills this gap in existing published knowledge. The kind of advance that the study makes is fundamental and conceptual.

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Reply to the reviewers

1. General Statements

__Response: __Thank you to all the reviewers for their helpful efforts on behalf of our manuscript. At current, we have addressed most of the reviewers’ major comments, including providing additional replicates for many experiments and clarifying ambiguous points in the text. Related data, figures and text have been adjusted accordingly. We believe that these changes have improved our manuscript, both strengthening our main conclusions and clarifying ambiguous text.

Several still-ongoing experiments are elaborated below. These experiments are well within the abilities of our lab and can be completed in short order.

Specific responses to the individual concerns addressed by the reviewers are outlined below.

Please feel free to contact me if I can be of any help in the decision process.

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.

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[Reviewer 1]

Comment: Across the manuscript, NIX levels appear to be unresponsive to most treatments in the MDA-MB-231 line, including hypoxia treatment. This is an unusual result and raises questions about the role of NIX in MDA-MB-231 line, mainly that BNIP3 is the primary driver of mitophagy in this system. Indeed, Figure 7D indicates that there is very little mitophagy contribution by NIX since knockout of BNIP3 is sufficient to abolish mitophagy almost completely. Therefore, the effects seen on mitophagy following EMC3 knockout in Figure 7 might be smaller in a line that is responsive to NIX mitophagy. It would be beneficial to analyse basal mitophagy flux in an additional cell line, for example U2OS (FigS1E) in which NIX is responsive to hypoxia.

Response: Thank you for bringing this intriguing insight to our attention. We have seen that EMC3 knockout prevents lysosomal delivery of BNIP3 in U2OS cells (Fig S2D). However, we don’t know what the effects on mitophagy are in U2OS, or the extent to which mitophagy is dependent on BNIP3 and/or NIX. To test this, we will perform the suggested experiment, taking mt-Keima expressing U2OS cells testing the role of NIX and/or BNIP3 in mitophagy.

Comment: Following on from comment 1 above, Figure 7 would benefit with an analysis of hypoxia (or DFP, or cobalt chloride) stimulation of mitophagy to assess whether mitophagy levels are higher in EMC3 KOs. The authors argue that BNIP3 is trafficked to the ER during mitophagy and is not turned over by mitophagy itself, it would therefore be interesting to test if BNIP3 is prevented from being removed from mitochondria whether this would affect the rate or levels of mitophagy under stimulating conditions.

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__Response: __To address this question, we will perform mitoflux analysis on EMC3 KO cells +/- hypoxia.

Comment: Figure 4B: The localisation of tf-BNIP3 is reminiscent of ER in BTZ treated samples. How much of the protein is on mitochondria in the presence of BTZ? Does MLN4924 cause a similar issue?

__Response: __To address this question, we will perform fluorescence microscopy of tf-BNIP3 cells co-expressing mito-BFP under these treatments and utilize our Coloc2 plugin pipeline to monitor correlation.

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Comment: Can the authors assess whether BNIP3 that is on mitochondria is transferred to the ER (perhaps through photoswitchable GFP-BNIP, activated on mitos and then observe its transfer to ER)? This seems important in order to address the possibility that BNIP3 that is being turned over by the endolysosome is being delivered directly to the ER.

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__Response: __This is an interesting question and a curiosity also shared by Reviewer #2. To test this hypothesis, we will utilize a photo-switchable Dendra2 fluorophore to track BNIP3 in the cell via microscopy.

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[Reviewer #2]

Comment: How is BNIP3 inserted into the outer membrane? A previous study from the Weissman lab proposed that MTCH2 serves as insertase. The authors did not mention MTCH1 and MTCH2 in context of Fig. 2B. Were these proteins not found? Did the authors test the relevance of MTCH2 in their assay? This aspect should be addressed and mentioned.

__Response: __Thank you for the insight and suggestion. We were intrigued when the Weissman/Voorhees paper characterizing MTCH1/2 was published. Consistent with their findings, MTCH2 was found in the “suppressor” population of our tf-BNIP3 CRISPR screen, but given our 0.5-fold change threshold, the gene was not validated (fold change value = 0.46, Table S1). We suspect the lack of significance stems from the redundancy with MTCH1. Consequently, we would hypothesize that MTCH1/2 are the responsible insertases. To formally address this suggestion, we plan to genetically perturb MTCH1/2 and look at BNIP3 localization and mitophagy.

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Comment: The authors generated an interesting BNIP3 mutant with a C-terminal Fis1 anchor. This variant is constantly located in the outer membrane (which is shown here). The physiological consequence of the constitutive distribution on mitochondria is however only superficially studied. The authors should characterize this interesting mutant in some more depth.

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__Response: __In the original manuscript, we characterized BNIP3(Fis1TMD) for lysosomal delivery and mitophagy. Going forward, we will perform Seahorse oxygen consumption experiments and mitochondrial network analysis to view the physiological consequences of constitutive expression of BNIP3(Fis1TMD) on the outer membrane.

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.

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[Reviewer #1]

Comment: Continuing from comment 2, given that the authors conclude that BNIP3 is not turned over by mitophagy, can they examine whether BNIP3 is excluded from sealed mitophagosomes?

__Response: __We have softened the wording of our conclusions to reflect that the vast majority of BNIP3 lysosomal degradation is by this alternative pathway and not mitophagy. However, we do not wish to completely dismiss that BNIP3 is present on mitophagosomes. Rather, if mitophagosomes contain BNIP3, they seemingly account for only a very small portion of BNIP3 degradation in the cell, to the extent that it is not easily detectable by our assays (Lines 414-419). Definitively identifying whether BNIP3 is in sealed mitophagosomes will be part of future studies using CLEM or FIB-SEM techniques.

Comment: Is the BNIP3(FisTMD) expressed to equivalent levels to WT BFP-BNIP3? Given that theFis1 form of BNIP3 cannot traffic to endolysosomes, its levels might be higher. In addition, overexpression of the BNIP3-Fis construct was used to make the argument that dimerization is not important for mitophagy. But the authors should also take into account the possibility that with overexpression, the potential efficiency afforded to mitophagy via dimerization of endogenous proteins may be negated, and therefore hidden. Given this, I don’t think that the authors can confidently conclude that dimerization does not contribute to mitophagy, and that instead its main role is ER-endolysosomal turnover of BNIP3.

__Response: __We thank the reviewer for pointing out the possible over-interpretation of our data. Overexpression is an important caveat to consider. We would expect the Fis1 form of BNIP3 to be higher in protein levels given its deficiency in endolysosomal trafficking. Still, as the reviewer points out, over-expression could be mitigating the effect of our dimerization mutants. This caveat is now discussed in the manuscript and our interpretations regarding this fact have been greatly softened (Lines 373-376, Lines 449-462).

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Comment: Please include molecular weight markers for all western blots.

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__Response: __All western blots have now been labeled with molecular weight markers.

Comment: Figure 5A-G: These data do not make a convincing case for the role of dimerization and are very difficult to follow. Only the mislocalized S172A mutant was responsive to Baf treatment, while the LG swap mutant which is mitochondrial and cannot dimerize is unaffected by Baf treatment. Figure 5H-I utilize a construct of BNIP3 that is missing most of the protein and which has very low turnover (Figure 5B). Unfortunately these results don’t make a highly convincing case about the biology of native, full length, mitochondrial BNIP3. The authors are advised to either strengthen the dimerization argument, or perhaps lighten the language around the main conclusions from these data.

Response: __Thank you for bringing the lack of clarity to our attention. Both dimer mutants of BNIP3 (S172A and LG swap) are insensitive to Baf-A1 treatment. These results hold for full-length BNIP3 using either the tf (__Fig 5D) or IRES (Fig 5I) reporter. To demonstrate that defects in lysosomal transport were due to dimerization defects (and not other, unanticipated effects of the mutations), we looked at whether chemically induced dimerization could reverse the trafficking defects. Indeed, forced dimerization of the ER-restricted variant rescued ER-to-lysosome trafficking. From this, we conclude that that dimerization is a critical facet of BNIP3 trafficking to the lysosome.

We have re-worked the relevant text (both in results and discussion) to clarify major points and lighten the language around the conclusions from these data (described below).

First, as mentioned above, we have added a significant discussion about the limitations of our assay and of possible interpretations. (Lines 300-303, Lines 323-326, Lines 483-489).

Second, with regards to the specific construct used in this experiment, we have expanded the results section to better describe our rationale and approach (Lines 304-308). In short, because dimerization of native BNIP3 occurs within the membrane, we aimed to place the DmrB domain as close to the TM segment as possible. Due to the topology of TA proteins, a C-terminal tag isn’t possible. Therefore, we used the shortest truncation version of BNIP3 (117-end) that undergoes measurable lysosomal delivery. This was an important experimental consideration, and one we did not sufficiently rationalize in the original manuscript. We now include this point in the text.

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[Reviewer #2]

Comment: The authors show that BNIP3 on the ER is not stable but degraded by the proteasome. Does this require ERAD factors? Is the mitochondrial BNIP3 protein likewise degraded by proteasomal degradation? It is not clear whether both BNIP3 pools are constantly turned over or whether degradation exclusively/predominantly occurs on the ER surface.

Response: __These are fascinating mechanistic questions. We hope to thoroughly address these questions in a subsequent study. However, as a teaser, we have included the basic answer to these questions in __Fig 5I.

To preliminarily characterize the proteasomal degradation of ER- and mitochondrial-BNIP3, we utilized our IRES reporter system - adapted from Steve Elledge’s system for degron monitoring (Fig 5I). Strikingly, our ER-restricted BNIP3 mutation (S172A) is sensitive to inhibition of both the proteasome and the AAA-ATPase p97/VCP, a key extractase for ERAD substrates. These data tentatively suggest an ERAD-dependent degradation mechanism (although many follow-up studies will be needed to confirm the mechanistic details). In sharp contrast, our mitochondrial-restricted mutant (LG Swap) is sensitive to proteasome inhibition by Bortezomib, but it is insensitive to VCP inhibition. The differential requirement for VCP suggests that proteasomal degradation occurs on both cellular pools of BNIP3 albeit through different mechanisms.

Comment: The results of the screen shown in Fig. 2B are particularly interesting for readers. The glutathione peroxidase GPX4 was found as a top hit among the EMC components. GPX4 protects membranes (including those of mitochondria) against oxidative damage, is a major component of ferroptosis and linked to mitochondrial dysfunction and mitophagy. The authors should mention this interesting hit in the context of their discussion of the lipid-sensing properties of the dimerizing TM domains of BNIP3.

__Response: __Thank you to Reviewer #2 for bringing this to our attention. The relationship between GPX4 and BNIP3 flux is very interesting. We have incorporated GPX4 into the discussion section (Lines 457-459).

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[Reviewer #3]

Comment: For all of the tf-BNIP3 FACS data (all violin plots), it is unclear how many biological replicates were performed. The author only stated that at least 10,000 cells were analyzed per sample, but I believe this is for each biological replicate. To better demonstrate the biological replicates, the authors should consider using bar graphs of the medians(triplicates) with error bars.

Response: We have included biological replicates of FACS data in all primary figures (except for Fig.1C). Biological replicates, represented as medians (in triplicate), are indicated in figure legends.

Comment: In Fig 3D, it is unclear as to why there is no basal state accumulation of BNIP3 protein levels compared to Baf1A treated condition especially with USO1 and SAR1A KO samples. Is this because BNIP3 are targeted for proteasomal degradation? I think Fig 3D should include a BTZ treatment next to Baf1A to account for the lack of basal state accumulation of BNIP3.

Response: We apologize for the lack of clarity on this point. Yes, the reviewer’s interpretation of the data is correct. This point is more clearly elaborated in the text of our revised manuscript (Lines 219-223). Our results indicate that when lysosomal degradation is diminished, the expected increase in total BNIP3 protein levels is attenuated by proteasomal degradation (as evidenced by the hyperstability of BNIP3 upon Bortezomib treatment in mutant backgrounds). As requested, we have included the same knockout panel, now treated with BTZ (Fig S2E). These genetic data are further supported by Fig 3E, where a small molecule inhibitor of vesicle trafficking, Brefeldin-A, ameliorates the effect of lysosomal inhibition (BafA1) but exacerbates the effect of proteasome inhibition.

Comment: Truncation of proteins could affect their protein stability even during their synthesis. For Fig 5B and 6B, the authors should show the blots for the expression of the different truncated mutants to prove that the change in BNIP3 stability and their effect of mitoflux (or lack thereof), is not due to poor expression of these mutants.

Response: These were important potential caveats to document, and we thank the reviewer for their comment.

We note that, due to differences in transduction efficiency, western blot data is an incomplete measure for relative expression levels – it cannot distinguish between fraction of cells transduced and expression level per cell. However, RFP fluorescence (Fig 5B) and BFP fluorescence (Fig 6B) are fluorescent internal controls allowing us to assess expression levels with single cell resolution. We have provided histograms of RFP and/or BFP intensity (new Fig S4A, Fig S5B), which provides support that overall expression levels of these constructs are similar. Critically, any variation we observe does not correlate with any of the effects we report.

In addition, we have clarified the figure axis in Fig 5B to indicate that the value we are reporting is the “fold-stabilization upon BafA1 treatment”. The original figure legend wasn’t clear. Our metric (fold-stabilization) is internally normalized to compensate for differences in expression level. This is an important clarification.

Comment: For the data in Fig 7, the authors demonstrated that treating cells with proteasomal inhibitor increases mitoflux. Since the proteasome targets monomeric BNIP3 for degradation, the logical assumption is that BTZ drives dimerization of BNIP3. Can the authors demonstrate this in an approach similar to Fig 5C? This simple experiment will add significant insight into the study.

Response: __Thank you for the suggestion. As Fig 5C relied on BNIP3 over-expression, we thought it even more informative to assess the effects of BTZ on dimerization of endogenous BNIP3. Indeed, we see accumulation of an SDS-resistant BNIP3 dimer in cells treated with BTZ (__new Fig S2E, line 221). We hypothesize that BTZ indirectly drives dimerization of BNIP3 by accumulating the total levels of the protein, potentiating monomers to form additional stable dimers.

Comment: In line 168-169, "In addition, multiple suppressor genes identified from our screen had previously been reported including TMEM11..." -- Unclear what biology they are reported to be involved in

__Response: __We have clarified this line to read: "In addition, we recovered multiple known suppressors of BNIP3 flux, including outer membrane protein spatial restrictor TMEM11, mitochondrial protein import factors DNAJA3 and DNAJA11, and mitochondrial chaperone HSPA9"

Comment: Along the line with Major comment 2, the explanation for Fig 3D needs to be better elaborated, perhaps to include the role of proteasome already at this point (if the authors think this is the reason why basal BNIP3 levels remains low with USO1 and SAR1A KO).

__Response: __We have included a discussion about compensation by the proteasome in these genetic backgrounds (lines 219-226) and have referred to the newly incorporated western blot (new Fig S2E).

Comment: Line 302-304, I believe that statement only refers to Fig S4C and the statement for Fig5G is in the next sentence. Please remove Fig5G from line 304. It was confusing to read.

Response: __The reference of __Fig 5G has been removed.

Comment: Line 367, there is a reference for Fig S5C but that figure is missing.

__Response: __The spurious reference has been removed.

Comment: Line 410-411, are there any reported clinical cases of EMC mutations with phenotypes that could be explained by elevated mitophagy?

__Response: __Thank you for the suggestion. There are clinical presentations of EMC mutations and splice variants in diseases and conditions related to the central nervous system (PMID: 23105016, PMID: 26942288, PMID: 29271071). However, all characterization has been done in the clinical setting looking at clinical presentations/symptoms and not molecular or cellular characterization. We have added a line to the discussion about this speculative correlation between EMC deficiency and mitophagy (lines 516-519).

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.

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[Reviewer #1]

Comment: Figure 3B: Are the red puncta observed in USO1 and SAR1A cells a product of higher levels of ER-phagy owing to BNIP3's high presence on the ER membrane?

__Response: __This is an intriguing hypothesis. We will test whether this is true using a USO1/ATG9A dual KO. However, we don’t think this result is critical to the overall arc of the manuscript and we will not include these data if they indicate otherwise.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors provided a comprehensive study on the regulation of BNIP3 protein levels by both the non-autophagic lysosomal and proteasomal degradation pathways. Using various nifty tools, the authors demonstrated that ER-localised BNIP3 dimers are rerouted via the ER-lysosomal pathway for non-autophagic lysosomal degradation whereas BNIP3 monomers on both the ER and mitochondria are targeted for proteasomal degradation. Together, these pathways help to repress hyperactivation of basal mitophagy.

Overall, I find this project very well executed and the manuscript is also very clear and concise. The key conclusions of this work are supported by orthogonal approaches, thus making the data highly convincing. I only have a few major and several minor comments for this manuscript:

Major comments:

1. For all of the tf-BNIP3 FACS data (all violin plots), it is unclear how many biological replicates were performed. The author only stated that at least 10,000 cells were analysed per sample but I believe this is for each biological replicate. To better demonstrate the biological replicates, the authors should consider using bar graphs of the medians (triplicates) with error bars.
2. In Fig 3D, it is unclear as to why there is no basal state accumulation of BNIP3 protein levels compared to Baf1A treated condition especially with USO1 and SAR1A KO samples. Is this because BNIP3 are targeted for proteasomal degradation? I think Fig 3D should include a BTZ treatment next to Baf1A to account for the lack of basal state accumulation of BNIP3.
3. Truncation of proteins could affect their protein stability even during their synthesis. For Fig 5B and 6B, the authors should show the blots for the expression of the different truncated mutants to prove that the change in BNIP3 stability and their effect of mitoflux (or lack thereof), is not due to poor expression of these mutants.
4. For the data in Fig 7, the authors demonstrated that treating cells with proteasomal inhibitor increases mitoflux. Since the proteasome targets monomeric BNIP3 for degradation, the logical assumption is that BTZ drives dimerization of BNIP3. Can the authors demonstrate this in an approach similar to Fig 5C? This simple experiment will add significant insight into the study.

Minor comments:

1. In line 168-169, "In addition, multiple suppressor genes identified from our screen had previously been reported including TMEM11..." -- Unclear what biology they are reported to be involved in
2. Along the line with Major comment 2, the explanation for Fig 3D needs to be better elaborated, perhaps to include the role of proteasome already at this point (if the authors think this is the reason why basal BNIP3 levels remains lowl with USO1 and SAR1A KO).
3. Line 302-304, I believe that statement only refers to Fig S4C and the statement for Fig 5G is in the next sentence. Please remove Fig5G from line 304. It was confusing to read.
4. Line 367, there is a reference for Fig S5C but that figure is missing.
5. Line 410-411, are there any reported clinical cases of EMC mutations with phenotypes that could be explained by elevated mitophagy?

Significance

My expertise lies in organelle-selective autophagy and protein homeostasis. Overall, I think this is a very strong manuscript and the data are very solid. The work adds to our current understanding of the basal regulation of BNIP3 which was not previously explored. The novelty of this work lies in the unexpected regulation of BNIP3 via an autophagy-independent, lysosomal pathway and the observation has the potential to be extended to the regulation of the stability of other tail-anchored proteins. This is a very specialised study and will be of interest to the mitophagy and transmembrane protein regulation community.

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Referee #2

Evidence, reproducibility and clarity

Mitochondria are degraded by autophagy in a reaction that depends on mitophagy receptors, such as BNIP3 and BNIP3L/NIX. These receptors are regulated on the level of gene expression, but also on a post-translational level. This study elucidates the processes which control the levels of BNIP3 in a process that relies on the alternative distribution of the protein to different cellular compartments. BNIP3 is a tail-anchored protein that is inserted into the mitochondrial outer membrane and, alternatively, into the ER membrane. The authors show that insertion into the ER is dependent on the EMC complex and, to a lesser extent, on the GET complex. After insertion into the ER membrane, BNIP3 can be trafficked to lysosomes for degradation or, alternatively, be degraded by proteasomal proteolysis. This study provided evidence that the conditional distribution of BNIP3 to these different intracellular locations is used to control mitophagy even though the specific conditions which determine the alternative destinations remain largely unexplored. The study is of high technical quality, all important controls are shown, and the text is well written.

Specific points

1. The mechanism of the alternative distribution is not addressed here. Is the location of BNIP3 dependent on where the newly synthesized protein is initially targeted to (such as in the case of Pink1) or is there a constant redistribution and flux of the protein between the two membranes? This is an important aspect which should be experimentally addressed and some data to this should be already published as part of this study since this aspect is important for the final model proposed.
2. How is BNIP3 inserted into the outer membrane? A previous study from the Weissman lab proposed that MTCH2 serves as insertase. The authors did not mention MTCH1 and MTCH2 in context of Fig. 2B. Were these proteins not found? Did the authors test the relevance of MTCH2 in their assay? This aspect should be addressed and mentioned.
3. The authors show that BNIP3 on the ER is not stable but degraded by the proteasome. Does this require ERAD factors? Is the mitochondrial BNIP3 protein likewise degraded by proteasomal degradation? It is not clear whether both BNIP3 pools are constantly turned over or whether degradation exclusively/predominantly occurs on the ER surface.
4. The authors generated an interesting BNIP3 mutant with a C-terminal Fis1 anchor. This variant is constantly located in the outer membrane (which is shown here). The physiological consequence of the constitutive distribution on mitochondria is however only superficially studied. The authors should characterize this interesting mutant in some more depth.
5. The results of the screen shown in Fig . 2B are particularly interesting for readers. The glutathione peroxidase GPX4 was found as a top hit among the EMC components.GPX4 protects membranes (including those of mitochondria) against oxidative damage, is a major component of ferroptosis and linked to mitochondrial dysfunction and mitophagy. The authors should mention this interesting hit in the context of their discussion of the lipid-sensing properties of the dimerizing TM domains of BNIP3.

Significance

Many studies in the last years focused on the roles of Pink and Parkin in the context of mitophagy, a system that also relies on alternative protein targeting (in that case between the inner and outer membrane of mitochondria). The study here shows that BNIP3, another highly important mitophagy receptor, uses in principle a similar strategy, however, here the alternative targeting occurs between the mitochondrial outer membrane and the ER membrane. Mechanistic insights are provided, for example also into the different domains of BNIP3 and their relevance for targeting and mitophagy. The study therefore addresses an important aspect, is of excellent quality and will be of interest for a broad readership.

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Referee #1

Evidence, reproducibility and clarity

Recent work by several groups has revealed that NIX and BNIP3 levels can be regulated through ubiquitination, mediated by FBXL4, to restrict mitophagy. In this study, the authors identify an additional avenue for the regulation of BNIP3 levels involving the transfer BNIP3 from mitochondria to the ER and eventually into the endolysosomal system for degradation. In addition, the authors argue that most of BNIP3 turnover during mitophagy is through the newly identified ER pathway and not through mitophagy. There was little to no endolysosomal turnover observed for NIX, and therefore ethe authors predominantly focused on BNIP3. Key ER transfer factors required for BNIP3 endolysosomal turnover were identified through whole genome CRISPR/Cas screening, and include EMC3. Knockout of EMC3 results in slightly higher levels of mitophagy under basal conditions, and higher levels of mitophagy following proteasome inhibition with BTZ, supporting the overall conclusion that BNIP3 levels are regulated by lysosomal turnover.

Major Comments:

1. Across the manuscript, NIX levels appear to be unresponsive to most treatments in the MDA-MB-231 line, including hypoxia treatment. This is an unusual result and raises questions about the role of NIX in MDA-MB-231 line, mainly that BNIP3 is the primary driver of mitophagy in this system. Indeed, Figure 7D indicates that there is very little mitophagy contribution by NIX since knockout of BNIP3 is sufficient to abolish mitophagy almost completely. Therefore, the effects seen on mitophagy following EMC3 knockout in Figure 7 might be smaller in a line that is responsive to NIX mitophagy. It would be beneficial to analyse basal mitophagy flux in an additional cell line, for example U2OS (Fig S1E) in which NIX is responsive to hypoxia.
2. Following on from comment 1 above, Figure 7 would benefit with an analysis of hypoxia (or DFP, or cobalt chloride) stimulation of mitophagy to assess whether mitophagy levels are higher in EMC3 KOs. The authors argue that BNIP3 is trafficked to the ER during mitophagy and is not turned over by mitophagy itself, it would therefore be interesting to test if BNIP3 is prevented from being removed from mitochondria whether this would affect the rate or levels of mitophagy under stimulating conditions.
3. Continuing from comment 2, given that the authors conclude that BNIP3 is not turned over by mitophagy, can they examine whether BNIP3 is excluded from sealed mitophagosomes?
4. Figure 4B: The localisation of tf-BNIP3 is reminiscent of ER in BTZ treated samples. How much of the protein is on mitochondria in the presence of BTZ? Does MLN4924 cause a similar issue?
5. Is the BNIP3(FisTMD) expressed to equivalent levels to WT BFP-BNIP3? Given that the Fis1 form of BNIP3 cannot traffic to endolysosomes, its levels might be higher. In addition, overexpression of the BNIP3-Fis construct was used to make the argument that dimerization is not important for mitophagy. But the authors should also take into account the possibility that with overexpression, the potential efficiency afforded to mitophagy via dimerization of endogenous proteins may be negated, and therefore hidden. Given this, I don't think that the authors can confidently conclude that dimerization does not contribute to mitophagy, and that instead its main role is ER-endolysosomal turnover of BNIP3.
6. Can the authors assess whether BNIP3 that is on mitochondria is transferred to the ER (perhaps through photoswitchable GFP-BNIP, activated on mitos and then observe its transfer to ER)? This seems important in order to address the possibility that BNIP3 that is being turned over by the endolysosome is being delivered directly to the ER.

Minor comments:

1. Figure 3B: Are the red puncta observed in USO1 and SAR1A cells a product of higher levels of ER-phagy owing to BNIP3's high presence on the ER membrane?
2. Please include molecular weight markers for all western blots.
3. Figure 5A-G: These data do not make a convincing case for the role of dimerization and are very difficult to follow. Only the mislocalized S172A mutant was responsive to Baf treatment, while the LG swap mutant which is mitochondrial and cannot dimerize is unaffected by Baf treatment. Figure 5H-I utilise a construct of BNIP3 that is missing most of the protein and which has very low turnover (Figure 5B). Unfortunately these results don't make a highly convincing case about the biology of native, full length, mitochondrial BNIP3. The authors are advised to either strengthen the dimerization argument, or perhaps lighten the language around the main conclusions from these data.

Significance

Overall, this is a valuable and important study that provides an important new advance into how mitophagy is regulated by mitophagy receptors. It adds another layer of regulation in addition to the ubiquitin-proteasome mediated restriction of mitophagy reported by others. The data are predominantly convincing and make a strong argument for endolysomal turnover of BNIP3 to regulate its levels. This study will be of high interest to the field of mitophagy. There is also general interest to the field of mitochondrial biology that a TA mitochondrial (and peroxisomal) protein can be extracted from mitochondria, transferred to the ER, and eventually to the endolysosomal system.

Reviewer expertise: mitophagy mechanisms, autophagosome formation

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Reply to the reviewers

Reply to the reviewers

Dear Editor and reviewers,

We would like to thank the three reviewers for their thorough review of our manuscript and their detailed comments and very helpful suggestions to improve the manuscript. Overall, we thought the reviews were very positive with the reviewers commenting that our discovery of a novel genetic code variant is a “cause for celebration” and that our study is “technically solid” and “rigorous”. All three reviewers agree that our manuscript would “stimulate new discussions in the field of genetic code evolution” and also be of broad interest to evolutionary cell biologists, protistologists and the translation/protein synthesis community at large. The reviewers highlight the particular novelty of the genetic code variant described here due to it being an exception to the wobble hypothesis which adds a new level of complexity to stop-codon reassignment. The reviewers share our frustration about the lack of proteomics data due to being unable to establish a stable culture but acknowledge that we address this limitation frankly in our discussion and agree that it is “frustrating but it's not a limitation”.

We present an updated and improved version of the manuscript after taking on board the reviewers’ suggestions. Our point-by-point responses to their comments and our modifications are detailed below in bold.

Point-by-point description of the revisions

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

Summary

This study by J. McGowan and colleagues reports the discovery of a ciliate species that uses a variant genetic code where the codons UAA and UAG, which are stop codons in the canonical code, instead code for lysine and glutamate respectively. The primary data are genomic and transcriptomic sequence libraries from single cells. The genetic code was predicted by aligning coding sequences to references from other species and examining the most frequent amino acids in positions homologous to putative coding-UAA/UAGs. They also identified suppressor tRNAs for UAA and UAG, and tandem in-frame stop UGAs (but not UAA/UAG) in the 3'-UTR, which further support the recoding of UAA and UAG.

A limitation of this study (and several other recent studies on variant genetic codes) is that the predictions are based on nucleic acid sequencing, without confirmation from proteomics. The authors acknowledge and briefly but frankly discuss the limitations in their manuscript (lines 258-261).

Major comments

Controls against contamination and sequence chimeras

The ciliate species studied here was an environmental isolate, and sequence libraries were prepared by amplification from small pools of cells sorted by FACS. The genome assembly was produced by co-assembly of multiple amplified libraries. Given the potential for contamination and amplification artefacts (such as sequence chimeras) associated with these methods, I think it is important to demonstrate that the data truly originate from one species, so as to rule out the possibility that the co-assembly may be chimeric, i.e. representing two or more organisms with different genetic codes (one with UAA recoded and the other with UAG recoded, for instance). Even if the cell sorting was accurate, contamination could still enter down the line during library preparation so it would be important to show internal evidence from the sequence data too.

We understand the reviewer's concerns about the possibility of contamination as it can be a major issue in environmental single cell sequencing experiments. We have addressed the individual points below in detail to demonstrate that we have generated a clean genome assembly of a single ciliate species but also summarise here:

• The cells we sequenced originated from the same clonally isolated cell propagated in culture
• We have manually curated the assembly
• The assembly has a unimodal GC content peak with a low BUSCO duplication score
• Most genes (95.9 %) contain both in-frame UAA and UAG codons
• We recovered a single identical ciliate 18S rRNA gene across all 10 samples
• De novo assemblies of the 10 individual gDNA libraries are virtually identical in terms of average nucleotide identity
• We also predicted the genetic code for each of the genome and transcriptome samples individually

• 85% of the final assembly is taxonomically classified as Ciliophora. The remainder is either unclassified (i.e. no hits) or has spurious/inconsistent hits

  Specifically:

(a) From the description in Methods under "Sampling, Ciliate isolation, culturing, and cell-sorting", it is not clear whether all the cells that were ultimately sequenced originated from the same clone (i.e. the same well in the 96-well plate described in line 389). Could the authors confirm whether this was the case?

Yes. All the sorted cells originated from the same ciliate clone. A single-cell was isolated and cleaned (without removing all the environmental bacteria). The ciliate single-cell divided and we established a mono-clonal ciliate culture that we used for the cell sorting and sequencing. This culture grew but only for a relatively short period. We could not establish a long term culture.

(b) What % of genes have in-frame coding UAA, UAG, or both? How per gene on average? Counts are given for the conserved genes/domains identified by PhyloFisher or Codetta (lines 192-207), and overall frequencies per codon are addressed later in lines 263 onward, but how often do they occur together in the same genes?

My reasoning behind this is that if genes with both in-frame coding UAA and UAGs are common then it is very unlikely to be the result of chimeric sequence artefacts from whole-genome amplification.

We have updated the text to include this information. From the PhyloFisher analysis, we had reported that 58 genes contained in-frame UAA codons and 46 genes contained in-frame UAG codons. We have now added the text “Amongst the genes identified by PhyloFisher, 27 contained both an in-frame UAA codon and an in-frame UAG codon.”

Additionally, from our annotated gene set, we had reported that 98.6% of genes contain at least one UAA codon and 96.4% of genes contain at least one UAG codon. We have now added text to report how many genes contain both codons “The reassigned codons are widely used across genes with 95.9% of genes containing both a UAA codon and a UAG codon”.

The example gene (tubulin gamma chain protein) shown in Figure 1 contains both in-frame UAA codons and in-frame UAG codons, with the UAA codons aligning to lysine and the UAG codons to glutamic acid.

(c) What is the sequence identity of conserved marker sequences between the individual amplified replicate libraries?

I would naively expect that individual replicates may not have the full set of markers because of uneven amplification, but if the sequences originate from the same clone they should have overlapping coverage of the conserved markers, and these should be +/- identical between replicates (save for allele variants). If so this would support the claim that contaminant sequences were mostly removed during sequence QC and that the cells were clonal.

We generated an individual assembly for each of the 10 gDNA libraries and calculated average nucleotide identity at the whole assembly level. On average, the 10 assemblies are 99.43% identical to each other, with the least similar pair being 99.37% identical to each other. This level of variation includes not only allelic variants but also sequencing/assembly errors as the individual libraries are relatively low coverage. In terms of assembly alignment coverage (i.e. the fraction of each assembly that is aligned to another assembly), the average value is 76.5% and the value for the lowest pair is 59.1%. We have now also made the individual 10 assemblies available in the Zenodo repository (10.5281/zenodo.7944379) and updated the methods section.

Furthermore, as an additional quality control step, we predicted the genetic code for each of the 10 individual genome assemblies and obtained the same predictions that UAA encodes lysine and UAG encodes glutamic acid for all 10 individual assemblies. We also predicted the genetic code for each individual RNA-Seq sample based on individual transcriptome assemblies which yielded consistent predictions.

(d) Line 392: "Non-axenic" presumably refers to environmental prokaryotes. This also appears to contradict the statement that the cells were "free of any other contaminant" (line 387). Could authors confirm whether they mean "non-axenic but monoeukaryotic"?

In line 387, when we say "free of any other contaminant” we mean that we isolated a ciliate single-cell from the environmental sample, and the picked ciliate cell was washed 3 times until it was free of any other eukaryotes, but still containing environmental bacteria. In line 392, when we say non-axenic, we mean that the mono-clonal ciliate culture contained environmental bacteria and was monoeukaryotic.

We have modified the text in the methods section to say “free from any other eukaryote” and “non-axenic but monoeukaryotic”.

(e) Lines 448-451: More details should be given on the criteria used to identify and bin out contaminants. MetaBAT typically bins prokaryotic genomes quite well, but not eukaryotic ones. What did the bins look like and how were the eukaryotic ones chosen?

We routinely use MetaBAT2 to assist with separating bacterial contigs from protist genomes. From our experience we find that it generally performs well but requires careful manual curation. We only use tetranucleotide frequencies when binning single-cell assemblies and not coverage variance as this is heavily skewed due to amplification bias from single-cell amplification. We integrated the binning results from MetaBAT2 with taxonomic classification from tools such as CAT, Blobtools and Tiara, and manually curated the assembly.

We have modified both the results and methods section to clarify that the assembly was manually curated to remove contaminant contigs.

For example, using CAT, which taxonomically classifies contigs based on blast/diamond hits to open reading frames:

The final curated assembly is 69.7 Mb in length.

59.5 Mb (85.4%) is classified as Ciliophora.

9.7 Mb (13.9%) is unclassified.

The remaining 0.5 Mb (0.7%) have inconsistent, low-identity hits to 22 different Eukaryotic and Bacterial phyla (due to lack of closely related species in public databases).

Furthermore, we recovered only a single ciliate 18S rRNA gene and the final curated assembly has a unimodal GC content peak with a low BUSCO duplication score and high cDNA mapping rate.

__Minor comments __

Line 52: Not strictly true, some germline-limited segments contain mobile elements with coding sequences, e.g. TBE elements in Oxytricha (doi:10.1371/journal.pgen.1003659)

Thank you for pointing this out. We have rephrased “excision of non-coding sequences” to “excision of micronucleus-limited sequences” to describe the process of macronuclear development more generally.

Lines 229-231, Supplementary Table 1: Presenting the identity matrix as a distance tree may make it easier to see the pattern of similarity between the tRNAs

We have added a phylogenetic network of tRNA genes as a supplementary figure to better visualise the relationships between tRNA genes.

Lines 274-275: Suggest stating the criterion for classifying genes as "highly expressed" on the first mention of this in the Results, although it's explained later on in the Methods.

We have clarified this in the results section by adding the text: ‘We defined a subset of genes as “highly expressed” based on the 10% of genes with the highest transcripts per million (TPM) values for comparison below.’

Lines 298-299: What is the frequency of tandem UGA stops in the 3'-UTR in genes with coding-UAA/UAG vs. genes without, and is there a significant difference? The argument in this paragraph is that UAA+UAG reassignment increases selective pressure to minimize translational readthrough. Therefore I think that it would make sense to compare the frequency in genes with and without these codons.

Following the reviewer’s suggestion, we have looked at tandem UGA stop codons in the 3’-UTR of genes that don’t use UAA and genes that don’t use UAG. We found similar enrichment for in-frame UGA codons at the beginning of the 3’-UTR in these small subsets of genes.

To clarify, the hypothesis from the literature is that there may be stronger selective pressure to maintain tandem stop codons in ciliates with reassigned genetic codes, particularly those that use only UGA as a stop codon. Within a genome, we wouldn’t expect a difference if a gene contains UAA/UAG codons.

Lines 353-354, Figure 5: Suggest marking the internal nodes where genetic code changes likely occurred. At the moment only the leaves of the tree are annotated with the genetic codes of the respective species. This would make it clearer how one counts the numbers of independent origins as reported in the text (e.g. "... a fourth independent origin of UGA being translated as tryptophan").

We have decided not to label the internal nodes on the phylogeny. We think that deeper sampling will reveal that some of these genetic code changes occurred independently, so we don’t want the figure to be misleading. Also, for the species with the genetic code UAA=Q, UAG=Q and UGA=W, we can’t determine the order of events.

Lines 371-372: Question out of curiosity (not necessary to address for the manuscript at hand): Do the authors think the recoding of UAA and UAG happened simultaneously in both codons or stepwise, or is there insufficient information to speculate?

An initial guess would be that it happened as a stepwise process but without deeper sampling of this lineage it is not possible to determine the order of events.

This highlights the need for deeper sampling and sequencing across undersampled lineages of ciliates and demonstrates the utility of single-cell OMICs approaches for species that are not yet amenable to culturing.

Line 395: "10uL" should use the actual symbol for "micro" prefix. Also, the choice of spacing or no spacing between numerical figure and units should be made consistent in manuscript.

Fixed

Line 403: "Biotynilated" should be "Biotinylated"

Fixed

Line 414 and elsewhere: "2" in MgCl2 should be subscripted

Fixed

Lines 419-420: Clarify whether the "r" and "+" symbols are to be read as prefixes or suffixes, i.e. is the modified base the preceding or succeeding one.

We have clarified in the text that these symbols are to be read as prefixes.

Table 1: What is the difference between the two sets of BUSCO completeness scores reported? One is given under "Genome assembly" and the other under "Genome annotation", but the annotation is based on the same assembly, right? I'm assuming this has to do with different modes in which BUSCO can be run, but this should be explained in the Methods (lines 452-453, 496-497) and briefly explained in the Table caption.

Yes this is because we ran BUSCO in two different modes. BUSCO is run in genome mode on the genome assembly and in protein mode on the genome annotation. In genome mode gene prediction is performed by Augustus guided by amino acid BUSCO group block-profiles while in protein mode the gene set described in our methods is the input to BUSCO classification. The superior BUSCO results for the protein mode reflect the superiority of our final annotation over that generated by BUSCO Augustus. We have added text to the methods section and to the table caption to clarify which mode was used.

**Referee Cross-commenting** I generally agree with the other reviewers' comments. Specifically I like reviewer #3's suggestion #3 to have a more detailed summary of the codon frequencies, perhaps as a graphic, and to compare the tandem stop frequencies with other ciliate species, especially those with all three canonical stops.

Reviewer #1 (Significance (Required)):

Any new genetic code variant discovered is a cause for celebration! This is a basic biological fact with inherent significance and should be generally interesting to biologists because the rarity of variant codes stands in contrast to the diversity of most biological systems.

This variant code would also stimulate new discussions in the field of genetic code evolution specifically because, as the authors point out, when both UAA and UAG are recoded they both usually encode same amino acid, but here they are recoded to different ones. This is an apparent exception to the "wobble" hypothesis for why these codons often evolve in concert, which was well explained with relevant citations in the Introduction.

For context: My expertise is in genomics and environmental microbiology.

END reviewer 1

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

This study reports the reassignment of the UAA and UAG stop codons to lysine and glutamic acid, respectively, in the ciliate Oligohymenophorea sp PL0344. The paper is nicely written, easy to read and the experimental approach, ideas and questions are easy to follow. The work is technically solid both at the NGS - in house library preparation, sequencing and data interpretation - as well as phylogeny levels. The conclusions are consistent with the comparative genomic and transcriptomic data obtained by the study.

__Reviewer #2 (Significance (Required)): __

The work extends current knowledge on codon reassignment in ciliates, confirming previous discoveries of existence of very high stop codon assignment flexibility in these organisms. The assignment of UAA and UAG to two different amino acids by two different tRNAs is very interesting and reinforces the idea that stop codon reassignment in ciliates is rather common. It also raises important questions about the parallel evolution of the release factor-1 (eRF1), Lysine and Glutamine tRNAs, as the reassignment requires loss of recognition of both UAA and UAG by eRF1 with parallel appearance of the new Lysine and Glutamic Acid suppressor tRNAs.

The main issue of this work is the inability to cultivate the ciliate Oligohymenophorea sp PL0344 in the laboratory to prepare protein extracts for direct analysis of the amino acids inserted at UAA and UAG sites by Mass Spectrometry. The comparative genomic and transcriptomic data, as well as the identification of cognate tRNA anticodons for UAA and UAG, are likely correct, but provide indirect evidence for the assignment of UAA to Lysine and UAG to Glutamic Acid. This issue is relevant because one cannot exclude the possibility of insertion of other amino acids at UAA and UAG sites beyond Lysine and Glutamic acid, respectively; nor can one exclude the possibility that such amino acids are inserted at high level. The authors do acknowledge the limitations of the unavailability of protein extracts for direct MS analysis of the reassignment, but should consider, in particular in the discussion, the possibility of multiple amino acid insertions in a context where Lysine and Glutamine Acid are the major but not the only amino acid species being inserted at those sites.

Based on my expertise of studying codon reassignments in fungi of the CTG clade, I believe this work is very interesting and appealing to the genetic code community, and is of relevance to the evolution and protein synthesis research communities at large.

We thank the reviewer for their positive review. They raise an important point about the possibility of amino acids other than lysine and glutamic acid being inserted for UAA/UAG codons which we hadn’t considered. We have added text and relevant references to our discussion to highlight this possibility:

“Additionally, while the genomic and transcriptomic data provide strong evidence that lysine and glutamic acid are the major translation products of UAA and UAG codons, respectively, we cannot rule out the possibility that other amino acids are (mis)incorporated at these sites which could be detected using mass-spectrometry [38, 39].”

Krassowski T, Coughlan AY, Shen X-X, Zhou X, Kominek J, Opulente DA, et al. Evolutionary instability of CUG-Leu in the genetic code of budding yeasts. Nat Commun. 2018;9:1887. Mordret E, Dahan O, Asraf O, Rak R, Yehonadav A, Barnabas GD, et al. Systematic Detection of Amino Acid Substitutions in Proteomes Reveals Mechanistic Basis of Ribosome Errors and Selection for Translation Fidelity. Molecular Cell. 2019;75:427-441.e5.

END reviewer 2

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

Summary: from genome and transcriptome sequencing of what appears to be a novel ciliate from the class Oligohymenophorea, McGowan et al provide convincing evidence of a protist in which the stop codons UAA and UAG have almost certainly been recoded to specify incorporation of different amino acids (UAA = K; UAG = E) during translation. Several ciliates from different classes use a non-standard genetic code (as do a narrow variety of other protists), but this is an unusual observation in that stop codons which differ only in the wobble position code for different amino acids in the ciliate identified here.

I say 'almost certainly' the stop codons have been recoded in Oligohymenophorea sp. PL0344 because in the absence of being able to retain the ciliate in culture the authors have not been able to complete the proteomics which would unequivocally (a) show stop codons now code for amino acids and (b) confirm the identity of the amino acids now encoded (the authors discuss this issue on p12).

Comments: overall this manuscript is straightforward to read and the analyses realistically taken as far as is realistic in the absence of a continuous culture method. My suggested revisions should be straightforward for the authors to address.

1) The manuscript appears to report the identification and genome/transcriptome sequencing of a novel ciliate species - clarity should be provided by the authors. However, it disappointed me that this manuscript was crafted entirely from nucleotide sequencing. I would have welcomed seeing the morphology of the ciliate identified here and would have anticipated that there was sufficient material to perform microscopy at the light level (for DIC images) and by scanning or transmission electron microscopy.

Yes, based on the 18S rRNA sequence and phylogenies of protein-coding genes, this is a novel species that hasn’t been described before. The most similar hits to the 18S rRNA gene are to other unnamed/environmental sequences. We haven’t attempted to name or describe this species as we weren’t able to establish a culture, so have referred to it as Oligohymenophorea sp. PL0344. We have clarified in the text that this is a novel, unnamed ciliate species.

The genomic and transcriptomic data was generated from a single cell isolate propagated into micro-cultures of 10’s of cells. These were done in the strictest conditions in an attempt to minimise contamination. Consistent with this approach it was not possible to obtain useful SEM/TEM as it would be very hard to recover EM imaging from 10’s of cells (a process that would have drastically reduced our ability to do replete genome sampling). Similarly, our approach to culturing limited our ability to acquire useful DIC images. After discovering that this ciliate uses a novel genetic code, we attempted on a number of occasions to re-isolate the same species from the same and surrounding water bodies but failed.

2) It is unfortunate that the ciliate could not be maintained in culture (or cryopreserved). Coordinates for the University Parks pond are provided, but I got the impression that this ciliate could be repeatedly isolated. Thus, in the absence of culture methods could the authors indicate the points in the year when the ciliate could be isolated (i.e. is there a season element to when PL0344 could be isolated) and how frequently when sampling was performed could PL0344 be seen? From the environmental sequence data that is publicly available is there any evidence for the presence of PL0344 anywhere else in the world? I'd be surprised if this was a UK-specific ciliate.

The water sample from which this ciliate was isolated was collected in April 2021. After having sequenced its genome and identifying the genetic code change, we made several attempts to reisolate it from the same pond but were unsuccessful. Regarding the geographic distribution of this ciliate, in the text we mention that the most similar 18S rRNA sequence in GenBank is to an unnamed species recovered in a metabarcoding study in France with 99.81% identity. We assume that this is the same species. We also examined other publicly available environmental datasets such as the PR2/metaPR2 database. The most similar match in the metaPR2 database was to a sequence “OLIGO4_XX_sp”. In the metaPR2 database this sequence is unique to Lake Garda in Italy (sample name: “Lake_Garda-LTER-euphotic-water”). However, this hit was only 98% identical with a partial alignment so we did not discuss it in the text. We agree that it is very unlikely that this is a UK-specific ciliate but cannot determine its geographic range based on the publicly available environmental sequence data, other than the single hit to a sequence from France. We think it is important to stress that it was not the aim of our paper to describe the taxonomy and biogeographical range of this ciliate but rather to report the exciting shift in codon usage.

3) I felt the statistics presented on pages 13-14 (lines 277-301) for codon usage were a little superficial. It would be helpful to see how frequently other E and K codons are used in PL0344 and ideally to see how similar codon usage differs in the more model ciliates Paramecium, Tetrahymena or Stentor. To complete an analysis and justify/confirm conclusions drawn, I would also like to see how frequently in-frame, downstream stop codons are seen in ciliates where stop codons have NOT been reassigned - although the data in Fig 5 indicates genome/transcriptome sequences are not necessarily complete for many ciliate species (where stop codons are not reassigned), there is certainly more varied data to look at than when Fleming and Cavalcanti published their PLoS One work (which is cited in the manuscript).

We have shortened this section about UAA and UAG usage, with supplementary table 3 showing usage of all codons in all genes compared to our subset of highly expressed genes.

We have also added a sentence stating how many genes contain both in-frame UAA and UAG codons based on the point from Reviewer 1: “The reassigned codons are widely used across genes with 95.9% of genes containing both a UAA codon and a UAG codon.“

According to our knowledge, there are no new genome assemblies available for ciliates that use the canonical genetic code since the Fleming and Cavalcanti publication from 2019, certainly not any with annotated gene sets available for comparison. The species in Fig 5 which use the canonical genetic code are all from transcriptome data (other than Stentor) that have generally low completeness. We do not think comparison with low-quality transcriptome assemblies would make a fair comparison as they would be biased towards transcripts with higher expression. Furthermore, they likely include many fragmented transcripts which are not suitable for detailed comparisons of the stop codon/3-UTR region.

4) Given the presence of just one stop codon in PL0344 have the authors looked genome-wide at nucleotide composition 5' and 3' to UGA. The nucleotide sequences 5' and 3' to a stop can influence whether read through is and thus potentially limits the frequency of or tendency for unwanted readthrough?

We thank the reviewer for this suggestion which is something we did not investigate initially but have now added a short section in the manuscript to address. Many studies in model organisms have demonstrated that UGA is the least robust stop codon and the most prone to read through. As the reviewer alludes to, this is particularly interesting for ciliates with reassigned genetic codes that use only UGA as a stop codon. Experimental data from model organisms have shown that the sequence composition surrounding a stop codon can influence the frequency of read through, with the nucleotide immediately downstream of the stop codon (“+4 position”) being particularly important.

We have now looked at the sequence composition around stop codons for Oligohymenophorea sp. PL0344 and our results show that cytosine tends to be avoided following the UGA stop codon. From the literature, presence of a cytosine following UGA (i.e., UGAC) leads to a substantial increase in translational read through. Furthermore, when examining the subset of highly expressed genes, there are significantly fewer cases of UGAC when compared to all genes. This trend has previously been reported in Paramecium and Tetrahymena based on EST data (Salim, Ring and Cavalcanti; 2008).

We have added a short section to the text reporting this and a supplementary figure showing a sequence frequency logo around the stop codon for all genes and for the subset of highly expressed genes. We are very cautious, however, that there is a paucity of experimental studies investigating stop codon robustness in ciliates. While several publications hypothesise that read through may happen at higher rates in ciliates due to a combination of factors (e.g., ERF-1 mutations, presence of tandem stop codons, competition from suppressor/near-cognate tRNA genes, etc..) we are careful not to speculate without experimental evidence.

__Reviewer #3 (Significance (Required)): __

Strengths - I found this a straightforward manuscript to read - aside from the interesting and unexpected observation about genetic code use in PL0344, Fig 5 draws together a lot of earlier published information into an easily accessible form - I felt this a particularly useful part of the manuscript.

I don't feel the absence of proteomics to back up the genome/transcriptome analysis is a notable limitation - it's perhaps frustrating but it's not a limitation. However, the work does perhaps inevitably feel a little bit observational - there's not really a lot of insight or new insight into why the genetic code can be revised in some microbial eukaryotes - in contrast, for instance, to a recently published study of the aptly named Blastocrithidia nonstop. McGowan et al's manuscript, however, will be of interest and should be formally published.

Descriptions of organisms that have tweaked the standard genetic code are not new; coupled to the limited insight into why the genetic code can be rewritten so readily in ciliates, this limits the general appeal of the work. However, the study executed is rigorous and it should be of interest to a wide variety of protistologists, evolutionary cell biologists, and researchers in the translation field.

END reviewer 3

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Referee #3

Evidence, reproducibility and clarity

Summary: from genome and transcriptome sequencing of what appears to be a novel ciliate from the class Oligohymenophorea, McGowan et al provide convincing evidence of a protist in which the stop codons UAA and UAG have almost certainly been recoded to specify incorporation of different amino acids (UAA = K; UAG = E) during translation. Several ciliates from different classes use a non-standard genetic code (as do a narrow variety of other protists), but this is an unusual observation in that stop codons which differ only in the wobble position code for different amino acids in the ciliate identified here.

I say 'almost certainly' the stop codons have been recoded in Oligohymenophorea sp. PL0344 because in the absence of being able to retain the ciliate in culture the authors have not been able to complete the proteomics which would unequivocally (a) show stop codons now code for amino acids and (b) confirm the identity of the amino acids now encoded (the authors discuss this issue on p12).

Comments: overall this manuscript is straightforward to read and the analyses realistically taken as far as is realistic in the absence of a continuous culture method. My suggested revisions should be straightforward for the authors to address.

1. The manuscript appears to report the identification and genome/transcriptome sequencing of a novel ciliate species - clarity should be provided by the authors. However, it disappointed me that this manuscript was crafted entirely from nucleotide sequencing. I would have welcomed seeing the morphology of the ciliate identified here and would have anticipated that there was sufficient material to perform microscopy at the light level (for DIC images) and by scanning or transmission electron microscopy.
2. It is unfortunate that the ciliate could not be maintained in culture (or cryopreserved). Coordinates for the University Parks pond are provided, but I got the impression that this ciliate could be repeatedly isolated. Thus, in the absence of culture methods could the authors indicate the points in the year when the ciliate could be isolated (i.e. is there a season element to when PL0344 could be isolated) and how frequently when sampling was performed could PL0344 be seen? From the environmental sequence data that is publicly available is there any evidence for the presence of PL0344 anywhere else in the world? I'd be surprised if this was a UK-specific ciliate.
3. I felt the statistics presented on pages 13-14 (lines 277-301) for codon usage were a little superficial. It would be helpful to see how frequently other E and K codons are used in PL0344 and ideally to see how similar codon usage differs in the more model ciliates Paramecium, Tetrahymena or Stentor. To complete an analysis and justify/confirm conclusions drawn, I would also like to see how frequently in-frame, downstream stop codons are seen in ciliates where stop codons have NOT been reassigned - although the data in Fig 5 indicates genome/transcriptome sequences are not necessarily complete for many ciliate species (where stop codons are not reassigned), there is certainly more varied data to look at than when Fleming and Cavalcanti published their PLoS One work (which is cited in the manuscript).
4. Given the presence of just one stop codon in PL0344 have the authors looked genome-wide at nucleotide composition 5' and 3' to UGA. The nucleotide sequences 5' and 3' to a stop can influence whether read through is and thus potentially limits the frequency of or tendency for unwanted readthrough?

Significance

Strengths - I found this a straightforward manuscript to read - aside from the interesting and unexpected observation about genetic code use in PL0344, Fig 5 draws together a lot of earlier published information into an easily accessible form - I felt this a particularly useful part of the manuscript.

I don't feel the absence of proteomics to back up the genome/transcriptome analysis is a notable limitation - it's perhaps frustrating but it's not a limitation. However, the work does perhaps inevitably feel a little bit observational - there's not really a lot of insight or new insight into why the genetic code can be revised in some microbial eukaryotes - in contrast, for instance, to a recently published study of the aptly named Blastocrithidia nonstop. McGowan et al's manuscript, however, will be of interest and should be formally published.

Descriptions of organisms that have tweaked the standard genetic code are not new; coupled to the limited insight into why the genetic code can be rewritten so readily in cliates, this limits the general appeal of the work. However, the study executed is rigorous and it should be of interest to a wide variety of protistologists, evolutionary cell biologists, and researchers in the translation field.

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Referee #2

Evidence, reproducibility and clarity

This study reports the reassignment of the UAA and UAG stop codons to lysine and glutamic acid, respectively, in the ciliate Oligohymenophorea sp PL0344. The paper is nicely written, easy to read and the experimental approach, ideas and questions are easy to follow. The work is technically solid both at the NGS - in house library preparation, sequencing and data interpretation - as well as phylogeny levels. The conclusions are consistent with the comparative genomic and transcriptomic data obtained by the study.

Significance

The work extends current knowledge on codon reassignment in ciliates, confirming previous discoveries of existence of very high stop codon assignment flexibility in these organisms. The assignment of UAA and UAG to two different amino acids by two different tRNAs is very interesting and reinforces the idea that stop codon reassignment in ciliates is rather common. It also raises important questions about the parallel evolution of the release factor-1 (eRF1), Lysine and Glutamine tRNAs, as the reassignment requires loss of recognition of both UAA and UAG by eRF1 with parallel appearance of the new Lysine and Glutamic Acid suppressor tRNAs.

The main issue of this work is the inability to cultivate the ciliate Oligohymenophorea sp PL0344 in the laboratory to prepare protein extracts for direct analysis of the amino acids inserted at UAA and UAG sites by Mass Spectrometry. The comparative genomic and transcriptomic data, as well as the identification of cognate tRNA anticodons for UAA and UAG, are likely correct, but provide indirect evidence for the assignment of UAA to Lysine and UAG to Glutamic Acid. This issue is relevant because one cannot exclude the possibility of insertion of other amino acids at UAA and UAG sites beyond Lysine and Glutamic acid, respectively; nor can one exclude the possibility that such amino acids are inserted at high level. The authors do acknowledge the limitations of the unavailability of protein extracts for direct MS analysis of the reassignment, but should consider, in particular in the discussion, the possibility of multiple amino acid insertions in a context where Lysine and Glutamine Acid are the major but not the only amino acid species being inserted at those sites.

Based on my expertise of studying codon reassignments in fungi of the CTG clade, I believe this work is very interesting and appealing to the genetic code community, and is of relevance to the evolution and protein synthesis research communities at large.

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Referee #1

Evidence, reproducibility and clarity

Summary

This study by J. McGowan and colleagues reports the discovery of a ciliate species that uses a variant genetic code where the codons UAA and UAG, which are stop codons in the canonical code, instead code for lysine and glutamate respectively. The primary data are genomic and transcriptomic sequence libraries from single cells. The genetic code was predicted by aligning coding sequences to references from other species and examining the most frequent amino acids in positions homologous to putative coding-UAA/UAGs. They also identified suppressor tRNAs for UAA and UAG, and tandem in-frame stop UGAs (but not UAA/UAG) in the 3'-UTR, which further support the recoding of UAA and UAG.

A limitation of this study (and several other recent studies on variant genetic codes) is that the predictions are based on nucleic acid sequencing, without confirmation from proteomics. The authors acknowledge and briefly but frankly discuss the limitations in their manuscript (lines 258-261).

Major comments

Controls against contamination and sequence chimeras

The ciliate species studied here was an environmental isolate, and sequence libraries were prepared by amplification from small pools of cells sorted by FACS. The genome assembly was produced by co-assembly of multiple amplified libraries. Given the potential for contamination and amplification artefacts (such as sequence chimeras) associated with these methods, I think it is important to demonstrate that the data truly originate from one species, so as to rule out the possibility that the co-assembly may be chimeric, i.e. representing two or more organisms with different genetic codes (one with UAA recoded and the other with UAG recoded, for instance). Even if the cell sorting was accurate, contamination could still enter down the line during library preparation so it would be important to show internal evidence from the sequence data too.

Specifically:

• (a) From the description in Methods under "Sampling, Ciliate isolation, culturing, and cell-sorting", it is not clear whether all the cells that were ultimately sequenced originated from the same clone (i.e. the same well in the 96-well plate described in line 389). Could the authors confirm whether this was the case?
• (b) What % of genes have in-frame coding UAA, UAG, or both? How per gene on average? Counts are given for the conserved genes/domains identified by PhyloFisher or Codetta (lines 192-207), and overall frequencies per codon are addressed later in lines 263 onward, but how often do they occur together in the same genes?

My reasoning behind this is that if genes with both in-frame coding UAA and UAGs are common then it is very unlikely to be the result of chimeric sequence artefacts from whole-genome amplification. - (c) What is the sequence identity of conserved marker sequences between the individual amplified replicate libraries?

I would naively expect that individual replicates may not have the full set of markers because of uneven amplification, but if the sequences originate from the same clone they should have overlapping coverage of the conserved markers, and these should be +/- identical between replicates (save for allele variants). If so this would support the claim that contaminant sequences were mostly removed during sequence QC and that the cells were clonal. - (d) Line 392: "Non-axenic" presumably refers to environmental prokaryotes. This also appears to contradict the statement that the cells were "free of any other contaminant" (line 387). Could authors confirm whether they mean "non-axenic but monoeukaryotic"? - (e) Lines 448-451: More details should be given on the criteria used to identify and bin out contaminants. MetaBAT typically bins prokaryotic genomes quite well, but not eukaryotic ones. What did the bins look like and how were the eukaryotic ones chosen?

Minor comments

Line 52: Not strictly true, some germline-limited segments contain mobile elements with coding sequences, e.g. TBE elements in Oxytricha (doi:10.1371/journal.pgen.1003659)

Lines 229-231, Supplementary Table 1: Presenting the identity matrix as a distance tree may make it easier to see the pattern of similarity between the tRNAs

Lines 274-275: Suggest stating the criterion for classifying genes as "highly expressed" on the first mention of this in the Results, although it's explained later on in the Methods.

Lines 298-299: What is the frequency of tandem UGA stops in the 3'-UTR in genes with coding-UAA/UAG vs. genes without, and is there a significant difference? The argument in this paragraph is that UAA+UAG reassignment increases selective pressure to minimize translational readthrough. Therefore I think that it would make sense to compare the frequency in genes with and without these codons.

Lines 353-354, Figure 5: Suggest marking the internal nodes where genetic code changes likely occurred. At the moment only the leaves of the tree are annotated with the genetic codes of the respective species. This would make it clearer how one counts the numbers of independent origins as reported in the text (e.g. "... a fourth independent origin of UGA being translated as tryptophan").

Lines 371-372: Question out of curiosity (not necessary to address for the manuscript at hand): Do the authors think the recoding of UAA and UAG happened simultaneously in both codons or stepwise, or is there insufficient information to speculate?

Line 395: "10uL" should use the actual symbol for "micro" prefix. Also, the choice of spacing or no spacing between numerical figure and units should be made consistent in manuscript.

Line 403: "Biotynilated" should be "Biotinylated"

Line 414 and elsewhere: "2" in MgCl2 should be subscripted

Lines 419-420: Clarify whether the "r" and "+" symbols are to be read as prefixes or suffixes, i.e. is the modified base the preceding or succeeding one.

Table 1: What is the difference between the two sets of BUSCO completeness scores reported? One is given under "Genome assembly" and the other under "Genome annotation", but the annotation is based on the same assembly, right? I'm assuming this has to do with different modes in which BUSCO can be run, but this should be explained in the Methods (lines 452-453, 496-497) and briefly explained in the Table caption.

Referee Cross-commenting

I generally agree with the other reviewers' comments. Specifically I like reviewer #3's suggestion #3 to have a more detailed summary of the codon frequencies, perhaps as a graphic, and to compare the tandem stop frequencies with other ciliate species, especially those with all three canonical stops.

Significance

Any new genetic code variant discovered is a cause for celebration! This is a basic biological fact with inherent significance and should be generally interesting to biologists because the rarity of variant codes stands in contrast to the diversity of most biological systems.

This variant code would also stimulate new discussions in the field of genetic code evolution specifically because, as the authors point out, when both UAA and UAG are recoded they both usually encode same amino acid, but here they are recoded to different ones. This is an apparent exception to the "wobble" hypothesis for why these codons often evolve in concert, which was well explained with relevant citations in the Introduction.

For context: My expertise is in genomics and environmental microbiology.

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Reply to the reviewers

1. General Statements [optional]

Thank you for your letter dated on May 5, 2023 concerning our manuscript (MS# RC-2023-01906) entitled “Activation of Nedd4L Ubiquitin Ligase by FCHO2-generated Membrane Curvature.”

We thank the reviewers for their constructive comments and suggestions. We have considered all reviewers’ comments and plan to revise our manuscript accordingly.

We believe that our revision plan will greatly improve the quality of our manuscript.

1. Description of the planned revisions

__Reviewer #1 __

I enjoyed reading the paper by Sakamoto and colleagues, where they show that Nedd4L ubiquitin ligase activity is stimulated by membranes and in particular positive membrane curvature. This paper is a conceptual advance that hopefully will be extended by many other groups where membranes topology participates in the activation of associated enzymes, giving rise to added complexity but also specificity and further compartmentalization. It is an important paper for all cell biologists to understand.

1. My comments are all relatively minor and I hope can improve the readability of the paper, but will not alter the overall conclusion as this is well backed up. In general I would like to see more/better statistics/quantitation and better figure legends. I found that often one had to read the paper to understand a figure where reading the figure legend should suffice.

__Reply: __According to the reviewer’s comment, we will quantify the experiments (Fig. 1C, Fig. 2, Fig. 9B, and Fig. 10B) and add descriptions of statistics (Fig. 5, Fig. 6, B and D, and Fig. 7C). We will also write better figure legends to enable the readers to easily understand experiments.

1. This paper reminds me of a paper from Gilbert Di Paolo's lab on the activation of synaptojanin PIP2 hydrolysis by high membrane curvature. One would expect that there may be many such proteins whose activities will be dependent on their membrane environment. I find it conceptually rather likely that a protein which interacts with membranes via a C2 domain (which has membrane insertions and will thus likely be curvature sensitive) will likely show some positive curvature sensitivity. Can I suggest this paper is referenced and discussed in the light of the discussion statement "Thus, our findings provide a new concept of signal transduction in which a specific degree of membrane curvature serves as a signal for activation of an enzyme that regulates a number of substrates."

Reply: __According to the reviewer’s comment, we will cite the paper entitled “synaptojanin-1-mediated PI(4,5)P2 hydrolysis is modulated by membrane curvature and facilitates membrane fission” by Chang-Ileto et al. (Dev. Cell __20, 206–18 , 2011). We will also discuss this paper in the light of the discussion statement.

1. Where the paper could be improved (or I have not understood fully). In figure 1 there is a robust endocytosis of ENaC that is FCHo2 and Nedd4L sensitive. There is a rescue for FCHo2 in a fluorescence image (unquantified), so it would be good to have the more quantitative approach of rescue with both FCHo2 and Nedd4L in the biochemical assay.

__Reply: __Although the reviewer suggests a rescue experiment in the biochemical assay, the experiment is difficult because the transfection efficiency is low (about 50%). On the other hand, we agree with the reviewer that a quantitative approach is required in the rescue experiment (Fig. 1C). Therefore, we plan to quantify the rescue experiment for FCHO2 in the immunofluorescence assay. The reviewer also suggests a rescue experiment for Nedd4L as well as FCHO2. However, since the involvement of Nedd4L in ENaC endocytosis is well established, we do not think that the rescue experiment for Nedd4L is further required.

1. In figure 2 there is nice co-localisation between clathrin/FCHo2 and ENaC but not with Nedd4L. It would be good to have some quantitation of the co-localisation. But also one should use a Nedd4L mutant or a mutant of ENaC and so be able to visualise co-localisation between receptor and ub-ligase. I find it strange that there is no (or much less) Nedd4L-GFP visible in the cells overexpressing ENaC... Is there an explanation? Does overexpression of ENaC lead to more auto-ubiquitination of Nedd4L. Also the Nedd4L-GFP signal in other cells is punctate, while in the next figure Myc-Nedd4L is not.

__Reply: __According to the reviewer’s comment, we will perform quantitative colocalization analysis in Fig. 2.

We have found that a catalytically inactive Nedd4L mutant, C922A, co-localizes with cell-surface αENaC and FCHO2 in αβγENaC-HeLa cells. According to the reviewer’s comment, these data will be added in the revised manuscript.

In Fig. 2C, Nedd4L was transiently transfected in cells stably expressing ENaC. In Nedd4L-transfected cells, overexpression of Nedd4L stimulated ENaC internalization, resulting in the disappearance of ENaC at the cell surface. On the other hand, in non-transfected cells, cell-surface ENaC was detected. Thus, Nedd4L-negative cells are non-transfected cells (cell-surface ENaC positive cells). This explanation will be added in the revised manuscript.

The staining pattern of Nedd4L depends on what section of the cell a confocal microscope was focused on. Nedd4L-GFP signals were punctate at the bottom section of the cell in Fig. 2, whereas Myc-Nedd4L was diffusely distributed at the upper section (cytoplasm) of the cell (Fig. 3). Thus, Nedd4L shows distribution throughout the cytoplasm and punctate staining at the bottom (cell surface). The staining pattern of Nedd4L is also affected by the expression amount of Nedd4L in cells. When Nedd4L was highly expressed in COS7 and HEK293 cells in Fig. 3, the punctate staining was hardly detected. This localization pattern of Nedd4L will be clearly described in the revised manuscript.

1. In figure 3 it appears to me that there is co-localization between ENaC and amphiphysin. Is this not a positive piece of information? I am not sure that FBP17 is a good F-BAR domain to use given its oligomerization may well prevent membrane association of Nedd4L. Minor comment: I don't see tubules for amphiphysin in panel B.

__Reply: __The reviewer states that there is co-localization between Nedd4L and amphiphysin1 (Fig. 3A). However, Nedd4L was not recruited to membrane tubules generated by amphiphysin1. We will clearly show that there is no colocalization between Nedd4L and amphiphysin1.

The reviewer states that FBP17 may not be a good F-BAR domain to use because its oligomerization may well prevent membrane association of Nedd4L. However, we have shown that FCHO2 as well as FBP17 forms oligomer (Uezu et al. Genes Cells, 16, 868-878, 2011). Furthermore, we have found that FCHO2 inhibits the membrane binding and catalytic activity of Nedd4L when the PS percentage in liposomes is elevated (unpublished data and Fig. 9C). Thus, since FBP17 and FCHO2 probably have similar properties, we presume that FBP17 is a good F-BAR domain to use.

As the reviewer pointed out, membrane tubules generated by amphiphysin1 were hardly detected in HEK293 cells (Fig. 3B). It showed punctate staining, but did not co-localized with Nedd4L. This description will be added in the revised manuscript.

1. Figure 5: The affinity of Nedd4 C2 domain for calcium is quite high given we normally assume a cytosolic concentration of 100nM (approximate). The authors have rightly buffered the calcium with EGTA. Normally we would check that the buffering is sufficient by varying the protein concentration and making sure the affinity is still the same, so can I suggest the authors use 3 or 4 times the amount of C2 domain and make sure the curve does not change (provided liposomes are not limiting). Minor comment: How many experiments and what are error bars (SD?).

__Reply: __According to the reviewer’s comment, we will check that the buffering is sufficient by varying the protein concentration (Fig. 5). We will also add a description of statistics to the legend to Fig. 5.

1. Figure 6: Controls have been performed to ensure that liposomes are pelleted, according to methods. In Figure 6B can the authors show that there is the same amount of liposomes in each sample by showing more of the coomassie gel so that the reader can see the Neutravidin band is the same in each sample. Also I believe a student t-test should not be used in this experiment (but perhaps an Anova test), and in panel D there does not appear to be a description of statistics.

__Reply: __To ensure that the same amounts of liposomes were pelleted, the reviewer suggests that we show more of the Coomassie gel to present the neutravidin bands in Fig. 6B. However, as the molecular weight of neutravidin is about 15 kDa, neutravidin run out of the gel (7% SDS-PAGE gel) where Nedd4L (As the reviewer pointed out, we will use an Anova test in Fig. 6B. We will also add a description of statistics in Fig. 6D.

1. Figure 11: In panel B I note that the FCHo2 BAR domain on small liposomes appears to inhibit Ubiquitination. Is this consistent with the BAR domain not preventing Nedd4L binding?

__Reply: __The FCHO2 BAR domain enhances the liposome binding and catalytic activity of Nedd4L when the strength of interaction of Nedd4L with liposomes (20% PS) is weak. In contrast, we have also found that the FCHO2 BAR domain inhibits the membrane binding and catalytic activity of Nedd4L when the interaction of Nedd4L with liposomes is increased by elevating the PS percentage in liposomes (unpublished data and Fig. 9C). The reason for the different effects of FCHO2 on Nedd4L is considered as follows: When liposomes (20% PS) are used (the interaction of Nedd4L with PS in liposomes is weak), Nedd4L binds to liposomes mainly through ENaC (Fig. 8F). The liposome binding is hardly mediated by PS. Addition of the FCHO2 BAR domain increases the strength of interaction Nedd4L with PS by generating membrane curvature. Consequently, the FCHO2 BAR domain newly induces the PS-mediated liposome binding of Nedd4L, resulting in the enhancement of liposome binding and catalytic activity of Nedd4L. On the other hand, when the interaction of Nedd4L with PS in liposomes is increased by elevating the PS percentage in liposomes (50% PS), the liposome binding of Nedd4L is mainly mediated by PS. Addition of the FCHO2 BAR domain inhibits the PS-mediated liposome binding of Nedd4L. Since both FCHO2 and Nedd4L are PS-binding proteins, they compete with each other to bind to PS in liposomes. Therefore, the results in Fig. 11B are consistent, because the interaction of Nedd4L with PS is increased by 0.05 µm pore-size liposomes. This explanation will be added in the revised manuscript.

__Reviewer #2 __

The authors have reported the involvement of the BAR domain-containing protein FCHO2 in the Nedd4L-mediated endocytosis of ENaC. They propose a model in which the membrane curvature induced by the BAR domain-FCHO2 relieves the auto-inhibition of E3 ligase causing its activation and recruitment. The paper describes a series of in vitro reconstituted experiments that are interesting but not fully connected with the mechanism of ENaC endocytosis. Additional experiments are needed to fully support the authors' conclusions.

Major comments:

1. Although the data reported by the authors regarding FCHO2 and Nedd4L involvement in ENaC endocytosis are convincing, it is suggested that the authors perform the same ENaC endocytosis assay presented in Fig.1B under conditions of FBP17 and amphiphysin1 siRNA to formally prove the selective involvement of FCHO2 in the process among other BAR-containing proteins.

__Reply: __The reviewer suggests the same ENaC endocytosis assay presented in Fig. 1B under conditions of FBP17 and amphiphysin1 siRNA to prove the selective involvement of FCHO2 in ENaC endocytosis. There seems to be a misunderstanding. Similar to FCHO2, FBP17 and amphiphysin are well known to be involved in clathrin-mediated endocytosis. As ENaC is internalized through clathrin-mediated endocytosis, FBP17 and amphiphysin siRNA presumably inhibit ENaC endocytosis. We cannot understand the significance of FBP17 and amphiphysin1 siRNA in the ENaC endocytosis assay.

1. According to the previous point, it will be interesting to see not only a snapshot image of the internalisation assay performed by immunofluorescence (Fig.1C) but a more quantitative analysis of the different time points (as in Fig.1B) in condition of FCHO2 siRNA and eventually FBP17 and amphiphysin1 siRNA.

__Reply: __According to the reviewer’s comment, we will perform a quantitative analysis in Fig. 1C. The reviewer also suggests the immunofluorescence assay at the different time point in Fig. 1C. However, we show the time course of ENaC internalization in Fig. 1B. We do not think that the time course in the immunofluorescence assay is further required. As for FBP17 and amphiphysin siRNA, our response is the same as that to the comment 1 of this reviewer.

1. In Fig.2B, overexpression of the catalytically inactive version of Nedd4L (Nedd4L C922A) would help to see Nedd4L-ENaC co-localization.

__Reply: __This comment is the same as the comment 4 of the reviewer#1.

1. In Fig.4D, the authors need to analyse ENaC ubiquitination in the same experimental setting as Fig. 4A instead of transfecting cells with increasing amounts of Nedd4L in the presence or absence of FCHO2 BAR. It is also recommended to include Nedd4L C922A as an additional control.

__Reply: __The reviewer requests us to analyse ENaC ubiquitination in the same setting as Fig. 4A. However, an in vivo autoubiquitination assay is widely used to determine the catalytic activity of E3 Ub ligase, because the E3 activity is typically reflected in their autoubiquitination. Therefore, the autoubiquitination assay is sufficient to show that Nedd4L is specifically activated by membrane tubules generated by FCHO2 in cells. Furthermore, we have found it very difficult to compare ENaC ubiquitination among many GFP-BAR proteins (GFP alone, GFP-FCHO2, GFP-FBP17, amphiphysin1-GFP, GFP-FCHO2 mutant) in the same experimental setting as Fig. 4A. In Fig. 4A, three types of cDNAs (HA-Ub, Myc-Nedd4L, and GFP-BAR protein) were transfected in cells. The expression amounts of Myc-Nedd4L were similar among the GFP-BAR proteins. On the other hand, in Fig. 4D, four types of cDNA (HA-Ub, Myc-Nedd4L, GFP-BAR protein, and FLAG-αENaC) were transfected in cells. Under these conditions, it is very difficult to adjust the expression amounts of Nedd4L and αENaC among many GFP-BAR proteins. Even when comparing two GFP-BAR proteins (GFP alone and GFP-FCHO2), it was necessary to assess the expression amounts of Nedd4L by transfection with various cDNA amounts of Nedd4L (Fig. 4D). Moreover, as shown in Fig. 4D, enhancement of ENaC ubiquitination by FCHO2 is decreased at higher expression of Nedd4L (1.0 and 1.5 μg DNA), although the reason is unknown. Therefore, we are not sure that we will able to accurately analyse ENaC ubiquitination in the same setting as Fig. 4A instead of transfecting cells with increasing amounts of Nedd4L.

According to the reviewer’s comment, we will examine the effect of Nedd4L C922A on ENaC ubiquitination.

1. While discussing the role of hydrophobic residues in Nedd4L C2 domain,the authors never mentioned the publication by Escobedo et al., Structure 2014 (DOI:10.1016/j.str.2014.08.016), which highlighted how I37 and L38 are directly involved in Ca2+ binding. This aspect should be discussed since the authors show the importance of Ca2+ for PS binding in the sedimentation assay.

__Reply: __According to the reviewer’s comment, we will cite the reference (Escobedo et al.) and discuss the aspect (I37 and L38 are directly involved in Ca2+ binding).

1. As stated by the authors those two residues I37 and L38 are also involved in E3 enzyme activation by relieving C2-HECT interaction. It is important to further demonstrate the effect of these mutations on ENaC substrate.

__Reply: __To prove that the I37 and F38 residues are involved in E3 enzyme activation by relieving C2-HECT interaction, the reviewer requests us to further demonstrate the effect of Nedd4L I37A+F38A on ENaC ubiquitination. However, these two residues are critical noy only for Nedd4L activation but also for membrane binding and curvature sensing of Nedd4L. We also show that membrane binding of Nedd4L is critical for ENaC ubiquitination. Actually, we have found that Nedd4L I37A+F38A mutant, which loses membrane binding, shows little ENaC ubiquitination (unpublished data), whereas it enhances autoubiquitination (Fig. 4C). Thus, the effect of the I37A+F38A mutant on ENaC ubiquitination is not appropriate to prove that the two residues are involved in E3 enzyme activation.

1. There are some concerns regarding the in vitro ubiquitination assay performed in Fig.8 and following figures. The Nedd4L proteins used during the assay has been produced as His tagged at the C-terminus, it was reported (Maspero et al, Nat Struct Mol Biol 2013 DOI: 10.1038/nsmb.2566), at least for the isolated HECT domain, that modification of the C-terminal residue of the protein affects its activity. It would be important to judge the activity of the purified proteins used in the assay. Moreover, as additional control it is suggested the introduction of a mSA-ENaC PY mutant protein. The authors claimed the importance of membrane localized PY motif for recruitment and activation of Nedd4L, it would be informative to perform the experiment in presence of PY mutated ENaC.

__Reply: __The reviewer states that there are some concerns regarding His-tagged Nedd4L proteins. We have prepared Nedd4L that has no tag at its N- or C-terminus. N-terminal GST-tagged, C-terminal untagged Nedd4L was expressed in E. coli and purified by Glutathione-Sepharose column chromatography. The GST tag was cleaved off and Nedd4L was further purified by Mono Q anion-exchange column chromatography. Using this purified sample, we have examined the catalytic activity of untagged Nedd4L. We have found that concerning Ca2+-dependency, PS-dependency, and curvature-sensing, the properties of untagged Nedd4L are similar to those of C-terminal His-tagged Nedd4L (unpublished data).

According to the reviewer’s comment, we will perform the experiment in the presence of PY-mutated ENaC.

1. It is not clear why increasing the concentration of PS (from 20% to 50%) the presence of BAR domain doesn't allow ENaC ubiquitination (Fig.9C), is Nedd4L not recruited to the pellet? It would be interesting to see the sedimentation experiment of Fig.9A done in presence of 50% PS.

__Reply: __This comment is essentially the same as the comment 8 of the reviewer#1. We have found that FCHO2 BAR domain inhibits the membrane binding of Nedd4L when the PS percentage in liposomes is elevated (~50%) (unpublished data). According to the reviewer’s comment, these data will be added in the revised manuscript.

1. This reviewer is not an expert of lipids biology, thus the explanations related to the effect of FCHO2 BAR in presence of PI(4,5)P2 (Fig. 10) or 0.05 pore-size liposomes (Fig.11) were not clear. Does FCHO2 BAR have a different effect in inducing membrane tubulation in these two conditions? Is this parameter measurable by tubulation assay?

__Reply: __According to the reviewer’s comment, we will write more clearly the explanation related to the effect of FCHO2 BAR domain in the presence of PI(4,5)P2 or 0.05 μm pore-size liposomes.

Minor Comments

1. It would be appreciated if a nuclei staining panel is included in all immunofluorescence images, as it would help to identify the number of cells in the field of view (e.g., Fig. 1C, Fig. 2B).

__Reply: __According to the reviewer’s comment, we will show immunofluorescence images to identify the number of cells in Fig. 1C and Fig. 2B.

1. It would be recommended to include colocalization analysis, such as Pearson's correlation coefficient or Manders coefficient in immunofluorescence images.

__Reply: __According to the reviewer comment, we plan to perform quantitative colocalization analysis in Fig. 2.

1. It is not clear how the quantitation of mSA-ENaC ubiquitination in Fig.8D, 8C, and 9B was performed. Did the authors normalise the detected Ub signal over the amount of unmodified mSA-ENaC?

__Reply: __We did not normalize the detected Ub signals over the amount of unmodified mSA-ENaC, because the same amount of mSA-ENaC was added in each assay. The chemiluminescence intensity of Ub signals was quantified by scanning using ImageJ. According to the reviewer’ comment, we will clearly describe how the quantification of mSA-ENaC ubiquitination was performed.

__Reviewer #3 __

--- Summary ---

The manuscript by Sakamoto et al. describes how the ubiquitin ligase Nedd4L is activated by membrane curvature generated by the endocytic protein FCHO2. For their experiments, the authors use the epithelial sodium channel (ENaC) as a model Nedd4L target and CME cargo. The authors start their manuscript by showing in cells the importance of FCHo2 and Nedd4L in ENaC internalization. Using a combination of experiments in cells and biochemistry, the authors show that Nedd4L binds preferentially to membranes with the same curvature generated by FCHO2. Next, the authors show that a combination of membrane composition (PS), calcium concentration, PY domain presence and membrane curvature all act in concert to recruit Nedd4L to membranes and fully release its ubiquitination activity. Crucially, the authors show that role of FCHO2 in Nedd4L recruitment is not direct, with FCHO2 simply generating an optimal membrane curvature for Nedd4L binding. Taken together, the authors suggest a mechanism by which the curvature of early clathrin coated pits, generated by FCHO1/2 define an optimal environment for the recruitment and activation of the ubiquitin ligase Nedd4L.

The manuscript convincingly shows the membrane curvature-dependent mechanism of Nedd4L activation. The biochemistry experiments in the manuscript are well designed and the results are of clear. The quality of these experiments is very high. The experiments in cells are, however, not of the same level of quality.

--- Major comments ---

1) The results do not show convincingly that Nedd4L is recruited to CCPs. There is plenty of indirect evidence, but to support the model shown in the last figure, authors need to show more than the staining in figure 2C. Live-cell imaging showing the post-FCHo2 recruitment of Nedd4L would be required. I understand that the recruitment would possibly occur in a fraction of events and may be difficult to catch. The cmeAnalysis script from the danuser lab(https://doi.org/10.1016/j.devcel.2013.06.019 can facilitate the identification of these events.

__Reply: __According to the reviewer comment, we plan to examine by live-cell TIRF microscopy that Nedd4L is recruited to CCPs.

2) What happens to ENaC in Nedd4L and FCHO2 knockdown cells? One would expect accumulation of the receptor on the surface.

__Reply: __We have found that upon Nedd4L or FCHO2 knockdown, αENaC accumulates at the cell surface in αβγENaC-HeLa cells. According to the reviewer’s comment, we will show these data in the revised manuscript.

*3) In the experiments in figure 1, it would be important to use a standard CME cargo as an internal control (transferrin). This will serve as a functional confirmation of FCHO2 knockdown and help the reader to put the Need4L knockdown experiments into the context of CME. *

__Reply: __According to the reviewer’s comment, we will use a standard CME cargo as an internal control (transferrin).

*4) Quantification for the rescue experiment is required (figure 1C). if not possible, at least a picture where the reader can see transfected and non-transfected cells side-by-side is necessary. *

Reply: This comment is the same as those of the reviewer#1 (comment 3) and reviewer#2 (comment 2). According to the reviewer’s comment, we plan to quantify the rescue experiment (Fig. 1C).

*--- Minor comments --- *

*1) The experiments in figure 3 must be presented in order as they are in the text. For example, figure 3E is cited in the text into the context of figure 7. It is very confusing. *

__Reply: __According to the reviewer’ s comment, we will present the experiments in Fig. 3 in order they are in the text.

*2) A better explanation of the assay in 1C would facilitate its understanding for the non-specialist reader. The reader needs to read the methods section to understand how it was done. *

__Reply: __According to the reviewer’ comment, we will write a better explanation of the assay in the Fig. 1C legend to enable the readers to understand how it was done.

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript by Sakamoto et al. describes how the ubiquitin ligase Nedd4L is activated by membrane curvature generated by the endocytic protein FCHO2. For their experiments, the authors use the epithelial sodium channel (ENaC) as a model Nedd4L target and CME cargo. The authors start their manuscript by showing in cells the importance of FCHo2 and Nedd4L in ENaC internalization. Using a combination of experiments in cells and biochemistry, the authors show that Nedd4L binds preferentially to membranes with the same curvature generated by FCHO2. Next, the authors show that a combination of membrane composition (PS), calcium concentration, PY domain presence and membrane curvature all act in concert to recruit Nedd4L to membranes and fully release its ubiquitination activity. Crucially, the authors show that role of FCHO2 in Nedd4L recruitment is not direct, with FCHO2 simply generating an optimal membrane curvature for Nedd4L binding. Taken together, the authors suggest a mechanism by which the curvature of early clathrin coated pits, generated by FCHO1/2 define an optimal environment for the recruitment and activation of the ubiquitin ligase Nedd4L.

The manuscript convincingly shows the membrane curvature-dependent mechanism of Nedd4L activation. The biochemistry experiments in the manuscript are well designed and the results are of clear. The quality of these experiments is very high. The experiments in cells are, however, not of the same level of quality.

Major comments

1. The results do not show convincingly that Nedd4L is recruited to CCPs. There is plenty of indirect evidence, but to support the model shown in the last figure, authors need to show more than the staining in figure 2C. Live-cell imaging showing the post-FCHo2 recruitment of Nedd4L would be required. I understand that the recruitment would possibly occur in a fraction of events and may be difficult to catch. The cmeAnalysis script from the danuser lab(https://doi.org/10.1016/j.devcel.2013.06.019 can facilitate the identification of these events.
2. What happens to ENaC in Nedd4L and FCHO2 knockdown cells? One would expect accumulation of the receptor on the surface.
3. In the experiments in figure 1, it would be important to use a standard CME cargo as an internal control (transferrin). This will serve as a functional confirmation of FCHO2 knockdown and help the reader to put the Need4L knockdown experiments into the context of CME.
4. Quantification for the rescue experiment is required (figure 1C). if not possible, at least a picture where the reader can see transfected and non-transfected cells side-by-side is necessary.

Minor comments

1. The experiments in figure 3 must be presented in order as they are in the text. For example, figure 3E is cited in the text into the context of figure 7. It is very confusing.
2. A better explanation of the assay in 1C would facilitate its understanding for the non-specialist reader. The reader needs to read the methods section to understand how it was done.

To end on a positive note - I applaud the authors for experiment 6A. It is critical to show that liposome extrusion beyond 0.2um does not guarantee liposomes at that size.

Referee cross-commenting

I also agree with the other comments. Nothing to add.

Significance

The manuscript convincingly describes a novel mechanism for the activation of the ubiquitin ligase Nedd4L. From a biochemical point of view, the manuscript is solid. However, to be able to put this mechanism in the context of a CME event, the authors need stronger evidence in cells. To be clear, I think that the results presented do suggest a CME link. However, one could argue, for example, that the results could also be explained by ubiquitination of ENaC post CME, in an endosomal compartment with similar curvature.

Expertise of the reviewer: F-BAR proteins, endocytosis, cell biology and biochemistry.

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Referee #2

Evidence, reproducibility and clarity

The authors have reported the involvement of the BAR domain-containing protein FCHO2 in the Nedd4L-mediated endocytosis of ENaC. They propose a model in which the membrane curvature induced by the BAR domain-FCHO2 relieves the auto-inhibition of E3 ligase causing its activation and recruitment. The paper describes a series of in vitro reconstituted experiments that are interesting but not fully connected with the mechanism of ENaC endocytosis. Additional experiments are needed to fully support the authors' conclusions.

Major comments:

1. Although the data reported by the authors regarding FCHO2 and Nedd4L involvement in ENaC endocytosis are convincing, it is suggested that the authors perform the same ENaC endocytosis assay presented in Fig.1B under conditions of FBP17 and amphiphysin1 siRNA to formally prove the selective involvement of FCHO2 in the process among other BAR-containing proteins.
2. According to the previous point, it will be interesting to see not only a snapshot image of the internalisation assay performed by immunofluorescence (Fig.1C) but a more quantitative analysis of the different time points (as in Fig.1B) in condition of FCHO2 siRNA and eventually FBP17 and amphiphysin1 siRNA.
3. In Fig.2B, overexpression of the catalytically inactive version of Nedd4L (Nedd4L C922A) would help to see Nedd4L-ENaC co-localization.
4. In Fig.4D, the authors need to analyse ENaC ubiquitination in the same experimental setting as Fig. 4A instead of transfecting cells with increasing amounts of Nedd4L in the presence or absence of FCHO2 BAR. It is also recommended to include Nedd4L C922A as an additional control.
5. While discussing the role of hydrophobic residues in Nedd4L C2 domain, the authors never mentioned the publication by Escobedo et al., Structure 2014 (DOI:10.1016/j.str.2014.08.016), which highlighted how I37 and L38 are directly involved in Ca2+ binding. This aspect should be discussed since the authors show the importance of Ca2+ for PS binding in the sedimentation assay.
6. As stated by the authors those two residues I37 and L38 are also involved in E3 enzyme activation by relieving C2-HECT interaction. It is important to further demonstrate the effect of these mutations on ENaC substrate.
7. There are some concerns regarding the in vitro ubiquitination assay performed in Fig.8 and following figures. The Nedd4L proteins used during the assay has been produced as His tagged at the C-terminus, it was reported (Maspero et al, Nat Struct Mol Biol 2013 DOI: 10.1038/nsmb.2566), at least for the isolated HECT domain, that modification of the C-terminal residue of the protein affects its activity. It would be important to judge the activity of the purified proteins used in the assay. Moreover, as additional control it is suggested the introduction of a mSA-ENaC PY mutant protein. The authors claimed the importance of membrane localized PY motif for recruitment and activation of Nedd4L, it would be informative to perform the experiment in presence of PY mutated ENaC.
8. It is not clear why increasing the concentration of PS (from 20% to 50%) the presence of BAR domain doesn't allow ENaC ubiquitination (Fig.9C), is Nedd4L not recruited to the pellet? It would be interesting to see the sedimentation experiment of Fig.9A done in presence of 50% PS.
9. This reviewer is not an expert of lipids biology, thus the explanations related to the effect of FCHO2 BAR in presence of PI(4,5)P2 (Fig. 10) or 0.05 pore-size liposomes (Fig.11) were not clear. Does FCHO2 BAR have a different effect in inducing membrane tubulation in these two conditions? Is this parameter measurable by tubulation assay?

Minor Comments

1. It would be appreciated if a nuclei staining panel is included in all immunofluorescence images, as it would help to identify the number of cells in the field of view (e.g., Fig. 1C, Fig. 2B).
2. It would be recommended to include colocalization analysis, such as Pearson's correlation coefficient or Manders coefficient in immunofluorescence images.
3. It is not clear how the quantitation of mSA-ENaC ubiquitination in Fig. 8D, 8C, and 9B was performed. Did the authors normalise the detected Ub signal over the amount of unmodified mSA-ENaC?

Referee cross-commenting

I agree with the comments of other two reviewers.

Significance

Unfortunately do to limited knowledge of the reviewer on the lipids biology field it is difficult to judge strengths and limitations of the last part of the manuscript.

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Referee #1

Evidence, reproducibility and clarity

I enjoyed reading the paper by Sakamoto and colleagues, where they show that Nedd4L ubiquitin ligase activity is stimulated by membranes and in particular positive membrane curvature. This paper is a conceptual advance that hopefully will be extended by many other groups where membranes topology participates in the activation of associated enzymes, giving rise to added complexity but also specificity and further compartmentmentalization. It is an importnat paper for all cell biologists to understand.

My comments are all relatively minor and I hope can improve the readability of the paper, but will not alter the overall conclusion as this is well backed up. In general I would like to see more/better statistics/quantitation and better figure legends. I found that often one had to read the paper to understand a figure where reading the figure legend should suffice.

This paper reminds me of a paper from Gilbert Di Paolo's lab on the activation of synaptojanin PIP2 hydrolysis by high membrane curvature. One would expect that there may be many such proteins whose activities will be dependent on their membrane environment. I find it conceptually rather likely that a protein which interacts with membranes via a C2 domain (which has membrane insertions and will thus likely be curvature sensitive) will likely show some positive curvature sensitivity. Can I suggest this paper is referenced and discussed in the light of the discussion statement "Thus, our findings provide a new concept of signal transduction in which a specific degree of membrane curvature serves as a signal for activation of an enzyme that regulates a number of substrates."

Where the paper could be improved (or I have not understood fully) In figure 1 there is a robust endocytosis of ENaC that is FCHo2 and Nedd4L sensitive. There is a rescue for FCHo2 in a fluorescence image (unquantified), so it would be good to have the more quantitative approach of rescue with both FCHo2 and Nedd4L in the biochemical assay.

In figure 2 there is nice co-localisation between clathrin/FCHo2 and ENaC but not with Nedd4L. It would be good to have some quantitation of the co-localisation. But also one should use a Nedd4L mutant or a mutant of ENaC and so be able to visualise co-localisation between receptor and ub-ligase. I find it strange that there is no (or much less) Nedd4L-GFP visible in the cells overexpressing ENaC... Is there an explanation? Does overexpression of ENaC lead to more auto-ubiquitination of Nedd4L. Also the Nedd4L-GFP signal in other cells is punctate, while in the next figure Myc-Nedd4L is not.

In figure 3 it appears to me that there is co-localization between ENaC and amphiphysin. Is this not a positive piece of information? I am not sure that FBP17 is a good F-BAR domain to use given its oligomerization may well prevent membrane association of Nedd4L. Minor comment: I don't see tubules for amphiphysin in panel B.

Figure 5: The affinity of Nedd4 C2 domain for calcium is quite high given we normally assume a cytosolic concentration of 100nM (approximate). The authors have rightly buffered the calcium with EGTA. Normally we would check that the buffering is sufficient by varying the protein concentration and making sure the affinity is still the same, so can I suggest the authors use 3 or 4 times the amount of C2 domain and make sure the curve does not change (provided liposomes are not limiting). Minor comment: How many experiments and what are error bars (SD?).

Figure 6: Controls have been performed to ensure that liposomes are pelleted, according to methods. In Figure 6B can the authors show that there is the same amount of liposomes in each sample by showing more of the coomassie gel so that the reader can see the Neutravidin band is the same in each sample. Also I believe a student t-test should not be used in this experiment (but perhaps an Anova test), and in panel D there does not appear to be a description of statistics.

Figure 11: In panel B I note that the FCHo2 BAR domain on small liposomes appears to inhibit Ubiquitination. Is this consistent with the BAR domain not preventing Nedd4L binding?

Significance

I enjoyed reading the paper by Sakamoto and colleagues, where they show that Nedd4L ubiquitin ligase activity is stimulated by membranes and in particular positive membrane curvature. This paper is a conceptual advance that hopefully will be extended by many other groups where membranes topology participates in the activation of associated enzymes, giving rise to added complexity but also specificity and further compartmentmentalization. It is an importnat paper for all cell biologists to understand.

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Reply to the reviewers

Reviewer #1:

Major comments:

1. • The relevance of these findings to human biology remains unclear. In Figures 1-4, the authors present data showing that AATBC is enriched in thermogenic fat, and they argue that it regulates thermogenesis and mitochondrial biology. However, in Figures 6-7, where the authors look at AATBC in different human cohorts, they actually find that it is enriched in visceral fat, which is thought of as being the least thermogenic fat depot. The authors do not explain this seeming paradox, and thus, the role of AATBC in fat remains uncertain. *

RESPONSE: We thank the reviewer for this comment and have clarified the discussion to address this point. It has been recently shown (PMID: 28529941) that the pattern of browning genes in human white adipose tissue depots is actually inverted to mice, making visceral adipose tissue in humans actually more thermogenic than subcutaneous. This aligns well with our findings of AATBC is predominantly expressed in thermogenic adipose tissue.

• In many of the experiments, insufficient controls are provided, or the data are not at all convincing. For example:*

(a) The first four figures rely on in vitro adipocyte models, but the authors do not present data to show these cells differentiate properly and equally. This is especially relevant for the gain and loss of function studies.

RESPONSE: We agree with the reviewer that equal differentiation is necessary for in vitro adipocyte models. Therefore, we added Oil-red-O stainings and the corresponding quantifications to Supp. Fig. 4 (see below) for the differentiation of hMADS in the absence of AATBC. We also want to emphasize, that the expression levels of PLIN1, a surrogate marker for differentiation was unchanged in our experiments, as already shown in the initial draft of the manuscript. On top of that, in all experiments presented in the original draft of the manuscript, AATBC gene expression was only altered in mature adipocytes.

(b) Some of the experiments in Figure 1 (K-L) seem to only show an N of 1.

RESPONSE: Figure 1 highlights a screening process to find new lncRNA regulated during thermogenesis. The forskolin sample was included to achieve an additional dimension in the filtering process. The displayed values in K&L demonstrate the validity of the sample. The validation of AATBC as a target was performed with statistical power in the work displayed in the following figures.

(c) The RNAscope data in Figure 2 is not at all convincing for nuclear localization

RESPONSE: We respectfully disagree. In our opinion, the RNAScope is convincing for nuclear localization of the lncRNA. However, we have repeated the experiments with different probes that strengthen our data (see figure for the reviewer)

(d) The ASO mediated knockdown of AATBC in Figure 3 only reduced expression slightly. A more complete knockdown or deletion may elicit a stronger phenotype.

RESPONSE: We thank the reviewer for the feedback. We have repeated the knockdown experiments but were not able to reduce the expression further, even after designing additional ASOs. However, already with current approach, the reduction in AATBC expression elicited a phenotype, highlighting the importance of AATBC in a dose-dependent manner.

(e) In Figure 4, OPA1 is shown as a single band in panel E and a doublet in panel N. Based on this, are the authors certain they are detecting OPA,1 or could this be a nonspecific band?

RESPONSE: We thank the reviewer for this comment. Protein extraction has been performed at different research institutes with slightly different buffers. Multiple bands (cleaved/uncleaved) have been described for OPA1 in the past, therefore we are certain that the correct protein has been detected.

*(f) The correlations in Figure 6 I-L and Figure 7 do not include any statistical analysis. *

REPONSE: For better readability, the statistical analysis is being mentioned in the figure legend. The reviewer might have overlooked this information.

• The gain of function studies in mice are problematic. The authors have performed a large amount of invasive studies in a short period of time. The animals will undoubtedly lose weight after each study and with insufficient time to recover, this could influence the subsequent studies.*

RESPONSE: These general concerns are valid, but all controls are in place and the animals gained weight during the experiments, as one would have been expected with animals of that age (see below).

*In addition, since the authors present data in Figures 1-4 arguing that AATBC overexpression is associated with increased thermogenesis, it is surprising that the authors never looked at this in Figure 5 (aside from measuring Ucp1 mRNA). It would be interesting to measure energy expenditure by indirect calorimetry and cold tolerance. *

RESPONSE: We agree with the reviewer on this point but are due to animal protocol limitations in conjunction with the viral approach are unable to perform these experiments.

• The authors do not provide any mechanistic insights into how AATBC may be acting.*

RESPONSE: Certainly, more mechanistic insight into the direct mode of action of AATBC would be interesting. To address this point, over the past year we performed multiple attempts to perform pulldown of AATBC using the ChIRP technology. However, we were unable to achieve a sufficient enrichment, which would have allowed us to give further information about direct interaction partners of AATBC. However, we believe that our data regarding mitochondrial dynamics, which we now also have confirmed in in vivo experiments, explain the connection of AATBC and thermogenicity. In future, we aim to work on this point further but for multiple reasons have decided to close this chapter here.

Minor comments:

• The introduction is rather long and would benefit from being condensed.*

RESPONSE: We have edited the text for better readability.

Reviewer #2:

Major Comments:

1. • The key conclusion that AATBC is a novel obesity-linked regulator of adipocyte plasticity is made relatively clear with the comparison between various stages of adipocytes and the loss and gain of function with AATBC. - Figure 1 H and J do not seem to be consistent with the data in Figure 1F in LINC00473 level-There is no difference in Control vs NE in the heatmap but in Figure1J, the difference seems to be quite obvious; Figure 1K does not seem to be consistent with AATBC level-The measurement in Control VS Fsk group showed no difference in AATBC in heatmap, but in Figure K, there seem to be a dramatic increase. Therefore, the claims that there is a difference in these two lncRNA expression in these cell groups needs further clarification. *

RESPONSE: To combine the different approaches to identify novel lncRNA into one heatmap the data need to be normalized over experiments. As the fold change of the expression of AATBC in BAT compared to WAT (on average ~100x) is higher than with forskolin (~4x), this will stand out in the heatmap and will to some extent overshadow the smaller fold changes. The same holds true for LINC00473, which is drastically induced with forskolin, which to some extent masks the higher expression in the other approaches. Therefore, we decided to show both the heatmap to represent the general approach and the “zoomed in” versions to show the consistent increases. We are confident this clarifies the issue.

• Figure 4H and I, the difference in the representative immunoblot seem to be minimal and inconsistent with the decrease shown in the bar graph. *

RESPONSE: We agree with the reviewer and have removed the claim from our manuscript.

• In Figure 5, after overexpressing human AATBC in murine adipose tissue , is it possible to look at the mitochondria changes that were seen before in cell lines? If there are similar changes in murine adipose tissue, then it would prove the changes in vitro hold up with the in vivo model. But if the mitochondria changes were not seen, then it would indicate the changes in leptin, triglyceride levels may due to other mechanisms. The length of the suggested experiment to look into the mitochondrial differences in mice may vary depending on whether there are preserved samples from previous experiments. If there are, then the time period would be couple of weeks for immunblot and analysis. If there are no samples preserved, then the estimated period for the suggested experiments may be around 1.5 to 2 months at least .*

RESPONSE: We thank the reviewer for the suggestion. We performed Western Blot analysis on the tissues from the in vivo study and have included them in Fig. 5, further strengthening the link between AATBC and mitochondrial dynamics (please see figure on the right).

• The data are convincing overall in that the replicates are clearly marked with dots in many figures. Some immune blot and expression level are inconsistent with other data showing the same results however. *

RESPONSE: We thank the reviewer and have removed the necessary quantifications.

• Figure 6 and 7 are provocative and significant, reporting strong associations of AATBC with well-known markers of metabolism in adipocytes. The sex difference for adiponectin and AATBC expression is particularly intriguing. Further discussion of this point would be interesting. However, there is no information provided about the medication status of the obese subjects that were consented for samples used in the analysis. Specifically, many of the obese subjects (mean BMI 45 or more with a range going up to 97.3) would be expected also to have metabolic diagnoses and to be treated with numerous medications, including Metformin, GLP1 agonists, Orlistat, Liraglutide, Bupropion/Naltrexone and combinations. It is unreasonable to ignore possible effects of major medications on AATBC expression. Please comment on the strengths and weaknesses of the analysis that ignores medications, or if some annotations of clinical data are available, perhaps to explain outliers in the plots, please discuss. *

RESPONSE: We thank the reviewer for this suggestion. Unfortunately, we are unable to exclude additional diagnoses and medication of our patients due to the points the reviewer stated. However, given the large size of the cohorts we are confident that such effects are being compensated for. We have added a part on weaknesses of the study in the discussion.

Minor Comments:

• The labeling of figure 2 A-K is not clear because the use of the same color of bars is easily misunderstood as the same source of cells, but it is in fact not. For example, the grey color that appeared in 2B and 2C are not the same source but can be misunderstood. *

RESPONSE: The coloring of Fig.2A&G has been changed.

• Figure 3 ASO-AATBC has two repeats #1 and #2, and over-expression of AATBC has one, even though there are enough repeats. It would be less confusing to present all of the repeats in ASO_AATBC together in one bar.*

RESPONSE: The two different ASO target different areas of AATBC. In line with general guidelines for ASO use, those are not pooled but used separately, which is why the results are also split up. As the overexpression is additional genomic information of AATBC, it is impossible to use different variants in this case, therefore only one bar for overexpression is shown.

• The experimental outline can be a bit more detailed and explain some of the words like Thermo versus Browning.*

RESPONSE: The manuscript has been revised regarding this point.

• Some of the panels in Figure 7 could be put into supplementary if space is at a premium, and present the representative graph would be enough*

RESPONSE: We think that all our data of Fig. 7 warrants enough attention to be considered in a main figure, but if space is sparse, we are very happy to oblige. We would kindly ask the editors for input on this matter.

Reviewer #3:

1. • Throughout the study, the data provided are mainly correlative and in some cases not robust. In Fig. 2, AATBC expression is described to be elevated in the so-called "thermogenic condition", which contained prolonged PPARg agonist treatment (rosiglitazone) known to promote adipogenesis. Consistent with this notion, adipogenic markers, such as PLIN1 and FABP4, are higher in "thermogenic adipocytes" (Suppl Fig. 2). As such, the result may only suggest that AATBC has higher expression in mature adipocytes vs pre-adipocytes. *

RESPONSE: We thank the reviewer for the suggestion. We have added Oil-Red-O-Stainings to Suppl. Fig. 2 to show unchanged lipid content upon modulation of AATBC gene expression, which can be seen as a surrogate for differentiation. Concerning the use of rosiglitazone as a browning agent, we want to emphasize that rosiglitazone was used during the entirety of differentiation until day 9, where it was removed in the “non-thermogenic” group. At this point we already observe fully differentiated adipocytes. This is an established protocol. Furthermore, the data is in line with using norepinephrine or forskolin as a short-term inducer of browning, making it very likely that the effect seen is due to the “more thermogenic” character of the adipocytes.

• Along the same vein, whether and how AATBC affects adipogenesis is unclear. Suppl Fig. 3H and 3L (misplaced as Suppl Fig. 4) show the adipocyte differentiation marker FABP4 is down-regulated by both ASO- and AV-AATBC. Since mitochondrial respiration (and other parameters including UCP1 expression) is tightly linked to adipogenic efficiency, the authors need to address whether these manipulations affect adipocyte differentiation. *

RESPONSE: We agree with the reviewer that differences in differentiation capacity would falsify our data on mitochondrial dynamics. We have added Oil-Red-O-Staining to Suppl. Fig. 2 to show that no significant difference in lipid content exists during modulation of AATBC gene expression, which can be seen as a surrogate for differentiation. Furthermore, in all experiments presented in the manuscript, the modulation of AATBC occurs in already fully differentiated adipocytes. Accordingly, we are confident that AATBC does not influence differentiation but mainly acts through the modulation of mitochondrial dynamics.

• The data in Fig. 4 supporting a role for AATBC in regulating mitochondrial dynamics are superficial and not robust. Fig. 4A/4J do not have high enough resolution to provide accurate assessment of the mitochondrial network.*

RESPONSE: We respectfully disagree with the reviewer on this point. State of the art methods and algorithms were used to image and analyze the mitochondrial network. Furthermore, we have used multiple established markers of mitochondrial dynamics in western blot analysis to further strengthen our assessments of the immunofluorescence. In summary, we feel like have given enough evidence for an accurate assessment of the mitochondrial network.

• The level of loading control TUBB is clearly lower in siAATBC in Fig. 4H. In addition, OPA1 should have multiple isoforms and Fig. 4E/4N show inconsistent patterns. As such, mitochondrial dynamics is not likely an underlying mechanism. *

RESPONSE: We agree with the reviewer on the assessment of the expression of complex 5 and have removed this claim from the manuscript. Regarding the expression of OPA1, protein extraction has been performed at different research institutes with slightly different buffers. Multiple bands (cleaved/uncleaved) have been described for OPA1 in the past, therefore we are certain that the correct protein has been detected.

• Notably, RNAseq data in Suppl Fig. 4 (misplaced as Suppl Fig. 3) seem to indicate that AATBC over-expression promotes TG synthesis, while AATBC knockdown modulates cell death. The authors should consider exploring the leads from RNAseq analysis?*

RESPONSE: We thank the reviewer for the feedback. The small number of altered genes in the RNASeq make us believe in a rather post-transcriptional role of AATBC. We investigated cell death and oxidative stress response as GO terms were highlighted in the analysis, but we were unable to detect any differences in the absence of AATBC, pointing to a minimal effect on transcriptional level (See figure below for the reviewers).

• In Fig. 5, the AV-AATBC transduction in WAT/BAT is localized, transient and not homogeneous. Not surprisingly, this manipulation does not produce any robust effects. The difference in circulating leptin/leptin expression appears to be driven by 4-5 mice in the control group (Fig. 5H/5N). The correlation data in Fig. 6 and Fig. 7, although relevant, do not provide additional mechanistic insights. Unfortunately, the efforts in Fig. 5-7 fail to lead to information related to the biological function of adipose AATBC.*

RESPONSE: We agree with the reviewer on the limitations of the AV model, but we have performed these experiments with the highest technical standard. As the reviewer states, the overexpression, especially in WAT, has different magnitudes depending on the individual mouse, but the overexpression is present and consistently high in every animal. We would expect even bigger alterations in a genetic model, which, however, is beyond the scope of this first manuscript on AATBC in adipocytes. We are disappointed that the reviewer does not value the human data presented, as it very strongly hints to a relevant function of our human lncRNA in vivo by robust correlations with established biomarkers mirroring the effects seen in vitro and in the mouse model. A limitation of human studies is in virtually every case that it is based on correlations, as manipulation of gene expression, which would be necessary to delineate a biological process as requested by the reviewer, is not possible in humans. We do not concur on dismissing our human data on that behalf.

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Referee #3

Evidence, reproducibility and clarity

In the current work, the authors have characterized a human IncRNA AATBC whose expression is up-regulated in conditions favoring a "thermogenic phenotype" of fat cells. Results derived from transient knockdown/over-expression approaches indicate that AATBC may play a role in modulating mitochondrial functions. In addition, gene expression analyses have demonstrated that AATBC is positively correlated with thermogenic genes, such as UCP-1 and PGC-1a and negatively correlated with adipogenic genes, including PPARg, FABP4 and Leptin in humans.

The association between AATBC and BMI is of potential interest. However, restricted by the limitations of the employed approaches, the current study falls short of robust evidence supporting a role for AATBC in adipocyte plasticity and mitochondrial dynamics/respiration (and certainly a link between the two events). A substantial amount of work would be needed to tie up loose ends for a cohesive study with mechanistic insights.

Specific comments:

1. Throughout the study, the data provided are mainly correlative and in some cases not robust. In Fig. 2, AATBC expression is described to be elevated in the so-called "thermogenic condition", which contained prolonged PPARg agonist treatment (rosiglitazone) known to promote adipogenesis. Consistent with this notion, adipogenic markers, such as PLIN1 and FABP4, are higher in "thermogenic adipocytes" (Suppl Fig. 2). As such, the result may only suggest that AATBC has higher expression in mature adipocytes vs pre-adipocytes.
2. Along the same vein, whether and how AATBC affects adipogenesis is unclear. Suppl Fig. 3H and 3L (misplaced as Suppl Fig. 4) show the adipocyte differentiation marker FABP4 is down-regulated by both ASO- and AV-AATBC. Since mitochondrial respiration (and other parameters including UCP1 expression) is tightly linked to adipogenic efficiency, the authors need to address whether these manipulations affect adipocyte differentiation.
3. The data in Fig. 4 supporting a role for AATBC in regulating mitochondrial dynamics are superficial and not robust. Fig. 4A/4J do not have high enough resolution to provide accurate assessment of the mitochondrial network. The level of loading control TUBB is clearly lower in siAATBC in Fig. 4H. In addition, OPA1 should have multiple isoforms and Fig. 4E/4N show inconsistent patterns. As such, mitochondrial dynamics is not likely an underlying mechanism. Notably, RNAseq data in Suppl Fig. 4 (misplaced as Suppl Fig. 3) seem to indicate that AATBC over-expression promotes TG synthesis, while AATBC knockdown modulates cell death. The authors should consider exploring the leads from RNAseq analysis.
4. In Fig. 5, the AV-AATBC transduction in WAT/BAT is localized, transient and not homogeneous. Not surprisingly, this manipulation does not produce any robust effects. The difference in circulating leptin/leptin expression appears to be driven by 4-5 mice in the control group (Fig. 5H/5N). The correlation data in Fig. 6 and Fig. 7, although relevant, do not provide additional mechanistic insights. Unfortunately, the efforts in Fig. 5-7 fail to lead to information related to the biological function of adipose AATBC.

Significance

Thermogenic adipocytes are thought to be a druggable target to combat obesity and related metabolic diseases. The current study aims to identify genes associated with thermogenic capacity in human adipocytes. To this end, the authors have characterized a human IncRNA AATBC whose expression is up-regulated by thermogenic stimulations in cultured adipocytes. Of potential interest is the association between adipose AATBC expression and BMI in human samples.

Reviewer's field of expertise: metabolic regulation, obesity and related metabolic diseases, molecular physiology.

Referee Cross-commenting

I think there is a good consensus about the strengths and weaknesses of the study. My comments were very similar to those of reviewer 1. My view is the authors did not provide sufficient evidence to support their claims. Some of the data are also not robust enough to reach meaningful conclusions.

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Referee #2

Evidence, reproducibility and clarity

This investigation deals with a significant problem: how to discover and understand the signals that regulate white and brown or beige adipogenesis, which is central to energy balance. New approaches to promote brown, thermogenic adipogenesis have been considered as potential metabolic therapies to combat the current epidemic of obesity and obesity-related complications. Interestingly, the authors have identified a long non-coding RNA that associates with the thermogenic phenotype, and then through functional studies offer strong evidence that this lncRNA (AATBC) has potential as a regulator of adipocyte plasticity. The investigation is rigorously conducted, novel and important. The report may be suitable for publication upon completion of the improvements suggested here.

Major Comments:

• The key conclusion that AATBC is a novel obesity-linked regulator of adipocyte plasticity is made relatively clear with the comparison between various stages of adipocytes and the loss and gain of function with AATBC.
• Figure 1 H and J do not seem to be consistent with the data in Figure 1F in LINC00473 level-There is no difference in Control vs NE in the heatmap but in Figure1J, the difference seems to be quite obvious; Figure 1K does not seem to be consistent with AATBC level-The measurement in Control VS Fsk group showed no difference in AATBC in heatmap, but in Figure K, there seem to be a dramatic increase. Therefore, the claims that there is a difference in these two lncRNA expression in these cell groups needs further clarification.
• Figure 4H and I, the difference in the representative immunoblot seem to be minimal and inconsistent with the decrease shown in the bar graph.
• In Figure 5, after overexpressing human AATBC in murine adipose tissue, is it possible to look at the mitochondria changes that were seen before in cell lines? If there are similar changes in murine adipose tissue, then it would prove the changes in vitro hold up with the in vivo model. But if the mitochondria changes were not seen, then it would indicate the changes in leptin, triglyceride levels may due to other mechanisms.
• The length of the suggested experiment to look into the mitochondrial differences in mice may vary depending on whether there are preserved samples from previous experiments. If there are, then the time period would be couple of weeks for immunblot and analysis. If there are no samples preserved, then the estimated period for the suggested experiments may be around 1.5 to 2 months at least.
• The data are convincing overall in that the replicates are clearly marked with dots in many figures. Some immune blot and expression level are inconsistent with other data showing the same results however.
• Figure 6 and 7 are provocative and significant, reporting strong associations of AATBC with well-known markers of metabolism in adipocytes. The sex difference for adiponectin and AATBC expression is particularly intriguing. Further discussion of this point would be interesting.

However, there is no information provided about the medication status of the obese subjects that were consented for samples used in the analysis. Specifically, many of the obese subjects (mean BMI 45 or more with a range going up to 97.3) would be expected also to have metabolic diagnoses and to be treated with numerous medications, including Metformin, GLP1 agonists, Orlistat, Liraglutide, Bupropion/Naltrexone and combinations. It is unreasonable to ignore possible effects of major medications on AATBC expression. Please comment on the strengths and weaknesses of the analysis that ignores medications, or if some annotations of clinical data are available, perhaps to explain outliers in the plots, please discuss.

Minor Comments:

• The labeling of figure 2 A-K is not clear because the use of the same color of bars is easily misunderstood as the same source of cells but it is in fact not. For example, the grey color that appeared in 2B and 2C are not the same source but can be misunderstood.
• Figure 3 ASO-AATBC has two repeats #1 and #2, and over-expression of AATBC has one, even though there are enough repeats.
• It would be less confusing to present all of the repeats in ASO_AATBC together in one bar.
• The experimental outline can be a bit more detailed and explain some of the words like Thermo versus Browning.
• Some of the panels in Figure 7 could be put into supplementary if space is at a premium, and present the representative graph would be enough.

Significance

• Adipocyte plasticity and physiology has been linked to a lot of diseases such as diabetes, cardiovascular diseases and cancer. Therefore the conclusion coming from this paper reveals other aspects when looking at adipocytes in healthy or disease conditions-long noncoding RNA. lncRNA can be seen as a biomarker of an indicator of the physiology of adipose tissue, and may be able to account for changes that cannot be explained by cell genome analysis. There has been a surge of interest in RNA containing in exosomes, which serves as vesicles that travel between cells. Some studies have also shown that the content of exosomes arrives at the nucleolus of the recipient cell. The overlap of the location of exosomal RNA and lncRNA is a representative of a whole set of regulation of genes and expressions that was not noticed before.

• The audience of the paper may be interested in the outcome of the changes of mitochondria change in the context of disease such as obesity, diabetes, etc. For example, if there is a casual relationship between AATBC level and the status of obesity.

Referee Cross-commenting

Thank you, I concur.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Giroud et al. describes a role for the human-specific lncRNA AATBC in adipocyte plasticity. By overlaying datasets from tissues (white vs. brown fat) and cell lines (treated with norepinephrine or forskolin), the authors identified a limited number of lncRNAs demonstrating coordinate regulation. One of these lncRNAs is AATBC, which has not previously been studied in adipocytes. The authors show that AATBC is enriched in thermogenic adipose tissues/cells. They then perform gain and loss of function studies in cellular models and argue that AATBC is involved in thermogenesis and appears to be associated with the state of the mitochondrial network. The authors then explain that modulating AATBC has minimal effects on global transcription, and so they argue it mainly works via post-transcriptional mechanisms, though these are not defined. The authors then expressed AATBC in adipose tissue of mice and observed a decrease in plasma leptin levels and an increase in triglyceride levels, while other metabolic phenotypes were unchanged. Finally, the authors analyzed associations between adipose tissue AATBC and a variety of metabolic parameters in a few human cohorts. While the identification of a novel lncRNA involved in adipocyte biology and systemic metabolism would be of great interest, the data presented here does not convincingly support the conclusions made. Substantial additional experiments are needed to support the claims in this paper.

Major comments:

1. The relevance of these findings to human biology remains unclear. In Figures 1-4, the authors present data showing that AATBC is enriched in thermogenic fat, and they argue that it regulates thermogenesis and mitochondrial biology. However, in Figures 6-7, where the authors look at AATBC in different human cohorts, they actually find that it is enriched in visceral fat, which is thought of as being the least thermogenic fat depot. The authors do not explain this seeming paradox, and thus, the role of AATBC in fat remains uncertain.
2. In many of the experiments, insufficient controls are provided or the data are not at all convincing. For example: (a) The first four figures rely on in vitro adipocyte models, but the authors do not present data to show these cells differentiate properly and equally. This is especially relevant for the gain and loss of function studies. (b) Some of the experiments in Figure 1 (K-L) seem to only show an N of 1. (c) The RNAscope data in Figure 2 is not at all convincing for nuclear localization. (d) The ASO mediated knockdown of AATBC in Figure 3 only reduced expression slightly. A more complete knockdown or deletion may elicit a stronger phenotype. (e) In Figure 4, OPA1 is shown as a single band in panel E and a doublet in panel N. Based on this, are the authors certain they are detecting OPA1 or could this be a nonspecific band?( f) The correlations in Figure 6 I-L and Figure 7 do not include any statistical analysis.
3. The gain of function studies in mice are problematic. The authors have performed a large amount of invasive studies in a short period of time. The animals will undoubtedly lose weight after each study, and with insufficient time to recover, this could influence the subsequent studies. In addition, since the authors present data in Figures 1-4 arguing that AATBC overexpression is associated with increased thermogenesis, it is surprising that the authors never looked at this in Figure 5 (aside from measuring Ucp1 mRNA). It would be interesting to measure energy expenditure by indirect calorimetry and cold tolerance.
4. The authors do not provide any mechanistic insights into how AATBC may be acting. The manuscript contains some potentially interesting observations, but without some mechanistic insight, it is hard to understand how AATBC might regulate adipocyte plasticity.

Minor comments:

1. The introduction is rather long and would benefit from being condensed.

Significance

This manuscript may represent an interesting advance in terms of highlighting a new lncRNA with a role in adipocyte biology. These findings would be of broad interest to researchers interested in obesity and metabolism. I myself am in this field of research, so feel quite qualified to evaluate this manuscript. However, as noted above, major concerns would need to be addressed in order to justify the conclusions made here.

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Reply to the reviewers

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

*The current manuscript by Shiryaev et al describes their observation of the new function of zika NS2B-NS3 proteases. They have shown that NS2B-NS3 protease lacking the helicase domain binds to RNA and the interaction can be affected by protease inhibitors. Main two new findings are presented in the manuscript: super open conformation of the protease; RNA binding activity of the protease region. Although the manuscript is interesting, the design of the experiments is not convincing. *

Major issues:

1. • the claim of a super open confirmation is problematic. Using an artificial construct lacking the C-terminal portion of NS2B will of course generate the open conformation. This is a wrong definition unless you observe such a conformation in living cells.*

2. We understand the skepticism towards a less known super-open confutation of flavivirus NS2B-NS3pro complex. In addition to our own structure of ZIKV NS2B-NS3pro (PDB ID 7M1V), the crystal structure of another orthologous flavivirus Japanese encephalitis virus (JEV) NS2B-NS3pro (PDB ID 4R8T) was discovered in 2015 1. However, no functional analysis was provided for this crystal structure resulting in the lack of attention paid by the research community. We computed the overlay of the ZIKV NS2B-NS3 protease structures in the super-open conformation (PDB ID 7M1V, deposited by us in 2021) with the crystal structure of JEV protease (PDB ID 7M1V ) (Rebuttal Figure 1). We observed an almost identical organization of the critical NS3pro C-terminal loop between these two structures (RMSD 0.6A). Polypeptides with over 35% identity are very likely to have a similar fold2. Given over 50% identity(!) between flaviviral proteases across the family3,4, we posit that the super-open conformation demonstrated for JEV and ZIKV NS2B-NS3pro is a common feature of the Flaviviridae family. Further, NS2B peptide is always tightly associated with NS3pro via a three-strand beta-barrel (aa 49-58 of NS2B), which remains intact in all NS3Pro conformations. The C-terminal portion of NS2B progressively loses association with NS3pro, being mostly associated in the closed conformation, less so in the open, and even less in the super-open conformation. The G4SG4 linker between NS2B and NS3pro remains unstructured in all conformations. The native C-terminal portion of NS2B (TGKR) is equally unstructured when competed out of the protease active site by another substrate. It is unclear to us why “lacking the C-terminal portion of NS2B will of course generate the open conformation”.

3. It is odd that authors made homology model to generate open conformation structures. the authors did not cite the two papers of eZiPro (Phoo et al 2016 NC) and bZiPro (Zhang et al 2016, Science). these two structures show the closed conformation of protease in the absence and presence of a natural substrate.*

4. We agree with the reviewer that in both constructs eZiPro5 and bZiPro6 of ZIKV NS2B-NS3pro are likely to exist in the closed conformation as documented by the crystal structures. However, in both cases, the active center of ZIKV NS2B-NS3pro is occupied with a short peptide fragment, which is sufficient to induce the closed conformation of NS2B-NS3 protease. We superimposed eZiPro (PDB ID 5GJ4) with bZiPro (PDB ID 5GPI) to better demonstrate that the active center in both structures is occupied either by tetrapeptide TGKR (T127-G128-K129-R130 ) originating from the NS2B C-terminus (eZiPro) or by a tetrapeptide KKGE (K14-K15-G16-E17) originating from a neighboring NS3 molecule (bZiPro) (Rebuttal Figure 2). Indeed, Zheng et al., 2016 6 stated that: “the structure (bZiPro) does capture the protease in complex with a reverse peptide. The tetrapeptide K14K15G16E17 folds into a small hairpin loop to occupy the active site.” Further, Phoo et al., 2016 5 stated that “binding of the ‘TGKR’ peptide to the catalytic site stabilizes the protease (eZiPro)”. To the best of our knowledge, so far there are no crystal structures of flaviviral NS2B-NS3 proteases in the closed conformation without peptide/inhibitor in the active center. We take it as a hint that the closed conformation is always induced by a substrate present in the active center.

Finally, we would like to draw the attention of this reviewer to the fact that the 15N R2 NMR signal from NS2B residues 65-85 is missing in bZiPro alone but re-appears when AcKR is added. This is consistent with the idea that without AcKR, bZiPro exists in the open conformation where much of the C-terminal part of NS2B is dissociated from NS3Pro and remains unstructured, thus resulting in the lack of NMR signal.

• RNA binding is novel, but is it observed in cells? only one method was used for testing the interactions, not other biophysical methods are used.*

• Given a complex network of protein-RNA interactions and the fact that NS3pro and NS3hel are connected by a single polypeptide, separating dynamically bound 11kB RNA to NS3pro from that to NS3hel in a native cell is a major technical challenge beyond the scope of this work. We employed a fluorescent polarization assay to demonstrate ssDNA and ssDNA binding to ZIKV NS2B-NS3pro. Subsequently, we employed a proteolytic activity assay with labeled peptide mimicking natural substrate for protease to demonstrate that the presence of ssRNA and ssDNA can efficiently inhibit proteolytic activity. To the best of our knowledge, this is the first indication that ssRNA or ssDNA could block proteolytic activity for any serine proteases, let alone a viral protease. Therefore, we consider the proteolytic activity assay used in the current work an orthogonal biochemical method supporting ssRNA binding to ZIKV NS2B-NS3pro.

• binding studies with RNA used artificial construct, how about the one with KTGR present like eZiPro. Keep in mind that the P1-P4 residues are present under native conditions.*

__- __As mentioned by the reviewer, TGKR peptide was found in the active center in the eZiPro crystal. Indeed, the junction region between NS2B and NS3 protease contains native cleavage sites for the NS2B-NS3Pro and is naturally cleaved by protease during the viral polyprotein processing. However, the TGKR peptide representing P1-P4 positions will have to leave the active center after the cleavage to ensure enzyme processivity/cleaving additional targets (otherwise, the protease would get stacked after the first cleavage). Proteolytic activity assay utilizes the fluorogenic peptide labeled with FAM (such as TGKR-FAM; where FAM is a group representing P1’ position in this case). TGKR-FAM peptide will compete and easily replace cleaved TGKR peptide from the active center in proteolytic activity assay. In sum, the C-terminal end of NS2B will be competed out of the protease active center by the next substrate, and there is no evidence that it will be naturally placed back in the active center after each round of protease proteolytic activity. Indeed, several crystal structures of flaviviral NS2B-NS3Pro in open conformation lack the C-terminal part of NS2B in the active center. Our unpublished NMR studies demonstrated that the C-terminal part of NS2B is unstructured in solution if the substrate peptide or small molecule inhibitor are not present in the active center of the protease.

• authors built up nice models, it is great to consider the full length NS2B, but authors haven't taken into account the effect of NS2B on the open or closed conformation of the protease. *

- __ All crystal structures of flavivirus NS2B-NS3pro in the closed, open, or super-open conformations have NS2B associated withNS3pro via a beta-barrel (__Rebuttal Figure 3), which is located at the opposite side from the RNA binding site. The transition from the closed to the open and to the super-open conformation is associated with the progressive dissociation of NS2B from NS3pro. Therefore, the effect of NS2B on NS3Pro is progressively diminished. In the closed conformation of NS3Pro, the negatively charged C-terminal part of NS2B is associated with the same positively charged grove as the RNA in the open conformation of NS3Pro. The C-terminal part of NS2B is dissociated from NS3Pro in the open conformation.

Minor issues:

*This manuscript shows the novel function of zika protease and conclude that protease binds to RNA. This is a novel finding, but the conclusion needs to be further confirmed, to avoid misinterpretations by future readers *

• closed, and super open conformations. But the definition was not carefully compared with current literatures. I am surprised that the two important papers are not cited. It is well known the G4SG4 linker affect the conformation of the protease.*

• The crystal structures and the proteolytic activities of gZiPro, eZiPro, and bZiPro are rather similar. In fact, Km (μM) are 2.86 ± 0.90 for gZiPro, 6.332 ± 2.41 for bZiPro, and the IC 50s of BPTI inhibition for gZiPro, eZiPro and bZiPro are 350, 76 and 12 nM respectively. NS2B and NS3pro have a large binding area in the closed conformation. Upon changing the conformation to the open conformation (and even more so to the super-open conformation), the C-terminal part of NS2B is progressively dissociated from NS3Pro. Therefore, possible minor effects introduced by the G4SG4 linker is unlikely to affect any of the conclusions in our work.

• Authors need to show super open conformation is present in nature e.g. the model in which full length NS2B and NS3pro.*

• A full-length NS2B has 2 transmembrane domains, which tether the NS2B-NS3pro complex to the cell membrane (we have modeled the presence of such transmembrane domains to account for the orientation of NS2B-NS3pro with respect to the cell membrane). The full-length complex has never been crystallized or tested in any assay due to the major technical challenges associated with the modeling of complex transmembrane proteins.

• RNA is a charged molecule under some conditions, NS3 also have charged residues, it is important to show whether the binding between RNA-protease is relevant to the function{Luo, 2010 #9270;Chernov, 2008 #9275;Xu, 2019 #10006}, or is this due to the application of the artificial constructs used in this study. Why so many mutants are used? *

• The requirement of NS3pro for the helicase function was shown by several investigators 7–9. Given the structural independence of NS3pro and NS3hel, which mostly rules out the allosteric effect, RNA binding by NS3pro is a newly proposed function of NS3pro for the helicase activity. We demonstrated biochemically that RNA-bound to NS3pro inhibits its protease function. A variety of mutants were used to constrain the conformations of NS2B-NS3pro (e.g. enforce the super-open confirmation) for crystallization studies.

• Using a construct close to the native protease, at least the P1-P4 residues should be present. Using a peptide in the assay is also useful.*

• We were unable to interpret this critique.

• Test binding of RNA with protease using another method such as biophysical methods, or even gel shift assay*

• We thank the reviewer for this suggestion. Although the gel-shift assay seems to be a reasonable method to test the binding, given the ease of spontaneous conformational change (i.e. into the super-open conformation), this assay could result in a progressive loss of bound RNA during migration in the gel.

• I don't know the correlation between Figure 7 and Figure 6. The authors describe ploy A binding to protease, while Figure 7 is talking about Helicase binds to dsRNAs. *

• There is no correlation. Figure 6 describes the models for NS2B-NS3pro binding to ssRNA. Figure 7 describes a separate point, the direction of dsRNA processing by NS3hel.

• I am glad to see the consideration of full length NS2B, NS3 in the models Figure 8, 9 and 11, but there is no data to support any of the model proposed. *

• There is no experimental data. We have modeled the N-terminal and C-terminal parts of full NS2B, which are predicted to be inserted into the cell membrane due to their characteristic amphipathic helical structure.

• Is the linker a ploy G not G4SG4? *

The linker is GGGGSGGGG (G4SG4) as stated in Materials and Methods of the manuscript.

• Do the mutant sustain their protease activity? *

• All mutants with intact catalytic centers have protease activity, except the mutants with a disulfide bridge that fixes the polypeptides in the super-open conformation.

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

*The manuscript by Shiryaev et al., submitted to BioRXiv is an exploration of the ability of NS2B-NS3protease to bind RNA and its subsequent role in NS3 helicase processivity. The authors first utilize fluorescence polarization assays to demonstrate that NS2B-NS3protease can bind ssRNA with a strong affinity (and also ssDNA with lower affinity). They subsequently utilize mutational and small molecule inhibitor strategies in these assays to force the NS2B-NS3protease into different conformations, with the associated results inferring that the "open" conformation is responsible for ssRNA binding affinity. Furthermore, they demonstrate that ssRNA binding impairs protease activity, suggesting these roles may be exclusive in the viral life cycle. They also identified a number of small molecule ligands that target the putative ssRNA binding channel, and demonstrate that these ligands inhibit ssRNA binding by NS2B-NS3protease, providing potential inhibitor candidates for ZIKV. Finally, the authors utilized their crystal structures and others for the various conformations of NS2B-NS3protease to model ssRNA binding by the domain and the full NS3 protein, and used these models to propose a reverse inchworm model for NS3 travelling along ssRNA as it unwinds the dsRNA duplex. Overall, the authors utilize a comprehensive approach to demonstrate a number of novel findings (ssRNA binding by NS2B-NS3protease, small molecule ligands that inhibit this interaction) that would be of interest to both virologists and structural biologists. However, there are some important experimental design limitations and viral life cycle considerations that the authors should address before acceptance of the manuscript. Major and minor comments intended to improve the manuscript are outlined in more detail below. *

Major Comments:

1. • While the quantity of indirect data (ruled out closed and super-open, inhibitors of ssRNA binding pocket) suggest that the open conformation of NS2B-NS3protease is associated with ssRNA binding, the argument would be greatly strengthened by direct experimental data. Is there a mutational or small molecule approach to locking the NS2B-NS3 protease in the open conformation? If so, the authors should perform such experiments to strengthen the foundation of their argument.*

2. Unfortunately, despite significant efforts, mutations or small molecules locking the NS2B-NS3 protease in the open conformation have not been identified for the ZIKV protease. However, several structures for NS2B-NS3 proteases have been documented in other flaviviruses (i.e., DENV PDB IDs 2FOM and 5T1V; WNV PDB ID 2GGV). Polypeptides with over 35% identity are very likely to have a similar fold2. Given over 50% identity(!) between flaviviral proteases across the family3,4, there is little doubt that ZIKV NS2-NS3 protease adopts an open conformation similar to all flaviviral proteases. Our modeling demonstrated that there are no sterically/structural problems in folding NS2B-NS3 protease into the open conformation.

3. A negative control should be used in Figure 4A to strengthen the claim that ssRNA binding in the open conformation impairs protease activity (ie. include a curve for dsRNA). Such an experiment would lend support to ssRNA inhibition being due to specific binding instead of some other non-specific effect of increasing local nucleic acid concentration.*

4. To address this critique, we have conducted the modeling of dsRNA binding to the open conformation of NS2B-NS3Pro. The model revealed that dsRNA could not be accommodated by the open conformation of the NS2B-NS3Pro complex (Rebuttal Figure 4). Indeed, dsRNA has a very different rigid structure compared to the extended form of the ssRNA chain. The dsRNA is unable to provide continuous interactions between negatively RNA backbone and positively charged side chain amino acids in NS3pro. The continuous interface on NS2B-NS3 protease interacting with ssRNA is an extension of the exit groove for one of the ssRNA strands exiting the NS3 Helicase after unwinding. Therefore, the ssRNA, but not dsRNA is naturally always present in close proximity of the NS2B-NS3Pro complex.

5. *

6. Due to the highly coupled roles of NS5 and NS3 in replication, the authors should include some more consideration of the role of NS5 in their complex. They very briefly address this interplay in the fifth paragraph of the discussion, but then neglect to discuss the implications any further. In particular (perhaps in a brief comparison to an NS3/NS5 modeling approach such as Brands et al., 2017; WIRES), the authors should consider some of the following questions: could the channel on protease domain lead to ssRNA entry site on RdRp?*

7. Indeed, our model suggests that the negative strand (-)ssRNA exits from NS2B-NS3protease facing the ER membrane in the area where the protease is anchored to the ER membrane via the NS2B transmembrane domains. It is possible that NS3pro interacts with NS5 polymerase and “handles” (-)ssRNA to the NS5 polymerase. This scenario would modify Brands et al., 2017 model to add NS2B-NS3Pro complex between NS3Hel and NS5. However, at present, the NS3-NS5 (or NS2B-NS3-NS5) complex together has not been crystallized. It would be logical for NS5 polymerase to access the (-)ssRNA strand after it is released from NS2B-NS3Pro since the (-)ssRNA strands are used as a template for the (+)ssRNA which is used for polyprotein synthesis and packaging into viral particles.

8. would NS5 interaction constrain or augment inchworm model of NS2B/NS3 translocation? *

9. Yes, integrating NS5 interaction with the NS2B-NS3pro handling (-)ssRNA will augment the utility of the suggested reverse inchworm model.

10. how does increased activity of NS3 when complexed with NS5 (**Xu et al. 2019) align with proposed inchworm model? *

11. We appreciate the reviewer's question. We think that NS2, NS3, NS4, and NS5 work in concert as one coordinated complex where various subunits of NS2 and NS4 may provide anchoring of the entire complex to the ER membrane. Indeed, such a complex has recently been proposed6. Also, see our response to the previous reviewer’s point (#4). We have incorporated this discussion into the revised manuscript.

Minor Comments: 1. Introduction, 4th paragraph, NS3-NS4 should read NS3-NS4A.

• We corrected this sentence.

* ** Throughout the manuscript, the authors should denote some key amino acid residues in each figure to help orient the reader better to the observed structural changes and rotations. Inclusion, at least in the supplement, of the crystal structures of mutants solved herein should **also be included. *

• We annotated the key residues in all figures (e.g. catalytic residues, loop interacting with the membrane, position of NS2B, and other elements) and kept the same orientation of complexes in all figures.

• Section: RNA binding inhibits the proteolytic activity of ZIKV NS2B-NS3pro, last sentence, NS2N-NS3pro should be NS2B-NS3pro*.

• We corrected this sentence.

• Section: Allosteric inhibitors of NS2B-NS3 protease interfere with RNA binding- first sentence: "The open conformation of NS2B-NS3pro is achieved by the rearrangement of NS2B cofactor (its dissociation from the C-terminal half of NS3pro) leading to a loss of proteolytic activity [32]. - the reference is not correct. I could not find the reference the authors refer to here and had not heard before that NS2B cofactor was able to disassociate from the C-terminal half of NS3pro; hence, this really needs to be appropriately referenced. *

• We have revised this sentence and added additional references. “The open conformation of NS2B-NS3pro is achieved by the rearrangement of NS2B cofactor (partial dissociation from NS3pro), leading to a loss of proteolytic activity4,11.”

• Section: Modeling RNA binding to ZIKV NS2B-NS3, first sentence - unwinds should be unwind*.

• We corrected this sentence.

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• With respect to the results of Figure 3A, the authors should address that adding the linker alone to the NS3 protease may not be an accurate examination of its role/importance. The linker in this scenario is only constrained at its N-terminus, while it is always constrained at both termini during infection (and even more so by the interactions of those two linked domains [protease and helicase] with each other). As such, the authors statement that "observations suggests that the 12-aa linker region modulates RNA binding to NS2B-NS3pro" should be more strongly qualified to this effect. In addition, it would be interesting to see the effects of the linker mutations on ssRNA binding in the context of the full NS3 protein, albeit admittedly more complex due to the confounding ssRNA binding by the helicase domain.*

• We agree with this reviewer that the protease-helicase linker is also restrained at both termini. We have rephrased the statement in the revised manuscript. The goal of the experiment shown in Figure 3A was to examine whether a negatively charged linker is able to compete with ssRNA binding as we expected from the structural model. The mutational analysis of the protease helicase linker is, indeed, a very interesting subject that is, however, beyond the scope of this work.

7. The NS#hel should be changed to NS3hel in part (C) of figure legend for Figure 11. - We corrected this mishap.

• The authors data in Figure 4A (and even more so the nature of the viral life cycle where 1000s of viral polyproteins are created from the first genome during infection) disputes the depiction in the inchworm model of how NS3 protease cleaves the polyprotein while the helicase binds ssRNA. At minimum, the authors need to discuss this discrepancy, and it is recommended that they modify the cartoon in their model to not include the ssRNA binding on the protease side of the equation (or show as alternative on that side to the existing cartoon).*

• Indeed, as proposed by our reverse inchworm model, ssRNA is not bound to NS3Pro in the closed conformation, while NS2B-NS3pro has a protein substrate in the active center (Figure 11A). We agree that NS2B-NS3Pro in the closed conformation cannot bind ssRNA as we demonstrated in competitive cleavage assay. Only large amounts of ssRNA can shift the balance towards the open conformation which binds ssRNA. We think that most of the time NS2B-NS3Pro cycles between the open and the super conformations handling ssRNA (Figure 11(B-C_D), but as soon as protein substrate becomes available (typically a loop from a transmembrane viral polypeptide), NS2B-NS3Pro quickly switches to the closed proteolytically active conformation to act as protease.

• In the third paragraph of the discussion, the authors state "An alternative model of coupled transcription and translation where viral RNA is associated with ribosomes right after the release from NS2B-NS3 is also possible". Considering there is abundant evidence that translation and replication are exclusive and that translation does not take place in ROs, it would be prudent to remove such statements from the discussion. Without any supporting evidence, these statements will be misleading to readers by providing a false equivalency. The preceding discussion of RFs would be sufficient to contextualize your inchworm model in the broader viral life cycle (which was done quite well). *

• We have adjusted the discussion in the revised manuscript to avoid a false equivalency.

10. There were a number of aspects I appreciated about the manuscript and will briefly list a few here: ** i) the focus on how different non-structural proteins effect the structure and function of ** each other during the viral life cycle, which forms a more comprehensive and informative model ** ii) the use of structural and functional assays as complementary approaches to studying the intra- and inter-protein relationships of NS3 ** iii) the depiction of the forks in Figure 10, which effectively demonstrated the channels and oriented the reader to the conservation data ** *iv) the use of small molecule inhibitors to modify structure and function of NS3, which greatly deepened the richness of the story from both a basic and applied science view point *

• We are very grateful to the Reviewer for these kind remarks.

Reviewer #2 (Significance (Required)): ** Strengths and limitations: ** - provides some experimental and modeling data to provide a new model for RNA interactions with the NS3pro-hel; may help inform models for enzyme function, mostly consistent with previous literature ** - leaves out the NS5 RdRp, known to contribute to NS3 activity. ** - some suggestions are made which might strengthen the conclusions and inclusions of additional controls would improve the data. ** Advance ** - conceptual, perhaps may provide some insight into mechanism; although limited by the lack of NS5 RdRp which is crucial to helicase activity. It is unclear if the ssRNA would be oriented this way given interactions with NS5 RdRp and MT domains (is the ssRNA routed to NS5 or along NS3, or potentially are both happening?) ** Audience: ** - quite specialist, but may include structural biologists and virologist alike. ** Expertise of the reviewer(s): ** *- molecular virologists, RNA viruses - including flaviviruses; replication complex biogenesis, protein-RNA and RNA-RNA interactions. While comfortable with the concepts regarding complex formation, the appropriateness of computational modeling and RNA docking tools as well as structural biology is out of our area of expertise. *

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

*This paper investigates the nucleic acid binding properties of zika virus protease. In particular the data suggest that single stranded RNAs and DNAs are capable of binding to and inhibiting ZIKV protease at micromolar concentrations. With the use of active site inhibitors and mutants that lock the protease in closed and super-open conformation, the authors concluded that RNA binds to the open conformation. Through extensive modeling of the protease and helicase domains, this manuscript provides a model of how ssRNAs can bind to all conformations of the proteas, but the open conformation provides two positively charged forks that should be available to bind RNA. *

* SECTION A - Evidence, reproducibility, and clarity ** Major comments: **

*·The main conclusions of this paper rely on the existence of the super-open conformation, however this conformation has not been reported in the scientific literature previously. Structures deposited in the pdb are referenced in this manuscript, however no citation for an accompanying publication is provided. This calls into question the biological relevance of this super open conformation. This is of particular concern because in other highly-homologous flaviviral proteases, structures that have been observed crystallographically (e.g. the open conformation of dengue virus protease) appear to be only very sparsely populated in solution. What is the evidence that the super-open conformation exists in solution.

• Please, see our reply to question #1 from Reviewer 1.

• The activity of each of the constructs used was not reported making it impossible to directly compare the impact of these changes on intrinsic activity. In particular, the NS2B-NS3 long construct is predicted to exist in the super-open conformation. If this is correct, it should show no activity against a peptide substrate. *

• We appreciate these concerns. The NS2B-NS3pro-long construct is proteolytically active (only NS2B-NS3pro-short construct is proteolytically inactive because its NS3pro C-terminal part is too short to fold into the closed conformation). It is unconstrained and likely capable of adopting all possible conformations (closed, open, super open). As we suspected, the negatively charged linker interferes with RNA binding, potentially via direct competition. Investigating the role of the protease-helicase linker is an exciting subject of a separate manuscript in preparation.

• This paper reports that the IC50 is much weaker than the Kd for binding of ssRNA to ZIKV NS2B-NS3pro. Are orthogonal assays, such as thermal shift assay, available which could distinguish between the reported IC50 and the Kd. *

• Binding of ssRNA occurs in an area distinct from the protease active center. We think that there is a constant competition between C-terminal NS2B binding/release versus ssRNA binding/release from NS3pro. We think that ssRNA “catches” the moment when protease has the open conformation and freezes that conformation by blocking the C-terminal of NS2B from binding to NS3Pro. In terms of thermal shift assay, the structure of NS3Pro is changed, only the C-terminal of NS2B is affected. Note that the 15N R2 NMR signal from NS2B residues 65-85 is missing in bZiPro alone but re-appears when AcKR is added6. This is consistent with the idea that without AcKR, bZiPro exists in the open conformation where much of the C-terminal part of NS2B is dissociated from NS3Pro and remains unstructured, thus resulting in the lack of NMR signal. Taken together, these observations suggest that thermal shift assay is unlikely to be of much help.

• *This paper suggests that ssRNA binds to the open conformation of ZIKV NS2B-NS3pro, however no experimental evidence, only modeling has been used to suggest binding to the open conformation. In Dengue virus protease, the M84P variant has been reported to lock the protease into the open conformation. How does the F84P variant of ZIKV NS2B-NS3pro impact ssRNA binding? *

• We appreciate this question. Indeed, M84P mutation shifts Dengue NS3Pro to the open conformation, which is proteolytically inactive12, consistent with our reverse inchworm model. We have not investigated the effect of this mutation on ZIKV NS3pro. We expect this mutation has a similar effect in ZIKV NS3pro in Dengue NS3Pro.

• The relevance of the discussion on the co-crystallization of NSC86314 with the Mut7was not clear. What point was being made?

• We provide a proof-of-principle for a novel class of allosteric inhibitors that specifically target newly identified druggable pockets present in the open and super-open conformations of ZIKV NS2B-NS3pro. Our results suggest that such allosteric inhibitors can interfere with the RNA-binding activities of NS2B-NS3pro in addition to blocking the protease activity. The co-crystallization of NSC86314 with the Mut7 confirms a novel pocked bound by NSC86314.

*- These data show that both active site and allosteric inhibitors block binding of ssRNA to the protease. The paper also suggests that ssRNA only binds to the open conformation. What is the evidence that the allosteric inhibitors do not enable or promote formation of the open conformation? *

• We thank this reviewer for an interesting question. Indeed, we have no evidence of whether allosteric inhibitors enable or promote the formation of the open conformation. This is formally possible and will need to be investigated.

• This paper makes two claims about the function of the protease. The title should specify what those dual functions are (proteolytic activity and ssRNA-recruitment).*

• We appreciate this reviewer's suggestions for the title.

• The discussion of Figures 6 and 9 are highly similar. The main takeaway points for both figures seem to be nearly identical: the presence of two positively charged pitchfork on the open conformation. The distinction between these two figures should be more significantly and explicitly stated. *
• Figure 6 presents several models that provide evidence for the open conformation of ZIKV NS2B-NS3pro being uniquely suitable to bind RNA. Figure 9 presents several models of the entire RNA-NS2B-NS3pro-NS3hel complex anchored into the ER membrane. Figure 9 illustrates that the open conformation of NS2B-NS3pro provides two positively charged/polar forks, contiguous with the positively charged groove on NS3hel. Figure 6 does not illustrate that point.

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*- Mention explicitly in the materials and methods if the 12-amino acid linker is present in all the mutants used. *

• This is mentioned explicitly and shown in Supplementary Figure 2A.

Minor comments: ** · Figure 1. The rotation that promotes the transitions from orientation in panel A to that in panel B should be drawn. ** · FAM should be defined in the legend of Figure 2. ** · The term Cold should be changed to unlabeled. ** · Please check labels for the supplementary Figure 2. For example one label states 1-1 but it ** should be 1-170. ** · Figure 1C does not exist and it is referenced in the results section under "NS2B-NS3pro substrate-mimicking inhibitors compete with RNA binding." ** · As discussed above, if the super open conformation is going to be addressed in this paper, then either a reference for the manuscript describing those structures should be included, or this manuscript should include in the materials and methods the procedure on crystallization, data collection, structure determination, refinement, and analysis as well as a table for crystallographic data and refinement statistics. ** · Adjust figure arrangement (ABCED to ABCDE) in Figure 11.

• We thank this reviewer for all minor comments. We corrected the above-mentioned errors in the manuscript.

Reviewer #3 (Significance (Required)): ** It is well established that the flaviviral proteases exist in different conformations but most of the structures published are concentrated on the closed conformation which is the one required for effective substrate processing. The open conformation has recently been the subject of increased interest, especially with the discovery of allosteric inhibitors for which modeling suggests that these compounds result in the dissociation of the C-terminal region of NS2B from the NS3. This paper adds important insights into the function of the open conformation and in general implicitly shows the importance of the dynamic nature of ZIKV NS2B-NS3pro. In addition to these insights, this paper aptly demonstrates that ssRNA can bind and inhibit these proteases as has not been shown previously. ** I am a senior graduate student working on characterizing and understanding the mechanism of action of allosteric compounds against viral proteases, specifically proteases from Zika and dengue viruses.

References.

1. Weinert T, Olieric V, Waltersperger S, Panepucci E, Chen L, Zhang H, Zhou D, Rose J, Ebihara A, Kuramitsu S, Li D, Howe N, Schnapp G, Pautsch A, Bargsten K, Prota AE, Surana P, Kottur J, Nair DT, Basilico F, Cecatiello V, Pasqualato S, Boland A, Weichenrieder O, Wang BC, Steinmetz MO, Caffrey M, Wang M. Fast native-SAD phasing for routine macromolecular structure determination. Nat Methods. nature.com; 2015 Feb;12(2):131–133. PMID: 25506719
2. Solis AD, Rackovsky SR. Fold homology detection using sequence fragment composition profiles of proteins. Proteins. 2010 Oct;78(13):2745–2756. PMCID: PMC2933786
3. Brinkworth RI, Fairlie DP, Leung D, Young PR. Homology model of the dengue 2 virus NS3 protease: putative interactions with both substrate and NS2B cofactor. J Gen Virol. 1999 May;80 ( Pt 5):1167–1177. PMID: 10355763
4. Aleshin AE, Shiryaev SA, Strongin AY, Liddington RC. Structural evidence for regulation and specificity of flaviviral proteases and evolution of the Flaviviridae fold. Protein Sci. 2007 May;16(5):795–806. PMCID: PMC2206648
5. Phoo WW, Li Y, Zhang Z, Lee MY, Loh YR, Tan YB, Ng EY, Lescar J, Kang C, Luo D. Structure of the NS2B-NS3 protease from Zika virus after self-cleavage. Nat Commun. 2016 Nov 15;7:13410. PMCID: PMC5116066
6. Zhang Z, Li Y, Loh YR, Phoo WW, Hung AW, Kang C, Luo D. Crystal structure of unlinked NS2B-NS3 protease from Zika virus. Science. science.org; 2016 Dec 23;354(6319):1597–1600. PMID: 27940580
7. Luo D, Wei N, Doan DN, Paradkar PN, Chong Y, Davidson AD, Kotaka M, Lescar J, Vasudevan SG. Flexibility between the protease and helicase domains of the dengue virus NS3 protein conferred by the linker region and its functional implications. J Biol Chem. 2010 Jun 11;285(24):18817–18827. PMCID: PMC2881804
8. Chernov AV, Shiryaev SA, Aleshin AE, Ratnikov BI, Smith JW, Liddington RC, Strongin AY. The two-component NS2B-NS3 proteinase represses DNA unwinding activity of the West Nile virus NS3 helicase. J Biol Chem. 2008 Jun 20;283(25):17270–17278. PMCID: PMC2427327
9. Xu S, Ci Y, Wang L, Yang Y, Zhang L, Xu C, Qin C, Shi L. Zika virus NS3 is a canonical RNA helicase stimulated by NS5 RNA polymerase. Nucleic Acids Res. 2019 Sep 19;47(16):8693–8707. PMCID: PMC6895266
10. Klema VJ, Padmanabhan R, Choi KH. Flaviviral Replication Complex: Coordination between RNA Synthesis and 5’-RNA Capping. Viruses. 2015 Aug 13;7(8):4640–4656. PMCID: PMC4576198
11. Shiryaev SA, Aleshin AE, Muranaka N, Kukreja M, Routenberg DA, Remacle AG, Liddington RC, Cieplak P, Kozlov IA, Strongin AY. Structural and functional diversity of metalloproteinases encoded by the Bacteroides fragilis pathogenicity island. FEBS J. 2014 Jun;281(11):2487–2502. PMCID: PMC4047133
12. Lee WHK, Liu W, Fan JS, Yang D. Dengue virus protease activity modulated by dynamics of protease cofactor. Biophys J. 2021 Jun 15;120(12):2444–2453. PMCID: PMC8390872

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Referee #3

Evidence, reproducibility and clarity

This paper investigates the nucleic acid binding properties of zika virus protease. In particular the data suggest that single stranded RNAs and DNAs are capable of binding to and inhibiting ZIKV protease at micromolar concentrations. With the use of active site inhibitors and mutants that lock the protease in closed and super-open conformation, the authors concluded that RNA binds to the open conformation. Through extensive modeling of the protease and helicase domains, this manuscript provides a model of how ssRNAs can bind to all conformations of the proteas, but the open conformation provides two positively charged forks that should be available to bind RNA.

SECTION A - Evidence, reproducibility, and clarity

Major comments:

• The main conclusions of this paper rely on the existence of the super-open conformation, however this conformation has not been reported in the scientific literature previously. Structures deposited in the pdb are referenced in this manuscript, however no citation for an accompanying publication is provided. This calls into question the biological relevance of this super open conformation. This is of particular concern because in other highly-homologous flaviviral proteases, structures that have been observed crystallographically (e.g. the open conformation of dengue virus protease) appear to be only very sparsely populated in solution. What is the evidence that the super-open conformation exists in solution.
• The activity of each of the constructs used was not reported making it impossible to directly compare the impact of these changes on intrinsic activity. In particular, the NS2B-NS3 long construct is predicted to exist in the super-open conformation. If this is correct, it should show no activity against a peptide substrate.
• This paper reports that the IC50 is much weaker than the Kd for binding of ssRNA to ZIKV NS2B-NS3pro. Are orthogonal assays, such as thermal shift assay, available which could distinguish between the reported IC50 and the Kd.
• This paper suggests that ssRNA binds to the open conformation of ZIKV NS2B-NS3pro, however no experimental evidence, only modeling has been used to suggest binding to the open conformation. In Dengue virus protease, the M84P variant has been reported to lock the protease into the open conformation. How does the F84P varian of ZIKV NS2B-NS3pro impact ssRNA binding?
• The relevance of the discussion on the co-crystallization of NSC86314 with the Mut7was not clear. What point was being made?
• These data show that both active site and allosteric inhibitors block binding of ssRNA to the protease. The paper also suggests that ssRNA only binds to the open conformation. What is the evidence that the allosteric inhibitors do not enable or promote formation of the open conformation?
• This paper makes two claims about the function of the protease. The title should specify what those dual functions are (proteolytic activity and ssRNA-recruitment).
• The discussion of Figures 6 and 9 are highly similar. The main takeaway points for both figures seem to be nearly identical: the presence of two positively charged pitchfork on the open conformation. The distinction between these two figures should be more significantly and explicitly stated.
• Mention explicitly in the materials and methods if the 12-amino acid linker is present in all the mutants used.

Minor comments:

• Figure 1. The rotation that promotes the transitions from orientation in panel A to that in panel B should be drawn.
• FAM should be defined in the legend of Figure 2.
• The term Cold should be changed to unlabeled.
• Please check labels for the supplementary Figure 2. For example one label states 1-1 but it should be 1-170.
• Figure 1C does not exist and it is referenced in the results section under "NS2B-NS3pro substrate-mimicking inhibitors compete with RNA binding."
• As discussed above, if the super open conformation is going to be addressed in this paper, then either a reference for the manuscript describing those structures should be included, or this manuscript should include in the materials and methods the procedure on crystallization, data collection, structure determination, refinement, and analysis as well as a table for crystallographic data and refinement statistics.
• Adjust figure arrangement (ABCED to ABCDE) in Figure 11.

Significance

It is well established that the flaviviral proteases exist in different conformations but most of the structures published are concentrated on the closed conformation which is the one required for effective substrate processing. The open conformation has recently been the subject of increased interest, especially with the discovery of allosteric inhibitors for which modeling suggests that these compounds result in the dissociation of the C-terminal region of NS2B from the NS3. This paper adds important insights into the function of the open conformation and in general implicitly shows the importance of the dynamic nature of ZIKV NS2B-NS3pro. In addition to these insights, this paper aptly demonstrates that ssRNA can bind and inhibit these proteases as has not been shown previously.

I am a senior graduate student working on characterizing and understanding the mechanism of action of allosteric compounds against viral proteases, specifically proteases from Zika and dengue viruses.

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 #2

Evidence, reproducibility and clarity

The manuscript by Shiryaev et al., submitted to BioRXiv is an exploration of the ability of NS2B-NS3protease to bind RNA and its subsequent role in NS3 helicase processivity. The authors first utilize fluorescence polarization assays to demonstrate that NS2B-NS3protease can bind ssRNA with a strong affinity (and also ssDNA with lower affinity). They subsequently utilize mutational and small molecule inhibitor strategies in these assays to force the NS2B-NS3protease into different conformations, with the associated results inferring that the "open" conformation is responsible for ssRNA binding affinity. Furthermore, they demonstrate that ssRNA binding impairs protease activity, suggesting these roles may be exclusive in the viral life cycle. They also identified a number of small molecule ligands that target the putative ssRNA binding channel, and demonstrate that these ligands inhibit ssRNA binding by NS2B-NS3protease, providing potential inhibitor candidates for ZIKV. Finally, the authors utilized their crystal structures and others for the various conformations of NS2B-NS3protease to model ssRNA binding by the domain and the full NS3 protein, and used these models to propose a reverse inchworm model for NS3 travelling along ssRNA as it unwinds the dsRNA duplex. Overall, the authors utilize a comprehensive approach to demonstrate a number of novel findings (ssRNA binding by NS2B-NS3protease, small molecule ligands that inhibit this interaction) that would be of interest to both virologists and structural biologists. However, there are some important experimental design limitations and viral life cycle considerations that the authors should address before acceptance of the manuscript. Major and minor comments intended to improve the manuscript are outlined in more detail below.

Major Comments:

1. While the quantity of indirect data (ruled out closed and super-open, inhibitors of ssRNA binding pocket) suggest that the open conformation of NS2B-NS3protease is associated with ssRNA binding, the argument would be greatly strengthened by direct experimental data. Is there a mutational or small molecule approach to locking the NS2B-NS3 protease in the open conformation? If so, the authors should perform such experiments to strengthen the foundation of their argument.
2. A negative control should be used in Figure 4A to strengthen the claim that ssRNA binding in the open conformation impairs protease activity (ie. include a curve for dsRNA). Such an experiment would lend support to ssRNA inhibition being due to specific binding instead of some other non-specific effect of increasing local nucleic acid concentration.
3. Due to the highly coupled roles of NS5 and NS3 in replication, the authors should include some more consideration of the role of NS5 in their complex. They very briefly address this interplay in the fifth paragraph of the discussion, but then neglect to discuss the implications any further.

In particular (perhaps in a brief comparison to an NS3/NS5 modeling approach such as Brands et al., 2017; WIRES), the authors should consider some of the following questions: - could the channel on protease domain lead to ssRNA entry site on RdRp? - would NS5 interaction constrain or augment inchworm model of NS2B/NS3 translocation? - how does increased activity of NS3 when complexed with NS5 (Xu et al. 2019) align with proposed inchworm model?

Minor Comments:

1. Introduction, 4th paragraph, NS3-NS4 should read NS3-NS4A.
2. Throughout the manuscript, the authors should denote some key amino acid residues in each figure to help orient the reader better to the observed structural changes and rotations. Inclusion, at least in the supplement, of the crystal structures of mutants solved herein should also be included.
3. Section: RNA binding inhibits the proteolytic activity of ZIKV NS2B-NS3pro, last sentence, NS2N-NS3pro should be NS2B-NS3pro
4. Section: Allosteric inhibitors of NS2B-NS3 protease interfere with RNA binding- first sentence: "The open conformation of NS2B-NS3pro is achieved by the rearrangement of NS2B cofactor (its dissociation from the C-terminal half of NS3pro) leading to a loss of proteolytic activity [32]. - the reference is not correct. I could not find the reference the authors refer to here and had not heard before that NS2B cofactor was able to disassociate from the C-terminal half of NS3pro; hence, this really needs to be appropriately referenced.
5. Section: Modeling RNA binding to ZIKV NS2B-NS3, first sentence - unwinds should be unwind
6. With respect to the results of Figure 3A, the authors should address that adding the linker alone to the NS3 protease may not be an accurate examination of its role/importance. The linker in this scenario is only constrained at its N-terminus, while it is always constrained at both termini during infection (and even more so by the interactions of those two linked domains [protease and helicase] with each other). As such, the authors statement that "observations suggests that the 12-aa linker region modulates RNA binding to NS2B-NS3pro" should be more strongly qualified to this effect.

In addition, it would be interesting to see the effects of the linker mutations on ssRNA binding in the context of the full NS3 protein, albeit admittedly more complex due to the confounding ssRNA binding by the helicase domain. 7. The NS#hel should be changed to NS3hel in part (C) of figure legend for Figure 11. 8. The authors data in Figure 4A (and even more so the nature of the viral life cycle where 1000s of viral polyproteins are created from the first genome during infection) disputes the depiction in the inchworm model of how NS3 protease cleaves the polyprotein while the helicase binds ssRNA. At minimum, the authors need to discuss this discrepancy, and it is recommended that they modify the cartoon in their model to not include the ssRNA binding on the protease side of the equation (or show as alternative on that side to the existing cartoon). 9. In the third paragraph of the discussion, the authors state "An alternative model of coupled transcription and translation where viral RNA is associated with ribosomes right after the release from NS2B-NS3 is also possible". Considering there is abundant evidence that translation and replication are exclusive and that translation does not take place in ROs, it would be prudent to remove such statements from the discussion. Without any supporting evidence, these statements will be misleading to readers by providing a false equivalency. The preceding discussion of RFs would be sufficient to contextualize your inchworm model in the broader viral life cycle (which was done quite well). 10. There were a number of aspects I appreciated about the manuscript and will briefly list a few here:

- i) the focus on how different non-structural proteins effect the structure and function of

each other during the viral life cycle, which forms a more comprehensive and informative model - ii) the use of structural and functional assays as complementary approaches to studying the intra- and inter-protein relationships of NS3 - iii) the depiction of the forks in Figure 10, which effectively demonstrated the channels and oriented the reader to the conservation data - iv) the use of small molecule inhibitors to modify structure and function of NS3, which greatly deepened the richness of the story from both a basic and applied science view point

Significance

Strengths and limitations:

• provides some experimental and modeling data to provide a new model for RNA interactions with the NS3pro-hel; may help inform models for enzyme function, mostly consistent with previous literature
• leaves out the NS5 RdRp, known to contribute to NS3 activity.
• some suggestions are made which might strengthen the conclusions and inclusions of additional controls would improve the data.

Advance

• conceptual, perhaps may provide some insight into mechanism; although limited by the lack of NS5 RdRp which is crucial to helicase activity. It is unclear if the ssRNA would be oriented this way given interactions with NS5 RdRp and MT domains (is the ssRNA routed to NS5 or along NS3, or potentially are both happening?)

Audience:

• quite specialist, but may include structural biologists and virologist alike.

Expertise of the reviewer(s):

• molecular virologists, RNA viruses - including flaviviruses; replication complex biogenesis, protein-RNA and RNA-RNA interactions. While comfortable with the concepts regarding complex formation, the appropriateness of computational modeling and RNA docking tools as well as structural biology is out of our area of expertise.

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

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Referee #1

Evidence, reproducibility and clarity

The current manuscript by Shiryaev et al describes their observation of the new function of zika NS2B-NS3 proteases. They have shown that NS2B-NS3 protease lacking the helicase domain binds to RNA and the interaction can be affected by protease inhibitors. Main two new findings are presented in the manuscript: super open conformation of the protease; RNA binding activity of the protease region. although the manuscript is interesting, the design of the experiments is not convincing.

Major issues

1. the claim of a super open conformation is problematic. Using an artificial construct lacking the C-terminal portion of NS2B will of course generate the open conformation. This is a wrong definition unless you observe such a conformation in living cells.
2. It is odd that authors made homology model to generate open conformation structures. the authors did not cite the two papers of eZiPro (phoo et al 2016 NC) and bZiPro (Zhang et al 2016, Science). these two structures show the closed conformation of protease in the absence and presence of natural substrate.
3. RNA binding is novel, but is it observed in cells? only one method was used for testing the interactions, not other biophysical methods are used.
4. binding studies with RNA used artificial construct, how about the one with KTGR present like eZiPro. Keep in mind that the P1-P4 residues are present under native conditions.
5. authors built up nice models, it is great to consider the full length NS2B, but authors haven't taken into account the effect of NS2B on the open or closed conformation of the protease.

Significance

This manuscript shows the novel function of zika protease and conclude that protease binds to RNA. This is a novel finding, but the conclusion needs to be further confirmed, to avoid misinterpretations by future readers

It is great to introduce the conformational changes of a protease through defining open, closed, and super open conformations. But the definition was not carefully compared with current literatures. I am surprised that the two important papers are not cited. It is well known the G4SG4 linker affect the conformation of the protease, it is problematic to introduce the super-open conformation here. Authors need to show super open conformation is present in nature e.g. the model in which full length NS2B and NS3pro. RNA is a charged molecule under some conditions, NS3 also have charged residues, it is important to show whether the binding between RNA-protease is relevant to the function, or is this due to the application of the artificial constructs used in this study. Why so many mutants are used?

Other minors

1. Using a construct close to the native protease, at least the P1-P4 residues should be present. Using a peptide in the assay is also useful.
2. Test binding of RNA with protease using another method such as biophysical methods, or even gel shift assay
3. I don't know the correlation between Figure 7 and Figure 6. The authors describe ploy A binding to protease, while Figure 7 is talking about Helicase binds to dsRNAs.
4. I am glad to see the consideration of full length NS2B, NS3 in the models Figure 8, 9 and 11, but there is no data to support any of the model proposed.
5. Is the linker a ploy G not G4SG4?
6. Do the mutant sustain their protease activity?

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Referee #3

Evidence, reproducibility and clarity

The authors ask the important question whether post-embryonic organ formation follows the same mechanisms as during embryonic development. They focus on neuromasts of the lateral line system in the caudal fin of medaka. They used live imaging to find that the post-embryonic caudal-neuromast-cluster develops from organ-founder neural stem cells as a bud (and not as individual migrating stem cells as in zebrafish) that detaches and migrates from the founding neuromast (P0). They show that the formation of post-embryonic neuromasts does not require the lateral line nerve, which establishes another difference to the process in zebrafish. Artificial reduction in Cxcr4b chemokine signalling slows down stem cell delamination, which invariably occurs at the anterior aspect of the P0-neuromast. They then show (via changes in cadherin-type gene expression and cellular imaging) that stem cell delamination from the P0 neuromast involves an epithelial-to-mesenchymal transition. Forcing this process in the entire neuromast accelerates new organ formation, but directionality is maintained. Finally they ask whether the stem cells required for this process are pre-specified or are generated from the neuromast by ablating the pre-bud stem cells. They find that other stem cells within the same organ rearrange and re-establish organ founder cells. The authors liken this new mechanism of organ formation to pathological metastases in humans and name it metastatic-like organogenesis.

Major comments

• In Fig. 2D both P0- and PE1-neuromasts appear with fewer hair cells, the reasons for this should be explained. Did the ablation also damage the primordium or is the pLL nerve required for complete neuromasts to form?
• p. 6: The reasoning behind generating a cxcr4b l-o-f mutant does not become clear, since a mutant already existed with a non-migratory primordium. Why did the authors expect their mutant would have a different phenotype?
• p. 7: The authors state that K15::cxcr7 larvae lack secondary embryonic neuromasts, but it seems from Figs. 3B,D that they might simply be delayed (note that the last one is missing in 3B). This delay may have been taken over from the delay in embryonic primordium formation of P0 and this result (as shown in Fig. 3) would not contradict the assumption that PE1 can form in the absence of cxcr4b signalling. I suggest that the authors actually show and quantify that K15::cxcr7 adults have fewer CNC neuromast numbers, because this seems to be the definitive proof that overexpressing the "sink" may be enough to reduce cxcr4b signaling to a level where its requirement for the formation of the PE1-neuromast can be assayed.
• Fig. 6A': The scheme is at least ambiguous and interpretation of it requires more supporting information: In A the stippled lines represent position within the neuromast, but what do they represent in A', numbers of BrdU+ cells? So what does e.g. the grey peak at the anterior mean - position or number of cells? Is the area inside the coloured lines important or the edge-points? Stage III is the only distribution with a clear left-bias, the others are centered (with a left-extreme for stage II), so what in the figure is the anterior proliferation peak? These are just some questions this reviewer had. Maybe the problem lies in the octagonal lines, meaning different things in both images? It is further unclear how the means given in the text can be derived from the figure. Maybe it would be best to try to represent the data with a heat map-overlay of the image in A, one for each stage?
• The authors propose two competing models regarding the origin of founder stem cells (p. 9, first sentence: early determination vs. in situ generation). In the third sentence again two scenarios are presented as to why experimentally prompting EMT does not trigger organ founder cell migration. This paragraph would benefit from stating more precisely which of these questions is addressed by the BrdU- and ablation experiments, together with a clearer statement at the end of that section as to which hypothesis in each case (origin and migration) is preferred.

Minor comments

• K15+ cells are described as neuromast stem cells and Fig. 1 suggests that these are the mantle cells: Please comment on the question whether all mantle cells are stem cells.
• p. 5: The reference (Seleit, Krämer et al., 2017) is ambiguous, as there are 2 references listed that fit the abbreviation.
• Fig.1B-F': Even though, as the authors state, there is variation in the timing of the budding process, it would be helpful to add an exemplay time frame to stages I-V.
• Fig. 4A'-D': The cell bodies of the support cells should have a distinct colour, otherwise they are easily confused with the nuclei of the other cell types. This would make it easier to understand the schematic at first sight.
• p. 9: T2A and H2A should be explained.
• Nuclei are shown protruding posteriorly in wildtype neuromasts (Fig. 5A-A'), while P0 neuromasts stem cells protrude anteriorly. Please explain the significance of the difference.
• Fig. 5 legend: Quantification is "E"; "and increased" should probably read "an increased"?
• p. 10: Unconventionally, Fig 7 is mentioned prior to Fig. 6B-C, I suggest combining both figures into one.

Significance

The manuscript describes a new mechanism of post-embryonic organ formation. Investigating how accesory neuromasts are formed during growth of juvenile medaka, the authors find that stem cells from a founder neuromast undergo epithelial-mesenchymal transition and migrate away directionally to form a complete new organ. This new mechanism is likened to that of cancer metastases.

Importantly, and different from zebrafish, this process is not dependent on innervation of the neuromast and is not a budding process, but relies on neural stem cells leaving the organ.

The interesting question posed by the authors, and answered here positively for accessory neuromasts in juvenile fish, is whether the mechanisms of organ formation differ between embryonic and post-embryonic development. The reported findings should be of interest to the stem cell communities and to researchers interested in post-embryonic development.

This review was written by a developmental biologist.

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Referee #2

Evidence, reproducibility and clarity

Authors study how new sensory organs of the lateral line form post-embryonically in medaka fish.

Evidence, reproducibility, and clarity

Overall, I find the study very preliminary, since hardly any conclusions are sufficiently backed by quantifications and statistical analysis as detailed below.

Major comments:

Figure 1: Authors describe events as "detached cells migrate" in the results text and in the legend as "detached stem cells...move". They should clarify how these images were exactly generated, since this has implication on whether they can conclude that cells migrate. Are these frames from movies in which the entire process was seen to occur in individual larvae? Are they derived from repeated imaging of the same larvae? Or are they images from different larvae and authors assume that the sequence of events occurs as presented? While it's likely that cell migration occurs, a wave of de novo transgene expression could also travel through the tissue. Thus, authors can only conclude that it's migration if they have seen cells move relative to their surroundings using live imaging or via lineage-tracing. e.g. using a photoconvertible fluorophore.

Page 5: "The process of post-embryonic neuromast formation in the CNC displays variability in timing". Authors should add information on the actual timing. This relates to issue 1, maybe they don't know, but if they did live imaging or repeated imaging of the same larvae they should have information on how long it takes from delamination of cells to new neuromast formation.

Figure 2A: where is the data showing that the laser ablation actually worked and supporting the statement "All ablated fish showed escaping cells from the P0-neuromast (N=7/7 fish)"?

Figure 2B-D: I find it difficult to see how these data support the conclusions the authors draw. First of all, it would be helpful to show the structures labeled by the individual transgenes for the non-initiated readers, so readers can judge themselves which of the signals are derived from the kremen and which from the eya1 transgene. Second, in B' readers are supposed to "Notice the uninjured primordium that continued migration and embryonic neuromast formation", yet where is the uninjured primordium? There are a lot of signals in the image. And how do we know that it "continued migration?" Relative to what? Finally in D, the label "PE1 neuromast" is printed in between a structure that is weakly and one that is strongly labeled. Do the authors suggest that there are 2 PE1 neuromasts here? Both the P0 and the P1 neuromast(s?) on the experimental side seem to be much smaller that on the control side, but authors do not mention this. Does this show that neuron proliferation or differentiation are nerve dependent?

Cxcr4 mutant: it's unclear why the authors mention the new mutant, albeit they don't use it. The only reason to justify this would be if the community were to benefit from this new allele. However, this requires that authors clarify how it differs from the previously existing one (e.g by showing the predicted protein sequence) and whether it has any advantages, e.g. is it more likely to be null? Further, where are the data supporting this statement? "cxcr4bD625 larvae display the same phenotype as the previously published cxcr4b mutants".

Figure 3: authors should validate the k15:cxcr7 line by showing cxcr7 (over) expression in k15+ cells using in situ hybridization.

Figure 3B: how do the authors distinguish single and double transgenics? If they cannot and only assume that those that have a phenotype are the double transgenic they need to confirm this by genotyping embryos post imaging.

Figure 3D: sample size is missing. Significance should be tested.

"Adult Tg(K15::Cxcr7) fish display significantly lower CNC neuromast numbers compared to wild type fish (N= 5 WT fish, 3.8 organs per CNC; N= 4 Tg(K15:Cxcr7), 2.2 organs per CNC". Which statistical test has been used to support the use of the term "significantly" in this statement? Images should be shown to support this conclusion.

Fig. 4C: authors should show YFP and CFP channels to allow readers to see why authors have false-colored 2 cells. What do they mean by the term "repolarization" that they put in the figure label?

Fig. 4D: "Subsequently, the organ-founder stem cells start elongating lamellipodia-like processes in the anterior direction". How do the authors know that this is "subsequently"? These are obviously not frames from a movie, so how do they know that the cells the point their arrow at delaminated from the neuromast considering that there are also quite a few other YFP+ cells in this frame?

Fig. 4C, D: These observations must be supported by a least rudimentary information on reproducibility. How many neuromasts have the authors analyzed? How often did they see this?

Fig. 4F, G: These conclusions must be supported by quantifications and statistics (e.g. E- and N-cadherin staining intensities).

Fig. 5: is the number of neuromasts with protruding cells significantly different between the control and experimental group? % should be rounded to significant figures.

Fig. 5D: these data are not convincing since it is unclear how authors identify the neuromast, considering that almost all cells seem to contain H2B-GFP.

Fig. 5E: is there a significant difference?

Fig. 6A: Exemplatory images of BrdU+ cells should be shown.

Fig. 6A: "This approach revealed a proliferation peak at stage I-II (mean: 6 and 5.4 BrdU+ cells, respectively". This statement does not support that this is a peak in the absence of information on how much proliferation there is at other stages. Why don't the authors show a graph plotting this with variation and statistical analyses to support that the numbers differ at different stages.

Fig.6A: also the conclusion that more proliferation happens in anterior positions must be backed by statistics.

Fig. 6: ablation data. Text mentions that PE1 formed in 7/8 ablated larvae, but images show differences between the control side, where PE1 has not yet formed and the ablated side where it has... Is this a non-representative image? Authors should clarify.

Fig. 7: Supplementary Movie 2 does not work, so I could not review it.

Fig. 7: Conclusions need to be supported by quantification and statistics, it's not sufficient to show only frames from one movie.

Fig. 7: Where is the data supporting this statement "(mean: 0.05 BrdU+ stem cells; N=8 P0-neuromasts)"? How was the BrdU incorporation experiment performed?

This statement needs to be supported by quantifications and statistical analysis: "We noticed that in most cases, the ablated P0-founder neuromast was considerably smaller than the non-ablated founder organ in the contralateral side (Fig.6 B',C)(N=4/7 larvae)"

This statement needs to be supported by quantifications and statistical analysis: The PE1-neuromast, however, reached the regular size in all cases, regardless of the status of the P0-founder neuromast.

Minor:

I think the author pitch the fact that they are examining "organ-founder stem cells" a bit too aggressively. It would be more appropriate to stick to the term "mantle" cells in all figures that describe data and reserve the "organ-founder stem cells" term to text where they interpret their results. It's particularly strange that Fig. 4C is labelled with such an interpretation.

Significance

There are many interesting open questions about post-embryonic development and in particular about how novel structures/organs form in those species where this happens. Thus, the overall research topic of this study is very interesting. The model is also well suited to derive novel mechanistic insight into these questions. The problem with the study in its current form is that I find it quite anecdotal, since hardly any conclusions are sufficiently backed by thorough data, in particular there is a rather shocking lack of quantifications and statistical analyses throughout. However, if the authors back their conclusions with such data, it'll certainly make a very interesting paper.

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Referee #1

Evidence, reproducibility and clarity

Groß and colleagues explore the mechanisms by which post-embryonic organogenesis occurs. To do so, they use medaka caudal fin neuromasts as a model, in which they follow the genesis of a new neuromast, PE1, from an existing neuromast, P0. Previously the group has established that ablation of the P0 neuromast results in the absence of PE1 neuromast formation, and lineage tracing confirmed that the P0 neuromast gives rise to all the neuromasts in the caudal-neuromast-cluster.

To dynamically assess PE1 formation, the authors use a broad lateral line transgene reporter, labeling keratin 15-expressing cells (K15+). Through this method, they observe that anterior K15+ cells of the P0 neuromast detach from the organ, migrate anteriorly, and give rise to the PE1 neuromast. By ablating the posterior lateral line (pLL) nerve prior to PE1 formation, which innervates the P0 neuromast initially, the authors report that the pLL is not necessary for proper PE1 formation, as it still develops in the absence of this nerve. Further, the authors explore chemokine signals which may underlie this process. The authors discuss a previous finding that the Cxcr4b/Cxcr7/Cxcl12a signaling pathway has been shown to regulate primordium migration, which is an organ required for neuromast formation. Therefore, the authors modulated the signaling pathway by first generating a missense cxcr4b mutant, only to find that this resulted in the absence of P0 formation. To circumvent this issue, the authors instead overexpressed Cxcr7, a non-signaling receptor that competes with Cxcr4b for the Cxcl12a ligand, in K15+ cells. Results from these experiments displayed a role for the Cxcr4b/Cxcr7/Cxcl12a signaling pathway in the temporal regulation of post embryonic neuromast formation. At the developmental time that wild type fish develop post embryonic neuromasts, Tg(K15:Cxcr7) animals have reduced numbers of post embryonic neuromasts. However, the authors find that post embryonic neuromasts do form in these animals at a later stage of development. Finally, the authors show throughout the report that the organ founder stem cells, which go on to form the PE1 neuromast, arise exclusively from the anterior side of the P0 neuromast. They questioned whether some cells were pre-specified to become organ-founder stem cells or if all stem cells have the same capacity to generate a new organ. To understand this, the authors used laser ablation on the anterior side of the P0 neuromast and found that the neuromast cells were capable of rearranging and initiating migration from the anterior side.

In all, this report highlights a potentially novel cellular mechanism by which a post embryonic neuromast is generated from a pre-established neuromast. By using longitudinal imaging, the authors were able to observe this process in developing animals and begin to probe its molecular mechanism. Several aspects of the manuscript should be strengthened prior to publication to more rigorously support the authors' model.

Major Comments:

A key aspect of the current manuscript is whether the morphogenetic process that they report is fundamentally different from the "budding" mechanism previously observed in zebrafish during neuromast stitch formation (Wada et al., 2010; Wada et al., 2013) or simply represents a different description of an analogous process in medaka. Inspection of the previous work in zebrafish reveals several similarities at the cellular level that leave this reviewer unconvinced that this is really a different process, rather than differences due to reporters used (membrane and nuclear here vs cytoplasmic previously). Specifically, Figures 2 and 3 in Wada et al., (2010) and Figure 2 in Wada et al., (2013) look quite similar to the morphogenetic process herein. Wada et al., (2013) describe stitch formation as: "a budding process that begins when a few cells elongate away from the founder neuromast". Here, on pg 4 Groß and colleagues describe a process that "is executed by a few organ-founder neural stem cells that detach from their original organ and migrate to generate a new organ remotely." How exactly are these two processes different? One key mechanistic difference is potentially the nerve dependence, but there are concerns with the interpretation of this experiment (see comment below). Unless the authors can definitively demonstrate that what they describe is a distinct process, they might be better served by reframing their results in light of previous findings by Wada and colleagues.

A second important thrust of the paper is that migrating K15+ cells act as "organ founder stem cells." However, the authors do not show conclusive evidence of K15+ cells acting as stem cells during PE1 formation. To support their claim, the authors should more rigorously define the K15+ organ-founder cells as stem cells. This could be done by several approaches (e.g., via lineage tracing, molecular analysis, or live-cell imaging). Importantly, it has previously been shown that zebrafish hair cell regeneration is predominantly driven by surrounding support cell proliferation (reviewed by ​​Lush and Piotrowski, 2014 doi: 10.1002/dvdy.24167). Therefore, it is important for the authors to determine whether their organ-founder cells are in fact stem cells or, alternatively, migrate along with K15- support cells from the P0 neuromast.

The rates of post-embryonic development in teleost fish, including medaka (Iwamatsu et al., 2003 doi: 10.2108/zsj.20.607), depend on several housing conditions (e.g., rearing density and feeding). It was surprising to this reviewer, therefore, that the authors performed all of their staging by days post-fertilization rather than standard length. Results from most experiments, especially those in Figures 1 and 3, would be more easily interpretable (and reproducible across different labs) if authors were to report standard length of the animals being used. For example, are Tg(K15:Cxcr7) animals smaller than their wildtype counterparts? If so, could this explain why PE1 neuromast formation is delayed? This goes for the interpretation of Figure 5E as well.

The authors should include statistical analyses of all their quantification. For example, it would be appropriate to use a statistical test to compare groups in Figures 3D and 5E.

The authors use the transgene Eya1:mCFP to visualize and laser ablate the pLL nerve, stating that Eya1 labels the nerve. However, a few sentences after introducing this transgene, the authors now use the transgene Kremen:mYFP to label the pLL nerve, and in double transgenic Kremen:mYFP; Eya1:mCFP fish, the Eya1 transgene is used to "assess the differentiation state of the putative newly formed PE1 neuromast". In the figure legend, the authors explain that Tg(Eya1:mCFP) labels the pLL in Figure 2A, but in Figure 2B it is used to visualize the primordium. The primordium is not the pLL nerve, and if the Eya1 transgene is labeling the primordium, and not the pLL (the text suggests it fulfills both roles in different scenarios) then the authors should repeat this experiment using the Kremen transgene to appropriately label the pLL nerve for accurate ablation. If, however, the Eya1 transgene labels both the primordium and the pLL (it is hard to tell from the double labeled images, as they are in grayscale), then this should be made explicitly clear.

Consider tempering the interpretation of the pLL nerve ablation experiment. Since the neurons and associated Schwann cells are still present following the severing of the nerve, albeit at a distance, could the nerve not still signal via a diffusible paracrine molecule? Alternatively, the authors could ablate the pLL ganglion. Since pLL ablation is performed 18 days prior to imaging, it may be possible that there is nerve regeneration occurring. To make the authors' findings more convincing, use of a secondary reporter, or antibody staining with a pan-neuronal antibody to confirm the absence of neuromast innervation at 21 dpf should be considered. Additionally, in Wada et al., (2013), neuromasts still extend cellular processes after nerve ablation. Since Wada et al. uses a membrane reporter, and here we see the use of a nuclear reporter, is it possible that we are seeing the same results as Wada et al.? To enhance the strength of this figure, authors should also consider using a membrane reporter or performing IHC similar to that in Figure 4D, so that readers can visualize there is no cellular process connecting the P0 and PE1 neuromasts in this condition.

Supplemental Figure 1 is a colorimetric in-situ hybridization image which depicts the localization of cxcl12 transcripts. The authors state that there is transcript expression in the vicinity of the P0 neuromast, however, the image is of poor quality and the expression does not appear spatially restricted to the anterior portion of the neuromast. Consider either discussing how a uniformly localized chemokine cue fits with their model and/or providing more detailed evidence of the expression pattern, e.g., by co-staining with a neuromast-specific marker and performing high-resolution imaging. Ideally the authors could quantify cxcl12 expression relative to the A/P axes of the P0 neuromast.

In Figure 4, the authors provide evidence that: 1) K15+ cells in the anterior of the P0 neuromast change shape and extend invasive, lamellipodia-like protrusions, and 2) that a cluster of cells to the anterior of the P0 neuromast show decreased E-cadherin and increased N-cadherin staining. These results are consistent with a subset of K15+ cells undergoing a MET. However, the authors could strengthen this portion of the manuscript in several ways. First, is it possible to live-image delamination from the neuromast? This would provide unambiguous evidence in support of their model. Second, is it possible to combine E- and N-cadherin staining with visualization of the K15+ population? The authors state that "N-cadherin is clearly upregulated in migrating organ-founder stem cells", but at the moment the evidence is circumstantial that K15+ cells switch cadherin expression. Co-visualization of the K15+ population would strengthen this point. Ideally, the authors could quantify E- and N-cadherin levels in K15+ cells relative to neighboring cells to support their claim. Minor point: have the E- and N-cadherin antibodies previously been validated in medaka? If so, the authors should cite the relevant work. If not, the authors should provide evidence of antibody specificity.

In Figure 5, the authors use Tg(K15:snail1b-T2A-H2A-mCherry) to address whether snail1b expression is sufficient to drive ectopic exit of cells from the P0 neuromast. The argument that snail1b is functional is an increase in neuromasts with protruding cells, but it is not demonstrated that any cells actually undergo EMT. A simple explanation for the observed lack of ectopic delamination is that snail1b is not expressed at sufficient levels from the transgene. With the current data, this reviewer would suggest tempering the claims related to interpretation of this experiment. On a related point, is snail1b normally expressed in delaminating cells? If so, this would provide further evidence to support the authors' EMT model in Figure 4. Minor point: the authors state that "not a single case of ectopic cell migration was observed when we analyzed the P0-neuromast by live imaging" - please clarify: what was the imaging time window and at what stage was the imaging performed?

Minor Comments:

Abstract, first sentence. This sentence is confusing since mammalian organs certainly grow at post-embryonic stages.

On page 6 of the manuscript, in the "pLL nerve is dispensable for organ-founder stem cell migration and PE1-neuromast formation" section, the authors describe the transgenic animals used in their pLL ablation studies as, "double Tg(Eya1:mCFP) - to label the pLL nerve - (K15:H2B-RFP) - to visualize migrating neuromast stem cells". The phrasing of the transgenic description is cluttered and confusing to read. Authors should consider rewriting this description as something such as, "double Tg(Eya1:mCFP); (K15:H2B-RFP) animals were used to visualize the pLL nerve as well as migrating neuromast stem cells, respectively".

On page 6 of the manuscript, in the "pLL nerve is dispensable for organ-founder stem cell migration and PE1-neuromast formation" section, the authors use the term escaping point. This is the first and only time the term is used, and it is not well defined. Presumably this refers to the anterior side of the P0 neuromast. This should be rewritten to more clearly articulate the meaning of this term.

Could the authors refer the reader to Figure 1A in the corresponding section of the introduction? It might also be helpful to the reader to label the primary vs secondary neuromasts on the schematic diagram.

In figure 2, the authors conclude that PE1 neuromast formation is not hindered by pLL ablation, however, in Figure 2C and D, it is apparent that the resulting PE1 neuromast post-pLL ablation is significantly smaller in size. The authors should address this, especially since they refer to the new PE1 neuromast in this condition as "mature". Is an organ mature if it is substantially smaller than in control conditions? Are the other resident cell types present in the proper proportions? Does the size of this organ grow to become wild-type further along in development?

On page 6, in the results section for Figure 2C and D, Eya1:GFP is being used to visualize "post-mitotic neurons" in the P0 and PE1 neuromasts, however, Figures 2C and 2D look more representative of the K15 reporter. Also this reviewer is not aware of post-mitotic neurons within neuromasts. The corresponding figure legend states that Tg(Eya1:EGFP) labels neuromast hair cells. Could the authors please clarify what is being labeled?

"Although specific for neural stem cells in the mature neuromast, the K15 promoter drives expression at earlier stages, after primary neuromasts were deposited by the primordium". This statement leads to confusion about the specificity of the K15 promoter, indicating it may be more broadly expressed than the authors state. The K15 promoter should be more rigorously described in the text, and evidence for its specificity should be clearly cited/provided.

The last sentence of the first paragraph of the Discussion is unnecessary and possibly overstating the findings within the report, as no evidence for "hijacking" of this post embryonic neuromast formation process was assayed.

The authors might consider discussing similarities and differences between their work and anchor cell invasion in C. elegans, which also involves post-embryonic organ remodeling by an invasive cellular behavior.

Methods transgene construction - please provide concentrations of nucleotides and proteins injected.

Methods Live-imaging section - "tranquilized" should probably read "anesthetized". More details on the imaging are needed. e.g., at what temperature was the imaging performed? What objective(s) was used?

Methods BrdU section - how were animals fixed? Please also describe the antigen retrieval step in detail.

It would be helpful for the supplemental movies to have labels for the transgenes, axes, and timestamps (as appropriate).

Supplemental Movie 2 shows significant xy movement between timepoints. Perhaps registration of the timepoints would help eliminate this and make the movie easier to interpret?

Significance

Groß and colleagues present an intriguing new model for post-embryonic morphogenesis of neuromasts in medaka. However, in its current state it is unclear whether these findings truly represent a new model for organ morphogenesis, rather than an alternative description of a previously described process. If it is the latter, the manuscript still has new cellular and molecular insights, but should be reframed. This work is likely to appeal to basic scientists, e.g., developmental biologists interested in organogenesis and neurobiologists interested in cell-cell interactions. This reviewer has expertise in teleost development and organogenesis.

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Reply to the reviewers

Dear Editor and reviewers,

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

1. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

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

Thank you very much for the positive assessment.

I have some comments to improve a few details:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Evidence, reproducibility and clarity):

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Significance):

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

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

Reviewer #3 (Evidence, reproducibility and clarity):

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Specific comments on single gene phylogenies:

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

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

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

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

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

Supplementary file 1: Accession numbers were added.

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

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

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

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

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

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

This part has been removed while streamlining the manuscript.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

We clarified this in the Results

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

And Material and Methods

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

• Line 911: How many sequences were collected?

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

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

Major comments:

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

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

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

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

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

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

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

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

The method used in the paper varies between the different parts of the paper. One example is single gene phylogenies, which are described three times in the method section [Lines 959-973, lines 1011-1034, lines 1093-1101], in addition to the automated approach within the LGT detection pipeline lines 923-926]. The approaches are slightly different with, for example, different procedures for trimming. This makes it difficult to know how the different presented analyses were done in detail. No rationale for using different approaches is given. At the least, it should be clear in the method section which approach was used for which analysis. Specific comments on single gene phylogenies: - Line 966-967: Why max 10 target sequences? - Lines 996-998: Is it a problem that these are rather old datasets?

Minor comments:

I appreciate that many data is included as supplementary material. However, the organisation of the data could be improved. The numbering of the files is not included in their names or within the files, as far as I could find. Descriptions of the files are often missing and information on the annotation such as colour coding is not always included. These aspects of the supplementary material needs to be strengthened in order to make it more useful. Specific comments: - Supplementary file 1, Table 1: accession numbers are missing. Kipferlia bialta appears to have a much smaller number of sequences than reported in the publication. The file consists of three tables and it would be very helpful if the reference in the main manuscript indicate the table number. - Supplementary file 4: The trees lack proper species names and a documented colour coding. There are multiple trees in the file, which make it difficult to find the correct tree. I would appreciate if the different trees were labelled A, B, C, etc., and if these were used in the main text. - There is no HPAD-AE tree (as indicated on line 258), but a HPAD tree. Which part of the tree contain the described fusion protein? - Line 280-281: "UbiE homologs occur also in some additional metamonads, including the oxymonad B. nauphoetae and certain fornicates." These sequences should be clearly highlighted in the tree. - Lines 538-544: A three-gene system is mentioned, but only two AmmoMemoRadiSam trees are found. - Supplementary file 6: I find it difficult to find the proteins discussed in the text, for example "the biosynthesis of p-cresol from tyrosine (line 254-255)". - Supplementary file 11: Which group of species are highlighted in red? How do I know from which species these sequences are (I can make educated guesses, but prefer full species names). I do not find any reference to this file in the main manuscript.

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

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

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

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

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

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

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

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

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

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

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

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

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

Lines 894-957: "Detection of lateral gene transfer candidates": - It is not clear which sequences were tested in the procedure. All Preaxostyla, or all metamonada? I think I am confused because in the result sections you only report numbers for Preaxostyla, but in the method section metamonada is mentioned repeatedly. - It would be easier to follow the procedure if numbers are provided for the different steps. - Why was only small oxymonad proteins discarded (line 900)? - Line 911: How many sequences were collected? - Lines 916-919: What is the difference between the protein superfamilies (line 916) and the OGs (line 919)? Are the OGs the same orthogroups that is described earlier in the method section? How are the redundancy of NCBI nr entries retrieved in different searches dealt with?

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

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

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

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

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

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

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

** Referees cross-commenting**

I agree with the other reviewers that the discussion of the functional and ecological implications of the LGTs could be developed.

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

Significance

The findings presented in this manuscript can be divided into two parts: the mitochondrial loss and the metabolic and Golgi analyses. The latter is a substantial contribution to the knowledge of metabolic adaptation in unicellular eukaryotes where it builds on previous similar works in other organismal groups. These findings should be of general interest for the protist field.

The loss of mitochondria in M. exilis has been reported by the authors in several previous publications (Karnkowska, et al. (2016, 2019), Treitli, et al. (2021)). Here they show that a distantly related oxymonad (B. nauphoetae) also lack all signs of the mitochondria, suggesting that all oxymonads might have lost the mitochondrion completely. This shows that M. elixis is not a weird lineage, which recently lost the organelle and therefore is on a fast evolutionary dead end. Rather, a whole group of microbial eukaryotes have lived for long evolutionary times without any organelle with mitochondrial ancestry.

This shows that eukaryotes can be successful without any kind of mitochondrial organelle. Such a conclusion should be of interest to a wide audience.

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Referee #2

Evidence, reproducibility and clarity

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

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

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

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

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

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

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

Some more thoughts:

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

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

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

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

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

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

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

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

** Referees cross-commenting**

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

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

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

Significance

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

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Referee #1

Evidence, reproducibility and clarity

This is a very interesting paper that investigates through detailed comparative genomics the tempo and mode of the evolution of microbial eukaryotes/protists members of the Metamonada with a focus on Preaxostyla, currently the only known lineage among eukaryotes to have species that have lost, by all accounts, the mitochondria organelle all together. Notably, it includes a free-living representative of the lineage allowing potential interesting comparison between lifestyles among the Preaxostyla. This is a generally nicely crafted manuscript that presents well supported conclusions based on good quality genome sequence assemblies and careful annotations. The manuscript presents in particular (i) additional evidence for the common role of LGT from various bacterial sources into eukaryotic lineages and (ii) more details on the transition from a free-living lifestyle to an endobiotic one and (iii) the related evolution of MROs and associated metabolism. I have some comments to improve a few details: In the introduction, lines 42-43, the last sentence should be more conservative by replacing "whole Oxymonadida" with "...all known/investigated Oxymonadida". Similarly on line 62, the sentence could state "... contain 140 described...". When discussing the estimated completeness of the genome are discussed (lines 117-120) and contrasted with the values for Trypanosoma brucei and other genomes, the author should explicitly state that these genomes are considered complete, which seems is what they imply, is that the case? If so, please provide more details to support this idea. The supplementary file named "132671_0_supp_2540708_rmsn23" is listed as a Table SX? (note: I found it rather difficult to establish exactly what file corresponds to what document referred in the main text) Lines 243-245, where 46 LGTs are discussed, it is relevant that the authors investigate their functional annotations. Indeed, it is suggested that these could have adaptive values, hence investigating their functional annotation will allow the authors to comment on this possibility in more details and precision. When discussing LGTs it would also be very useful to cite relevant reviews on the topic - covering their origins, functional relevance when known, distribution among eukaryotes. This is done when discussing the evolution and characteristics of MROs but not when discussing LGTs, with several reviews cited and integrated in the discussion of the data and their interpretation. The sentence, lines 263-265, where the distribution of some LGTs are discussed, needs to be made more precise. When using the work "close" the authors presumably refer to shared/similar habitat,s or else? Entamoeba is not a close relative to the other listed taxa. Lines 346-348, that sentence needs to end with a citation (e.g. Carlton et al. 2007). In the paragraph (line 580-585) discussing ATP transporters, note that Major et al. (2017) did not describes NTTs but distantly related members of MSF transporter, shared across a broader range of organisms then the NTTs. Did the authors checked if the genome of interest encoded homologues of these transporters too? Line 920-921, I don't understand how the number 30 relates to "guarantee" inferring the directionality of LGTs events. This will be very much dataset dependent, 100 sequences might still not allow to infer directionality of LGT events. The authors probably meant to "increase the possibility to infer directionality".

Significance

This is a very interesting paper that investigates through detailed comparative genomics the tempo and mode of the evolution of microbial eukaryotes/protists members of the Metamonada with a focus on Preaxostyla, currently the only known lineage among eukaryotes to have species that have lost, by all accounts, the mitochondria organelle all together. Notably, it includes a free-living representative of the lineage allowing potential interesting comparison between lifestyles among the Preaxostyla. This is a generally nicely crafted manuscript that presents well supported conclusions based on good quality genome sequence assemblies and careful annotations.

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Reply to the reviewers

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

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

Reviewer #1 (Significance (Required)):

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

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

*

Responses:

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

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

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

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

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

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

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

Responses:

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

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

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

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

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

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

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

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

Response:

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

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

Response:

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

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

Responses:

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

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

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

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

Response:

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

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

Responses:

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

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

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

Responses:

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

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

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

Response:

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

---

*Reviewer #2 (Significance (Required)):

*

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

*

Response:

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

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

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

*

Response:

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

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

*

Response:

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

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

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

Response:

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

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

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

*

Response:

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

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

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

Response:

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

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

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

Responses:

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

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

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

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

Response:

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

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

Responses:

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

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

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

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

Responses:

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

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

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

Response:

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

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

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

Responses:

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

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

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

Response:

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

*13/ line 218, 243 - reference error *

Response:

Thank you, we have fixed this error

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

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

Response:

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

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

Responses:

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

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

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

Response:

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

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

Responses:

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

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

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

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

Response:

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

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

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

Response:

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

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

Responses:

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

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

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

Lack of consistency in conclusion. *

Response:

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

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

Response:

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

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

Response:

Thank you, we changed the phrasing accordingly.

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Referee #2

Evidence, reproducibility and clarity

The study presented the role of cytolic fungal toxin - candidalysin, secreted by the hyphal form of Candida albicans, in the formation of neutrophil extracellular traps during C. albicans contact with neutrophils, which serve as the first line of the responses. The key conclusions are convincing. The authors considered the whole mechanism of NLT formation, which explained previous observations made by others. Some of the additional proposed experiments are not necessary to perform. They would only complement the results already presented by the authors. A few missing citations in the text need to be filled in. The others have been used appropriately and present earlier work on the subject. The reviewer indicated minor corrections to the drawings in the detailed comments. This paper is very interesting and is crucial to understanding some unusual observations made earlier about NET production in fungal infections. On the other hand, the text requires minor corrections to understand better the occurrence of both forms of extracellular neutrophil traps. The authors of the paper have experience in the subject matter presented, and the lead authors are among the leading researchers who analyze this problem. The presented research is a valuable addition to the previous work.

Significance

The advantage of this work is the presentation of the mechanism associated with NLS formation in contact with candidalysin, where activation of NADPH oxidase and calcium influx have been documented to be important. This toxin can trigger ROS production and activate downstream signaling that is important for morphological changes and NLS formation. The important finding is also that NLS are resistant to nuclease treatment and increase the ability of neutrophils to control C. albicans hyphae formation and fungal cell growth. These findings provide a better understanding of the role of neutrophils in the treatment of infections caused by these microorganisms.

Below I present are minor suggestions that, in my opinion, will improve the text and correct the presentation of the results, making this set of results a valuable source for explaining such a complex problem.

1. The authors should decide what thesis about NLS they want to prove: 100 NLS are less fibrous and ....... than canonical NETs and are triggered in an NADPH oxidase-independent fashion. 121 NLS were dependent on NADPH oxidase-mediated reactive oxygen species (ROS) production
2. for the experiment described in the line below, MOI 2 was chosen; did the authors conduct an analysis of the response/eventual change in it, depending on the MOI?

131 we infected neutrophils with wild-type C. albicans, ECE1-deficient (ece1ΔΔ), and corresponding revertant (ece1ΔΔ+ECE1) strains, 3. Has the effect of deletion of ECE1 on other aspects of virulence, such as adhesion, virulence factor production, or biofilm formation, been analyzed?

137 the ECE1- and candidalysin-deficient strains triggered reduced levels 4. Fig.1 - How were C. albicans cells stained? Does 100%NET mean the number of cells netting after PMA treatment? This information should be given. 5. 168 dependent effect with increased NLS formation from 3 μM to 15 μM. However, the reduced NLS

How was determined the limiting concentration value of the toxin, for which an increase in NLS was observed? Was a wide range of concentrations used in the analysis or was the determination made only for these three selected values? A complete concentration analysis should be performed. 6. 169 formation was observed at 70 μM (Fig. 2b), which can be explained by neutrophil cell death induced by the toxin as determined by a DNA Sytox Green assay (Fig. S1a).

Was another viability test conducted? AnnexinV? Caspase 3/7? Sytox is not a specific staining in this regard. Furthermore, in Fig. S1a you state the kinetics of cell death, also after PMA treatment. On the one hand, you say that the production of candidalysin of NLS above 70 uM is reduced due to cell death, but at the same time you define as cell death the changes under PMA, which induce netosis. Please explain this reasoning better. 7. 175 mixing of granular and nuclear components at ~120 min after stimulation (Fig. 2d and Fig. S2).

Figure S2 does not show mixing with the content of the granules. You are not labeling any granule component, only histones. You cannot draw that conclusion from these results. 8. Fig. 2. What concentration of PMA was used? What does 100% NLS mean? How is it different from 100% NET, since you are using PMA in both cases. Please explain. 9. 181 NLS were quantified with the same criteria as previous described for NETs.

The criterion for NETs was an area above 100um2, so what is the criterion for NLS? If we assume that this is the same as for NETs, then what is the difference between NLS and NETs? The criteria adopted do not differentiate between the two forms and appear to be subjective. 10. 190 allows a more detailed view of the neutrophil-derived structures (Error! Reference source not Please, eliminate this error. 11. 193 Ionomycin has been previously reported to induce NLS, also... 194 Both, PMA and ionomycin generated widespread chromatin fibers in the extracellular space 197 In addition, C. albicans hyphae induced NETs with observable fibers and 198 threads similar to PMA- and ionomycin-stimulated neutrophils (Fig. 3b). 199 Image-based quantification of NLS events (candidalysin and ionomycin)

In a sentence earlier (193) you mentioned that the action of PMA leads to classical netosis and ionomycin leads to NLS. You pointed out earlier that NLS are poorly developed NETs (line 100), and here you write that PMA and ionomycin generate the same developed structures. You again differentiate between these structures depending on the stimulating factors. Pointing out the differences between the two forms, you should be more precise and consistent in your descriptions. This comment applies to the entire manuscript. 12. 203 NLS after 3 h and 5 h, respectively, and led to overall fewer NLS events. This was confirmed by observation. 204 area-based analysis of the events (Fig. 3d). The average area per event that exceeded 100 μm2 was 205 determined using the images from the DNA stain. What is the accepted criterion for distinguishing between NLS and NETs? 13. line 218, 243 - reference error 14. What form are we actually talking about? Are we focusing on the effect of a natural agent or a synthetic one in relation to NLS/NET? Perhaps it is more important to focus on the citrullination process:

247 synthetic candidalysin only induces NLS, we concluded that candidalysin augments NET release when the toxin is secreted by C. albicans hyphae. 256 This confirmed that candidalysin promotes C. albicans-triggered NET release. 262 Interestingly, the addition of synthetic candidalysin resulted in a shift to NLS, 274 External addition of synthetic candidalysin resulted in a shift to NLS structures rather than NETs as visualized by microscopy after 5 h incubation (20X). 15. Has there been any method to track candidalysin production during contact of C. albicans with neutrophils? 16. In Figure 4f-the given information indicates 1,2 hour incubation, in the caption of the figure there is information about 5 hour incubation - please clarify. The description of the stains used is lacking. 17. Fig. 5 - result for 15 uM MitoTEMPO - adds nothing to the results and introduces image information noise - should be removed. No information on the concentration of the peptide used. 18. Fig. 5, line 309: and cell-permeable Sytox Green DNA dye (250310 nM) to determine the total number of cells".

Please correct the information on the use of both dyes, according to the manufacturer's description: "SYTOX® Green nucleic acid stain is an excellent green-fluorescent nuclear and chromosome counterstain that is impermeant to live cells, making it a useful indicator of dead cells within a population." 19. 324 At later time points, BAPTA-AM led to an increase in NLS, probably due to toxic effects as indicated by higher background levels of NLS formation in non-stimulated, BAPTA-AM-treated neutrophils (Fig. 6d).

If such an assumption is made, the toxic effect should also be observed for the control. 20. Fig. 6C PAD inhibitor should affect PMA-induced netosis, but the figure presents NLS existence - how was this change found? 21. line320 "This indicates that candidalysin most probably causes Ca2+ influx via pore formation and not via direct receptor stimulation" And: line 358. As C.albicans hyphae bind to pathogen recognition receptors (PRRs), activate neutrophils and ultimately promote the release of NETs, we aimed to elucidate whether candidalysin alone leads to the activation of similar pathways in neutrophils. Hence, we stimulated neutrophils with candidalysin in the presence or absence of specific inhibitors for SYK, PI3K, and Akt.

Lack of consistency in conclusion. 22. Fig. 7 It would be good to verify these results with experiments using mutants. Figures 7b, 7c, and 7d can be combined to make the whole drawing clearer. 23. line 603 'The percentage of dead cells was calculated using TritonX-100 lysed neutrophils as 100% control' - maybe use " treated or permeabilized"

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Referee #1

Evidence, reproducibility and clarity

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

Significance

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

Comments:

1. I was a bit confused by what should be the main message of the paper - is it that candidalysin on its own doesn't induce NETosis but only NLS? The answer to this question wasn't well addressed in my opinion, but the paper switches between using live fungi and purified candidalysin so it became confusing at times.
2. If candidalysin on its own only induces NLS - what is the relevance of this for disease? A lot of work has been provided on the pathway driving NLS formation, but it wasn't clear to me why this is important. More in discussion needed or evidence of disease relevance.
3. In Figure 2, it would be helpful to include images of ionomycin-stim neutrophils for comparison of the NLS structures across different stim conditions.
4. Few places where reference manager has failed (see bottom on page 10, line 190 for example)
5. Lines 191-198 - I was confused here by the text. I thought the point was that candidalysin induced NLS similar to ionomycin, but here the point is being made that the two are different? This led me to being confused as to the point of all the comparisons made between ionomycin NLS and candidalysin NLS... this could be made clearer.
6. Could the authors include some unstim neutrophil control images in Fig 3 for the SEM? Can the SEM sample processing affect neutrophil structure in anyway? Feels like an important control although I don't have much experience with SEM personally.
7. I was very intrigued by the experiments where the authors added candidalysin in to neutrophils infected with ece1-null strain. Those experiments showed that candidalysin addition still drove NLS instead of NETosis. Can the authors investigate why this is? Is membrane intercalation different when candidalysin is delivered by hyphae vs added on its own? Could that explain some of the differences they have seen?
8. Is phagocytosis needed for NETosis induction by candidalysin? What happens if you add beads or beta-glucan particles with candidalysin stimulation? Do you get NLS or NETs?
9. Please confirm what the n numbers refer to in the figure legends - are these biological or technical replicates? How many experiments are the representative images representing?

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Reply to the reviewers

1. General Statements

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

2. Description of the planned revisions:

__Reviewer #1: __

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

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

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

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

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

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

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

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

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

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

Minor Comments:

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

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

__Reviewer #2: __

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

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

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

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

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

Minor Comments:

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

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

Reviewer #3:

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

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

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

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

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

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

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

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

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

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

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

__Reviewer #1: __

Minor Comments:

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

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

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

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

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

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

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

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

__Reviewer #3: __

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

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

Minor Comments:

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

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

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

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

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

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

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

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

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

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

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

Reviewer #1:

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

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

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

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

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

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

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.

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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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