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Referee #1

Evidence, reproducibility and clarity

Summary

In this study the authors addressed how Ect2 localization is controlled during polarization and cytokinesis in the one-cell C. elegans embryo. Ect2 is a central regulator of cortical contractility and its spatial and temporal regulation is of uttermost importance. After fertilization, the centrosome induces removal of Ect2 from the posterior plasma membrane. During cytokinesis Ect2 activity is expected to be high at the cell equator and low at the cell poles. Similarly to polarization, the centrosome provides an inhibitory signal during cytokinesis that clears contractile ring components from the cell poles. Whether and how the centrosomes regulate Ect2 localization is not know and investigated in the study.

The authors start by filming endogenously-tagged Ect2 and find that Ect2 localizes asymmetrically, with high anterior and low posterior membrane levels during polarization and cytokinesis. They reveal that the centrosome together with myosin-dependent flows results in asymmetric Ect2 localization. Previous studies had suggested that Air1, clears Ect2 from the posterior during polarization and the authors expand those finding by showing that Air1 function is also required to displace Ect2 from the posterior membrane during cytokinesis. To elucidate if Ect2 displacement is induced by phosphorylation of Ect2 by Air1, the authors investigate the localization of a C-terminal Ect2 fragment containing the membrane binding PH domain. When the predicted Air1 phosphorylation sites are mutated to alanine, the Ect2 fragment still localizes asymmetrically but exhibits increased membrane accumulation.

Finally, they investigate the functional role of Air-1 during furrow ingression. They demonstrate that embryos deficient of Air1 and NOP1 have impaired furrow ingression. Lastly, the authors sought to confirm that there is a direct effect of Air1 on Ect2 function by generating a phosphomimetic point mutation of Ect2 using Crispr. They find that the membrane localization of phosphomimetic Ect2 is reduced and consequently furrow ingression is impaired.

Major comments

It is not convincing that the six putative phosphorylation sites are targeted by the Air1. If Air1 phosphorylation displaces Ect2 from the membrane, a reduction in Ant/Post Ect2 ratio is expected in the phosphodeficient mutants, like after air1 RNAi. However this is not observed for cytokinesis or polarization (Fig. 5D(i); E). This suggests that phosphorylation of those sites is not essential for the asymmetric Ect2 localization.

The authors aim to demonstrate that phosphorylation of the identified sites is important for cytokinesis. For this they investigate contractile ring ingression in the phosphomimetic point mutation. Since ring ingression is slower and fails in nop1 mutant they authors conclude that this demonstrates a functional importance of this site. I am not surprised that embryos ingress slower in this mutant since Ect2 localization to the membrane is reduced. This however does not show that this phosphorylation site is the target of the centrosome signal. Importantly, authors would need to demonstrate that Rho signaling and thus Ect2 activity, is increased at the poles, when phosphodeficient Ect2 is the only Ect2 in the embryo.

The authors use the Aurora A inhibitor MLN8237: It was shown prior (De Groot et al., 2015) that this inhibitor is not highly specific for Aurora A, and that it also inhibits Aurora B. Thus experiments need to be repeated with MK5108 or MK8745. They should also be conducted during polarization. Why does Aurora A inhibition not abolish asymmetry? That would be expected?

There is no statistical analysis of the results in the entire study. For all claims stating a change in Ant/Post Ect2 ratio or Ect2 membrane localization selected time points should be statistically compared: for example the main point of Fig.1 is that Ect2 becomes more asymmetric during anaphase. Thus a statistical analysis of the Ect2 ratio at anaphase onset (t=0s) and eg. t=90 s after anaphase onset should be performed; or Fig. 3A nop-1 mutant Ant/Post Ect2 ratio during polarization: again statistical analysis of control and nop-1 mutant embryos is needed at a particular time point.

The aim of Fig. 2B is to demonstrate that Ect2 localization is independent of microtubules, however they still observe some microtubules with the Cherry-tubulin marker and those are even very close to the membrane and therefore could very well influence Ect2 on the membrane. Therefore I am not convinced that this experiment rules out that microtubules have no role in regulating Ect2 localization.

Throughout the paper the authors should tone down their statement that Air1 breaks symmetry by phosphorylating Ect2, since phosphorylation of Ect2 by Air2 is not shown.

I understand that the establishment of Ect2 asymmetry is important for polarization. However, how does asymmetric Ect2 localization result in more active Ect2 at the cell equator, which is required for the formation of the active RhoA zone? Would we not expect an accumulation of Ect2 at the cell equator, or if that is not the case more active Ect2 at the equator versus the poles?

Minor comments

Can the authors explain why the quantification of Ant/Post Ect2 ratio in control embryos differs in different figures? For example: in Fig. 1D i) a slight increase of Ect2 asymmetry ratio is seen at around 80 s after anaphase onset. In comparison, in Fig. 2C (i) this increase is not obvious. Are those different genetic backgrounds?

One key point of the paper is that myosin-dependent cortical flows amplify Ect2 asymmetry during polarization and cytokinesis. During polarization the data is convincing, however during cytokinesis Ect2 ratio is only slightly decreased after nmy-2 depletion, again is this decrease even significant?

In the introduction: "Centralspindlin both induces relief of ECT-2 auto-inhibition and promotes Ect2 recruitment to the plasma membrane" it should be added 'Equatorial' membrane, since Ect2 membrane binding is, to my knowledge, not compromised in centralspindlin mutants or in Ect2 mutants that cannot bind centralspindlin.

Labels in the figures are often very small eg Fig. 1 ii-v) and difficult to read. In addition it is easier for the reader if the proteins shown in the fluorescent images is also labeled in the figure (eg Fig. 2B add NG-Ect2).

Material and methods it should be mentioned which IPTG concentration was used.

The authors speculate that the Air1 phosphorylation sites in Ect2 PH domain prevent binding to phospholipid due the negative charge. At the same time, the authors propose that the PH domain binds to a more stable protein on the membrane, which is swept along with the cortical flows and they propose anillin could be that additional binding partner. I might miss something, but do the authors suggest Ect2 has two binding partners: anillin and the phospholipids? It would be necessary to explain this better. The authors should test if anillin represents the suggested myosin II dependent Ect2 anchor. For this they should check if Ect2 localization to the membrane is altered upon on anillin RNAi.

The title of fig. 3 does not fit the statement the authors want to make, since the key point is how Ect2 polarization is affected and not membrane localization in general.

In Fig 4A/C. After air1 depletion the authors observe a reduction in Ect2 asymmetry. Why are the centrosomes not marked in the figures? Because they cannot be detected? The authors would also need to show that the mitotic spindle and centrosomes are no altered by air1 RNAi in the zyg9 mutant. Otherwise the observed effect might be indirect.

The authors state that tpxl-1 depletion attenuates Ect2 asymmetry, this is not seen in the quantification ((Fig. 4B(i)). The main phenotype they observe is that Ect2 levels on the membrane increase (Fig. 4 (ii) and (iii). They go on testing the function of tpxl1 by depleting tpxl1 in the zyg9 mutant, where the centrosomes are close to the posterior cortex. Here they see no effect on Ect2 asymmetry. Based on that they conclude that tpxl1 has no role in this process. To me this finding is not surprising since the centrosome is close the cortex in zyg9 mutant embryos. Therefore sufficient amounts of active Air1 could reach the membrane and displace Ect2. Thus an amplification of the inhibitory signal by tpxl1 on astral microtubules might not be required. The authors need to mention this possibility and tone down their statment (also in the discussion) that tpxl1 is not required for this process.

It was shown that the C-terminus of Ect2 is sufficient and the PH domain is required for Ect2 membrane localization in C. elegans (Chan and Nance, 2013; Gomez-Cavazos et al., 2020). Papers should be cited.

The authors find that nmy-2 depletion results in loss of asymmetry for the Ect2 C-term and Ect2 3A fragment during polarization. Why is the same experiment not shown for cytokinesis?

Air1 is targeted to GFP-C-term Ect2 fragment via GFP-binding to determine the influence on GFP-C-term Ect2 localization (Fig. 5F). They state that they see a reduction of Ect2 C-term but not of C-term 3A after targeting. The reader has to compare Fig. 5D with F. Since the differences are not big, they need to compare the Ect2 C-term and Ect2 C-term 3A with and without Air1 targeting in the same graph (plus statistics). Otherwise this statement is not convincing.

In Fig. 6A the authors determine the contribution of air1 to furrowing. For this they deplete air1 in the nop1 mutant. According to previous studies, air1 mutants have a monopolar spindle. How can the authors analyze the function of air1 in cytokinesis when the spindle is monopolar? Did the authors do partial air1 depletion? They authors need to show that there is not major effect on the spindle and centrosome for their conditions. For comparison air1(RNAi) alone has to be included, otherwise the experiment is not conclusive.

Upon air1(RNAi) in the nop1 mutant NMY2 intensity seems decreased and not increased. Can the authors comment on that, since that is opposite of what is expected.

In Fig 6B they introduce a phosphomimetic point mutation in S634 in the endogenous Ect2 locus. It not clear why the authors chose this site out of the six putative sites and why they only chose one and not 3 or 6 sites? This needs some explanation.

In the model (fig. 7) no astral microtubules are shown during pronuclear meeting and metaphase. Astral microtubules are present at this stage and should be added to the schematic.

Significance

The centrosomes inhibit cortical contractility during polarization and cytokinesis in the one-cell C. elegans embryo. Centrosome localized Air1 was proposed to be part of this inhibitory signal, however the phosphorylation target of Air1 is not known. The identification of Ect2 as a phosphorylation target of Air1 would be a great advancement in the field. However, the presented manuscript lacks convincing data that Ect2 is the phosphorylation target of Air1 during polarization and cytokinesis.

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Reply to the reviewers

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

We will provide the point-by-point response when we submit the full revision of our manuscript

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Referee #3

Evidence, reproducibility and clarity

This paper presents an investigation of the mechanisms of how chitin is synthesized in Drosophila by investigating the chitin synthetase Kkv and two proteins related/redundant proteins that are required for chitin production Exp and Reb.

The authors show that synthesis of nascent chitin polymers is separable from the secretion of chitin and that Ex/Reb is specifically required for chitin translocation/secretion. To understand the functions of Exp/Reb, the authors perform structure/function analyses and examine the localization of the proteins. They find that Na-MH2 domain in Exp/Reb is required for chitin translocation, and that a motif the authors name CM2 is required for Exp localization. For Kkv, they show the WGTRE domain is required for ER exit and that a coiled-coiled domain is required for KKV localization and full Kkv activity. By using live imaging and mutations that disrupt membrane trafficking, the authors show that Kkv, which is a transmembrane protein, cycles to the membrane, and like most membrane proteins, is endocytosed and transits through the endocytic system and is returned to the apical surface. Interestingly, despite being dynamically moved around the cell, chitin synthesis produces highly organized extracellular matrixes. Considering that constitutive production of chitin by Kkv everywhere in the cell would create a mess, these results underscore that regulated organized secretion/translocation of chitin is central to generating patterned extracellular matrixes (as the saying goes, "location, location, location"). Consistent with Exp/Reb being important regulators in extracellular matrix patterning, Exp/Reb not only are required for export of chitin, in the absence of Exp/Reb, the pattern of Kkv localization at the apical surface is altered. Unexpectedly however, by using super resolution microscopy the authors show that Kkv and Exp/Reb have complementary rather than matching localizations. Thus, while it is not clear exactly how Exp/Reb are regulating Kkv, they are doing something very interesting.<br /> Overall, this paper will be of broad interest to the cell biology and developmental biology communities, and to the translational community working to develop chitin as a commercial biopolymer. It is also generally clearly written, although I think there are some inaccuracies in the how some points are phrased. The experiments are well done, and subject to the revisions out lined below.

Major concerns:

• A major conclusion of the paper is that Exp/Reb are not required for chitin synthesis. On the most basic level this statement is well supported, because chitin grains are made in the cytoplasm in the Exp/Reb mutants. However, I think the field would be better served with a more nuanced consideration or the role of Reb/Exp. From the data presented, it seems that in the absence of Reb/Exp, the total amount of chitin produced is greatly reduced. I think it would be worth considering Exp/Reb, or the synthesis process in general, as having processivity or duty cycle or quality control such that in the absence of Exp/Reb while Kkv may make short chitin polymers, or occasional long polymers, the major production of chitin doesn't get going without Exp/Reb. Thinking of Reb/Exp as processivity factors in addition to export factors dramatically changes how one thinks of the proteins and the process of chitin synthesis. While these considerations can be handed with some discussion, it would be very interesting to look at the length of the chitin polymers in the Reb/Exp mutants and see if the average chain length is much reduced. This would help distinguish between Exp/Reb reving up the total number of Kkv molecules that produce chitin and Exp/Reb allowing the same number of Kkv molecules to stay active and produce much longer chitin chains. A caveat here is that I have no idea how hard this is to do, so I won't put this at the level of a required revision, but this result would significantly deepen the analysis in the paper.
• In looking that the subcellular localization of the Kkv and Reb in regular and super resolution, the authors I think the authors missed an important, but straight forward way to gain insight into the apparent complementary distribution of Kkv and Exp/Reb. In stage 16 WT embryos, Kkv has a distinct ringed pattern that corresponds to the tanedial ridges (e.g. clearly visible in Fig. 6A and 6G). How those ridges are set up is unclear, although there are some interesting Turing-pattern models out there. One prediction might be that Exp/Reb should be in between the Kkv rings. If so, maybe Exp/Reb are key components of patterning chitin secretion to make this 3D patterned matrix? Alternatively, maybe Exp/Reb act on a smaller length scale and will match the Kkv ring pattern, just not overlapping with Kkv at the very fine scale. These are straightforward experiments and again could provide key insights into the function of Exp/Reb.
• In general, most of the figures do not include WT or a control for comparison. This makes it hard for non-experts to assess what the effect of a mutation or condition is. For example, there are no examples of WT or Df(exp reb) in Figures 1-4. I realize this would increase the number of panels, but the paper would be more accessible if comparisons were within figures instead of comparing between main and supplementary figures and other papers.
• To bolster the case the Exp/Reb directly regulate Kkv distribution, the authors should examine the distribution of Kkv in a catalytically null Kkv mutant, or drugs that block Kkv, or mutations in other genes required for Kkv activity to show that the altered distribution of Kkv in Exp/Reb mutants is a direct consequence of the lack of Exp/Reb rather than in indirect consequence of lack of extracellular chitin, which causes gross perturbations in the trachea. Also, are there differences in the distributions of Kkv in salivary glands with or without the presence of Exp/Reb? If Exp/Reb change the distribution of Kkv in the salivary glands, which normally do not express Kkv and presumably many other components of the chitin ECM system, this would be a powerful argument that there is a direct effect.

Minor concerns.

• Page 5 "These intracellular chitin punctae disappeared from stage 14, when chitin is then deposited extracellularly (Fig 1B')." Fig. 1B' is stage 15 embryos.
• Page 5 "lead to tracheal morphogenetic defects". It would be helpful to the reader if the text or legend told the reader what they were looking for? Broken tubes? Inflated tubes? Variable tubes?
• Fig. 1H. Main text says "co-expression of Kkv and expMH2/rebMH2 did not lead to tracheal morphogenetic defects (Fig 1H, ...". The tracheal dorsal trunk in Fig. 1H does not look WT. The legend does not state the stage, but the DT looks to have an enlarged diameter and it might be too long. Please present measurements on stage 16 trachea to confirm that there is no effect on tracheal morphology.
• Fig. 3E there is a lot of GFP-Kkv that is not in co-localized with the KDEL marker. Can the authors clarify what compartment all the other staining is? ER?
• Section 3.1. The authors imply that the WGTRE domain is specifically required for ER exit. However, an alternative is that absent the WGTRE domain, the protein just does not fold correctly, which would also preclude ER exit, but would be a different problem for the protein to make chitin if it isn't folded.
• Page 15. I disagree with statement "At stage 16, control embryos showed a highly homogeneous apical distribution of Kkv in stripes, corresponding to the taenidial folds, and Kkv vesicles were largely absent (Fig 6G)." In Fig. 6G, the tandeal ring pattern is clearly visible, as are the fusion cells. If Kkv distribution were "highly homogeneous" these structures/pattern would not be visible.
• Page 15. I also disagree with the characterization of the apical Kkv distribution in st 15 embryos. "In control embryos we detected a very uniform and homogenous pattern of apical Kkv (Fig 6I).". To my eye, the pattern is punctate and random for the clumps of stain, with the underlying beginnings of the tanidial pattern starting to be visible. The pattern appears neither uniform nor homogenous.
• P16. The degree of order in the distribution of Kkv is overstated. The authors state that "The results of this analysis, showed that Kkv on the apical membrane, is evenly distributed following a regular pattern (Fig. 6L,L',L',M)." However, given that there is barely a visibly perceptible difference between the actual distribution of Kkv in 6L' and a calculated random distribution in 6L", and that the pattern is neither visibly even or regular, it would be more representative to say something to the effect that the analysis shows there is "underlying order" or "some degree of order" or a "non-random pattern". Visually, the key difference between 6L ' and L" is that there are fewer closely clustered Kkv dots. You could still have an uneven distribution of Kkv that maintains minimum spacing, which is a kind of ordered organization, but not one that would be assumed from the description. It would be helpful if the authors instead of just saying a "regular pattern" also stated the nature of the pattern they observe, i.e. Grid? Stripes? Minimum spacing?
• Discussion. Another model for the role of Exp/Reb could be to bind and neutralize an inhibitor of Kkv activity. This would account complementary distribution of Kkv and Exp/Reb.
• Fig. 6L. what tissue is being analyzed? Presumably trachea, but this should be specified as salivary glands are also mentioned in the legend.
• Fig. 7 C models. I believe that the super resolution data is not accurately accounted for in the models. In both model 1 and model 2, Kkv and Exp/Reb are shown to be in close proximity, but the super resolution data suggests that most Kkv and Exp/Reb are separated hundreds of nanometers. Further, showing Kkv and Exp/Reb as touching was not supported by the coIP experiments, which failed to detect an interaction. It is possible that only a small fraction of Exp/Reb that is in close proximity to Kkv is active, but if so, this should be explicitly mentioned in the models to reconcile the data showing that Kkv and Exp/Reb are mostly not anywhere near each other.
• -Image analysis. Please detail the criteria for "apical" and "basal" regions were the basis for freehand segmentation. What was counted as apical and what was basal?
• Abstract and Introduction: The authors state that "We find that Kkv activity in chitin translocation, but not in polymerization, requires the activity of Exp/Reb, and in particular of its conserved Na-MH2 domain.", but then follow that with the statement that "Furthermore, we find that Kkv and Exp/Reb display a largely complementary pattern at the apical domain, and that Exp/Reb activity regulates the topological distribution of Kkv at the apical membrane." Many readers, will find the use of "furthermore" confusing because they will take furthermore as the about to be described data logically following the previous data, but then run headlong into the fact the Kkv and Exp/Reb show a complementary distribution, which does not obviously follow from Kkv activity requiring Exp/Reb. The authors could clarify this and highlight the interesting, unexpected and exciting nature of their results by replacing "Furthermore" with "Unexpectedly" or "Surprisingly", and emphasizing the important role of Exp/Reb in Kkv organization. Maybe something like: Unexpectedly, we find that although Kkv and Exp/Reb display largely complementary patterns at the apical domain, Exp/Reb activity nonetheless regulates the topological distribution of Kkv at the apical membrane.

Significance

The topic is interesting from the aspect of cell biology in terms of how a long polymer is created intracellularly, secreted and spatially organized to create a sophisticated extracellular matrix. The topic is also of general interest because chitin is central to the body plan of all insects, crustaceans and many other species, and chitin is of increasing interest as a biopolymer that could have extensive commercial uses.

In addition to an informative structure/function analysis of the Kvv and Exp/Reb, the results identify what is, to my knowledge, the first regulator of the spatial organization of chitin sythase in insects and it unexpectedly shows a complementary pattern to the the synthase. This highlights just how little we understand about how complex extracellular matrixes are synthesized.

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Referee #2

Evidence, reproducibility and clarity

This paper deciphers very nicely the genetics and cellular events where and how chitin polymers become synthesized and translocated towards the apical cell membrane for further release into the extracellular space. Altogether this is fundamental work of high significance explaining how chitin is produced and released.

The authors initially detected unusual intracellular chitin by overexpression of the chitin synthase kkv in tracheal cells before regular chitin deposition occurs. In addition, they recognized that the kkv gain of function mediated unusual intracellular chitin vesicles and in later stages in exp/reb mutants. These findings were the starting point of further experiments, suggesting that Kkv synthesizes chitin and that Kkv-mediated chitin deposition requires Exp/Reb activity to translocate and release chitin. Their genetic studies further show that chitin polymerization and translocation are uncoupled.

All primary studies were tested in embryonic tracheal cells and as a proof of principle control in salivary glands which do not express chitin. Elegant rescue experiments in the mutant background showed that the Exp/Reb Nα-MH2 domains are required but not sufficient for chitin translocation and deposition and are dispensable for protein localization. Additionally, they identified another conserved domain (CM2) which is required Exp/Reb localization but not for chitin translocation. Similarly, they investigated Kkv domains by rescue experiments in kkv mutant embryos. They identified the WGTRE domain as essential for ER exit and the coiled-coil region for proper apical Kkv localization. Altogether they provide evidence that Kkv requires proper localization at the apical membrane, which is likely coordinated by Exp/Reb. This precise Kkv localization is linked with Kkv activity and chitin deposition. Therefore, this work is new and fundamental to many disciplines such as insect biology, chitin biology, cell & developmental biology, and others. Thus, the work is worth publishing but requires some changes from my point of view.

Major Comments

1. The authors nicely show that Kkv is able to synthesize chitin in a constitutive manner and that it can accumulate intracellularly. However, this needs some more input to understand the underlying biological sense. For example, what are the chitin vesicles' nature of early vesicles (st 13) and the unusual late (st15) chitin vesicles? Exocytosis, endocytosis or recycling? This can be clarified to understand chitin translocation and that synthesis and translocation are uncoupled. The authors tested rab5DN mutant salivary glands to exclude endocytosis. However, the chitin-positive vesicle size and amount in the rab5 mutant appear different from the control experiment, where much more intracellular chitin accumulates. Thus, it may suggest that some chitin vesicles are independent of Rab5-mediated endocytosis, others probably not. Indeed, the authors identified some KKv and some other chitin vesicles in all discussed intracellular processes; however, additionally, chitin appears to accumulate also in the cytoplasm. The authors conclude that Kkv protein might be able to polymerize chitin at all different intercellular stages, including endocytosis and degradation pathway. First, I wonder why chitin was found within membranous vesicles and, at the same time, within the cytoplasm. Second, does it make sense in the biological context when tracheal cells or other chitin-producing organs want to secrete chitin at the apical membrane while Kkv has the ability to produce chitin in all cellular areas, even in endosomes? In this context, another fundamental question concerning chitin secretion and subsequent organization could be investigated with the author's tools. Are the chitin vesicles loaded with chitin binding proteins or deacetylases that organize the formation of the nano and makro fibrillar chitin matrix in tracheal tubes? For example, previous research showed a reduced luminal accumulation of the 2A12 antigen in kkv mutants and expRNAi knockdown embryos.
2. Observation of Extracellular kkv-GFP: does extracellular anti-GFP staining co-localize with the anti-Kkv antibody?
3. Putative Kkv microvesicles: the authors state that extracellular GFP staining could be Kkv located in microvesicles. I wonder whether the observed extracellular GFP puncta contain a membrane or other membranous proteins.
4. Fig.1:
5. general remarks: some images of this figure could be improved by showing the single channels of CBP to judge whether chitin is secreted and/or vesicles appear. -In addition, some images show higher magnifications, others overview only. It would be beneficial to visualize the small vesicles additionally with higher magnifications.
6. Fig.1M: This image is problematic due to the epidermal background staining. The tracheal system is hard to recognize. A single channel of Cbp ist not indicated.
7. Fig. 1P: Apical membrane marker or any cytoplasmic marker would be extremely useful to judge subcellular Exp localization in this experiment - this image is hard to compare with Exp localization in Fig S2D.

Fig. 2O: Apical/Basal accumulation, what are the numbers at the Y-axis?

Fig. 3F: The authors state that the WGTRE domain is required for ER exit of Kkv based on colocalization studies with KDEL and FK2. However, the study with FK2 is not convincing as immunostainings are of poor quality. The GFP construct appears not to be expressed in all tracheal cells, and moreover, the FK2 staining is faint. Thus, judging whether the protein is not ubiquitinated from the presented image is challenging. However, it does not change the key message, Kkv does not exit ER. By the way, there is a new paper showing Serca to be essential for ER exit of Kkv, which would fit the discussion of the kkv domains.

Fig. 7 - model: First, Since the authors do not show that Kkv is part of a membranous microvesicle, I'm skeptical whether this should be part of a model that explains the shown data. Therefore, I'm asking the authors to delete it or to show it more clearly. Second, the meaning of the yellow arrowheads is not indicated. Third, the explanation in the legend is sound, but showing the two options could be improved.

Minor comments:

1. Missing reference: Chirin has been recognized importance in physiology (Zhao et al., 2019; Zhu et al., 2016) but also as a biomaterial (? Reference). Suggestion: DOI: 10.3390/ma15031041 (Improving Polysaccharide-Based Chitin/Chitosan-Aerogel Materials by Learning from Genetics and Molecular Biology) This paper discusses the current usage and potential of chitin as a biomaterial in many disciplines.)
2. 3.1, second paragraph final sentence: double point

Referees cross-commenting

Rev#1 asks the same questions as I do. Technical questions and the idea to compare endogenous Kkv.The same is true with Rev#3. Overlapping questions concerning technical things about figure illustration and clarity of presented stainings. Altogether, the criticism will improve the manuscript

Significance

This paper deciphers very nicely the genetics and cellular events where and how chitin polymers become synthesized and translocated towards the apical cell membrane for further release into the extracellular space. Altogether this is fundamental work of high significance explaining how chitin is produced and released.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors provide data on the function of exp/reb and Kkv in chitin deposition. They show chitin polymerization and deposition are uncoupled and exp/reb are required for the deposition of the chitin by regulating the distribution of kkv at the apical membrane. However, there is no direct interaction between Kkv and Exp/reb. The functional analysis of Kkv and Exp/reb is interesting.

The overexpression lines are used throughout the manuscript to analyze protein functions. Since ectopic expression of kkv and exp leads to chitin synthesis and deposition. Authors use this overexpression system to analyze the functional domain of kkv and Exp/reb. It is reasonable. However overexpression line might not represent the endogenous protein perfectly, it might cause some issues to answer certain questions.

Major comments

1. Fig. 4 Does ectopic overexpression of Kkv-GFP have the same expression pattern as the endogenous Kkv? The overexpression line may lead to ectopic expression. the colocalization of endogenous Kkv and intracellular vesicles would be more accurate.
2. Are Kkv and Exp/reb expressed at the same time endogenously? If kkv is expressed earlier than Exp, can intracellular chitin be detected in wild-type embryos at early stages? Fig. 1b shows overexpression of Kkv at S13 has intracellular chitin (exp is not expressed at this stage).
3. Fig. 1B no intracellular chitin is detected. Fig. 1H intracellular chitin is detected. Does Overexpression of exp-MH2 interfere with the endogenous Exp function?
4. For measurement, some detailed info is needed, for example, what is your area of interest?

Minor comments:

1. Fig. 2 and Fig. 3. how do you define the region of apical and basal? An apical marker is needed here. N is the total number of embryos or the number of sections in the same embryo?
2. Fig. 5H What is your area of interest to measure vesicles? Which tracheal segment do you measure? Some details need to be provided here.
3. Fig. 5 what is your area of interest when you measure Kkv?

Significance

This work further advance the knowledge about chitin synthesis and deposition

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Reply to the reviewers

1. General Statements

All three reviewers demonstrated similar concerns and provided clear guidance on potential revisions. All three reviewers recognized the importance of our study to the mitosis, genome instability and DNA damage fields, and identify limitations regarding potential therapeutic implications of the study. To mitigate these limitations and extend the breadth of our study, the revised manuscript now includes colony formation assays to more directly evaluate the impact of mitotic DNA damage therapies in cancer cell proliferation. It also includes several of the experimental suggestions/clarifications proposed by the reviewers. Lastly, we include here a clear plan of additional experiments that we agree to conduct.

2. Description of the planned revisions

Reviewer #1

Major comments:

1) In the opinion of the reviewer, the study is somewhat unbalanced as it starts with a high throughput analysis of a large number of compounds but only etoposide treatment is investigated in detail in the key experiments shown in Figures 5 and 6. The effect of topoisomerase II inhibitor on kinetochore-MT stability has already been demonstrated by Bakhoum et al, 2014. If authors wish to generalize that similar phenotypes are observed after various types of DNA damage, they should test additional compounds (such as Lomustine, Mitomycin C, and Carboplatin). In addition, measuring of the kinetochore-MT half-life in figure 5 should be performed with better time resolution within the first 5 minutes. This would allow better comparison of the measured half lives that are much shorter than 5 minutes.

R: We agree with the reviewer and we will perform additional measurements of kinetochore microtubule half-life with these different compounds and include shorter time points to increase the temporal resolution within the first 5 min.

3) Involvement of Kid and Kif4A in arm ejection of the polar chromosomes is an interesting observation in context of mitotic DNA damage. However, it is unclear how the distribution of the chromokinesines was evaluated in Figure 6A-D. Was the signal quantified at the metaphase plate or at polar chromosomes? It seems that Kif4A localizes to the polar chromosome caused by etoposide treatment whereas no signal is visible in DMSO control (Fig. 6C).

R: Since whole cells were exposed to DNA damage, we had previously quantified total fluorescence intensity of Kid and Kif4a on all chromosomes (aligned and unaligned). We nevertheless concede that some chromosomes might have been more exposed (or are more susceptible) to DNA damage and we will therefore provide a quantification of the fluorescence intensity ratio of Kid and Kif4A levels on polar chromosomes relative to the metaphase plate, with and without mitotic DNA damage.

4) Authors convincingly showed that SAC is activated by mitotic damage and this is also consistent with previous reports. However they did not address if DDR pathways contribute to the activation of SAC. This would be interesting especially in context of a recent report that showed Bub3 as a direct substrate of ATM (Xiao et al. 2022, JBC). I wonder if the polar chromosomes are formed and missegregate also in the absence of ATM activity.

R: This is an interesting suggestion and we have already obtained data from one experiment regarding the formation of polar chromosomes upon ATM inhibition. We will perform additional independent validation of these data and include our findings in the fully revised manuscript.

Reviewer #2

Major comments:

…They need to present the % of cells with polar chromosomes, and it would also be informative to understand the rate of cells with lagging chromosomes, or that underwent anaphase with polar chromosomes with and without chromokinesin depletion.

R: We will quantify the frequency of the different segregation errors upon DNA damage, with and without Chromokinesin depletion.

It would be very helpful for them to provide a schematic model between DNA damage, overstable microtubules, satisfied SAC, monotelic attached chromosomes, and the role of chromokinesins. At present these connections are very unclear.

R: We thank the reviewer for drawing attention to this point. We will provide a step-by-step model in the fully revised manuscript.

Reviewer #3

Major comments:

According to Figure 2C, the ratio of "Exit with micronuclei (from misaligned chromosome(s))" is relatively low compared to other phenotypes such as "Mitotic arrest" or "Cell death." I wonder if polar chromosome phenotype is also correlated with these other cell fates. Please clarify which fate is correlated with polar chromosome formation after DNA damage.

R: We will provide these correlations. We already know that those cells that arrest in mitosis is due to misaligned chromosomes. We will also perform the correlation between cells that died and the presence of misaligned chromosomes.

In Figure 3, the authors used Nocodazole-treated background to assess the involvement of SAC in DNA-damaging compound-induced mitotic delay. However, as shown in Figure 2B, DNA-damaging compounds cause a minor delay in mitosis, which might be challenging to analyze in the presence of Nocodazole. There is also a possibility that DNA damage response (DDR) works independently and adjunctly to delay mitosis. Because one of the major claims of the authors is that "the SAC is the only mechanism that is required to delay mitosis in the presence of long-term mitotic DNA damage (page 10, line278)", I recommend Nocodazole wash-out (as in Figure 2B) to examine the effect of MPS1-IN-1 (and ideally an inhibitor of the DDR pathway, such as ATMi) on mitotic delay induced by DNA-damaging compounds.

R: We now clarify that the observed mitotic delay in the presence of DNA damaging compounds occurred after nocodazole washout. As so, nocodazole was no longer present in the system. We also draw the attention that DNA damage in the presence of nocodazole, a condition that promotes maximal SAC activity, was fully dependent on MPS1 activity (Figure 4A). We have also obtained data from one experiment regarding the formation of polar chromosomes after nocodazole wash-out and ATM inhibition. We will perform additional independent validation of these data and include our findings in the fully revised manuscript.

Figure 6E-G: I wonder whether siKid+siKif4a affected %polar chromosomes or not.

R: We will perform this experiment and include the results addressing this point in the fully revised manuscript.

Page 10, line 287: the authors claim that "we show that long-term mitotic DNA damage..., causing the missegregation of polar chromosomes due to the action of arm-ejection forces by chromokinesisns,...." However, only Mad1 localization data is provided in Figure 6E-G, and whether siKid + siKif4a rescues the missegregation of polar chromosomes is not clear. The authors should either provide supporting evidence or revise this sentence for clarity.

R: We will determine whether Kid+Kif4a depletion rescues the missegregation of polar chromosomes (i.e. reduces the frequency of cells that exit with polar chromosomes in the presence of mitotic DNA damage).

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

Reviewer #1

Major comments:

2) Authors claim that the observed phenotype of the chromosomal missegregation following the mitotic DNA damage occurs specifically in cancer cells but the data supporting this statement is poor. They need to show more data in non-transformed cells or remove the statement.

R: Data from non-transformed RPE-1 cells are now included in the revised manuscript.

Minor comments:

1) Specificity of Aurora-B pT232 antibody should be validated to exclude cross-reactivity with Aurora-A at spindle pole (Fig S8C)

R: Antibody specificity against active Aurora A and B was validated with specific kinase inhibitors. These data are now included in the revised manuscript.

Reviewer #2

Major comments:

1. The term 'long-term DNA damage during mitosis' is confusing. DNA damage occurs when? (before, or during mitosis?). Their live cell data shows they are following cells that underwent mitosis within a certain time window after damage occurred, but it is not clear if it occurs only before, or sometimes during mitosis.

R: We realize that this was indeed confusing. The only experiment where mitotic DNA damage might have been introduced before mitosis is in Figure 1A-C. All other experiments were directly or indirectly based on live-cell data in which only cells that were already in mitosis when they were exposed to DNA damage were analysed. Because these live-cell experiments revealed that DNA damage before mitosis prevented mitotic entry at the used concentration of the DNA-damaging agents, mitotic cells scored upon DNA damage in fixed cell experiments must have been already in mitosis when DNA damage was applied. We also now include a scheme of each experimental set up in the respective figures to clearly indicate how the data was obtained and to facilitate the respective interpretations. This is now clarified in the main text.

All damage occurred in cells treated with nocodazole - could this have impacted the results? Was similar DNA damage induced if cells were arrested in monastrol/STLC, or MG132 for example? They show the distal Mad2 data in STLC but not the damage. Also Figure S4A/B appears to be from one experiment only which makes it difficult to interpret.

R: We have additionally induced DNA damage when the cells were arrested in STLC. yH2AX levels as inferred by western blot analysis were indistinguishable from cells treated with nocodazole. These data are now included in the revised manuscript. We also clarify that data presented in previous Figure S4 are from 2 independent experiments.

Why not show the RPE1 data for polar chromosomes?

R: Data from non-transformed RPE-1 cells are now included in the revised manuscript.

Confusing interpretation - monotelic attachments, yet also stable attachments,..? Please can they clarify what is meant by these terms.

R: Monotelic attachments in which a single chromatid is attached to microtubules are intrinsically unstable due to the lack of centromeric tension. However, mitotic DNA damage alters this scenario and stabilizes monotelic attachments. We have now clarified this point in the main text.

They focus most of the study on understanding why polar chromosomes arise after DNA damage. However, this phenotype seems to be a relatively minor effect. Eg. In Figure 2b only a few cells exhibit very extended mitosis, and in Figure 2c only a small percentage exit mitosis with misaligned chromosomes. Furthermore, in Figure 4B the percentage of polar chromosomes with only distal Mad2 is low. In Figure 4A the images are not clear whether a 'both' or 'distal' is being shown. It does not seem as if any are distal only, and an example of this would be helpful.

R: We thank the reviewer for alluding to this important point. The frequency of cells with polar chromosomes with/without DNA damage is indicated in Figure 2C. The respective duration of mitosis due to polar chromosomes is clearly and significantly increased as shown in Figure 2B. In fixed material we chose 70 min after nocodazole washout in these experiments because there is no difference in the frequency of cells with polar chromosomes between DMSO and DNA-damage-treated cells, allowing a direct comparison of the types of kinetochore-microtubule attachments on polar chromosomes only (please see new Figure 5). We now clarify that beyond this time frame, only DNA-damage-treated cells show polar chromosomes. We also draw the reviewer’s attention to the B&W panels where the different types of attachments are clearly highlighted.

It is also not clear what 'other' means in Figure 2C.

R: The phenotypes classified as ‘other’ in Figure 2C are detailed in Figure S1C. This was indicated in the figure 2 legend, but we have now clarified it also in the main text.

They conclude that chromokinesin depletion rescues the polar chromosomes phenotype. However they do not directly assess the rate of polar chromosome formation, only the % of polar chromosomes that are only distal Mad2 as far as I can see?

R: Similar to reviewer 1, we thank this reviewer for alluding to this important point. The frequency of cells with polar chromosomes with/without DNA damage is indicated in figure 2C. The respective duration of mitosis due to polar chromosomes is clearly and significantly increased as shown in Figure 2B. In fixed material we chose 70 min after nocodazole washout in these experiments because there is no difference in the frequency of cells with polar chromosomes between DMSO and DNA-damage-treated cells, allowing a direct comparison of the types of kinetochore-microtubule attachments (please see new Figure 5). We now clarify that beyond this time frame, only DNA-damage-treated cells show polar chromosomes.

It is not clear from how many experiments data are shown for the Mad1 distal experiments in Figures 4 and S4 (there are no error bars, so is this one experiment only?). This should be indicated in figure legends, and repeated if performed only once.

R: Data presented in Figure 4 is a pool from 3 independent experiments and data presented in Figure S4 is a pool from 2 independent experiments. For these reasons, there are no error bars to include. This is now clarified in the figure legends.

Reviewer #3

Major comments:

1. Page 6, line 155: the authors claim that "In contrast, among other defects, treatment with any of the DNA-damaging compounds caused a significant mitotic delay due to the presence of misaligned chromosomes near the spindle poles." Although Figure 2A shows a representative image of polar chromosomes, I do not find quantitative data that analyze %polar chromosomes in mitosis treated with DNA-damaging compounds. I also do not find the data supporting the claim that polar chromosomes caused a mitotic delay. Because most subsequent analyses were performed based on this result, the quantitative data should be provided here. For the latter, I suggest showing "time in mitosis (Fig 2B)" separately with or without polar chromosomes.

R: The frequency of cells with polar chromosomes with/without DNA damage is indicated in figure 2C. The respective duration of mitosis due to polar chromosomes is clearly and significantly increased as shown in Figure 2B. In fixed material we chose 70 min after nocodazole washout in these experiments because there is no difference in the frequency of cells with polar chromosomes between DMSO and DNA-damage-treated cells, allowing a direct comparison of the types of kinetochore-microtubule attachments (please see new Figure 5). We now clarify that beyond this time frame, only DNA-damage-treated cells show polar chromosomes. We now highlight in figure 2C what fraction of cells underwent mitotic arrest due to polar chromosomes, as well as those that exited mitosis with polar chromosomes.

In Figure 3, the authors used Nocodazole-treated background to assess the involvement of SAC in DNA-damaging compound-induced mitotic delay. However, as shown in Figure 2B, DNA-damaging compounds cause a minor delay in mitosis, which might be challenging to analyze in the presence of Nocodazole. There is also a possibility that DNA damage response (DDR) works independently and adjunctly to delay mitosis. Because one of the major claims of the authors is that "the SAC is the only mechanism that is required to delay mitosis in the presence of long-term mitotic DNA damage (page 10, line278)", I recommend Nocodazole wash-out (as in Figure 2B) to examine the effect of MPS1-IN-1 (and ideally an inhibitor of the DDR pathway, such as ATMi) on mitotic delay induced by DNA-damaging compounds.

R: We now clarify that the observed mitotic delay in the presence of DNA damaging compounds occurred after nocodazole washout. As so, nocodazole was no longer present in the system. We also draw the attention that DNA damage in the presence of nocodazole, a condition that promotes maximal SAC activity, was fully dependent on MPS1 activity (Figure 4A).

Line 226, (our unpublished observations): because the authors claim that "the formation of polar chromosomes due to the stabilization of kinetochore-microtubule attachments upon long-term mitotic DNA damage is likely exclusive to cancer cells," the authors should present data on RPE-1 cells at least for %polar chromosome formation (as suggested in comment 1) and Mad1 localization. Plus, even though the data is provided, the statement "exclusive to cancer cells (page 8, line 230)" is speculative and should be toned down. Mad1 localization data is also important because the authors claim that "long-term mitotic NA damage specifically stabilized kinetochore-microtubule attachments in cancer cells (page 10, line 288)" in the discussion.

R: Data from non-transformed RPE-1 cells are now included in the revised manuscript.

For the Mad1 assay, such as in Fig. 4A, the authors analyzed the CENP-C pair with two or one Mad1 foci formation. However, in some representative pictures, for example, Fig S4A-Etoposide, I found pairs of CENP-C signals on the polar chromosome without any Mad1 foci (the one next to the pairs shown in the square). As the authors argue, these kinetochores may represent polar chromosomes that eventually satisfy SAC and may be important. I, therefore, wonder why those kinetochores are omitted from the assay. Please explain this point in the manuscript if there is any reason.

R: We have now provided a clearer example and clarified in the main text that only chromosomes outside the spindle area were considered polar chromosomes.

Minor comments:

Page 7, line 168: the authors claim that "regardless of the type of DNA lesion, long-term mitotic DNA damage persists throughout mitosis and promotes micronuclei formation from polar chromosomes." However, the former claim is not fully supported by Figure S3, which addressed the effect of Etoposide only; the latter claim is not fully supported by Figure 2C, which lacks clarity (as pointed out in comment 2) and statistical analysis. Please revise this sentence.

R: We now present the levels of yH2AX after treatment with Lomustine, Mitomycin C, and Carboplatin and compared it with DMSO-treated controls and Etoposide. We also include statistics for the cell fate and respective chromosome segregations errors after treatment with the different DNA damaging agents.

Line 182: it would be helpful for readers to explain why MG132 was used.

R: This is now explained in the main text.

Line 210: it would be helpful for readers to explain briefly what PA-GFP means and how the assay works.

R: This is now explained in the main text.

Figure 1E: some color codes for each compound are difficult to distinguish. I also found it challenging to locate some lines on the graph. I recommend separating this graph, for example, by types of DNA lesions caused by compounds, and color codes that are easy to distinguish should be used.

R: We have now changed the most confusing colors and provide a higher temporal resolution chart in the low yH2AX region to facilitate visualization.

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.

R: None

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Referee #3

Evidence, reproducibility and clarity

In the manuscript entitled "Long-term mitotic DNA damage promotes chromokinesin-mediated missegregation of polar chromosomes in cancer cells," the authors propose that DNA damage on mitotic chromosomes causes chromokinesin-mediated polar chromosomes, which eventually results in missegregation and micronuclei formation. They first performed screening of compounds that cause DNA damage on mitotic chromosomes and found that DNA damage delayed mitosis in the nocodazole wash-out experiment. The authors found that several DNA damage-inducing compounds all caused an increase of asymmetric Mad1 localization on polar chromosomes. Using photoactivatable GFP-a-tubulin, the authors showed that a-tubulin stabilizes after Etoposide treatment. They finally showed that chromokinesin Kid and Kif4a knockdown rescues the asymmetric Mad1 localization.

Major comments:

1. Page 6, line 155: the authors claim that "In contrast, among other defects, treatment with any of the DNA-damaging compounds caused a significant mitotic delay due to the presence of misaligned chromosomes near the spindle poles." Although Figure 2A shows a representative image of polar chromosomes, I do not find quantitative data that analyze %polar chromosomes in mitosis treated with DNA-damaging compounds. I also do not find the data supporting the claim that polar chromosomes caused a mitotic delay. Because most subsequent analyses were performed based on this result, the quantitative data should be provided here. For the latter, I suggest showing "time in mitosis (Fig 2B)" separately with or without polar chromosomes.
2. According to Figure 2C, the ratio of "Exit with micronuclei (from misaligned chromosome(s))" is relatively low compared to other phenotypes such as "Mitotic arrest" or "Cell death." I wonder if polar chromosome phenotype is also correlated with these other cell fates. Please clarify which fate is correlated with polar chromosome formation after DNA damage.
3. In Figure 3, the authors used Nocodazole-treated background to assess the involvement of SAC in DNA-damaging compound-induced mitotic delay. However, as shown in Figure 2B, DNA-damaging compounds cause a minor delay in mitosis, which might be challenging to analyze in the presence of Nocodazole. There is also a possibility that DNA damage response (DDR) works independently and adjunctly to delay mitosis. Because one of the major claims of the authors is that "the SAC is the only mechanism that is required to delay mitosis in the presence of long-term mitotic DNA damage (page 10, line278)", I recommend Nocodazole wash-out (as in Figure 2B) to examine the effect of MPS1-IN-1 (and ideally an inhibitor of the DDR pathway, such as ATMi) on mitotic delay induced by DNA-damaging compounds.
4. Line 226, (our unpublished observations): because the authors claim that "the formation of polar chromosomes due to the stabilization of kinetochore-microtubule attachments upon long-term mitotic DNA damage is likely exclusive to cancer cells," the authors should present data on RPE-1 cells at least for %polar chromosome formation (as suggested in comment 1) and Mad1 localization. Plus, even though the data is provided, the statement "exclusive to cancer cells (page 8, line 230)" is speculative and should be toned down. Mad1 localization data is also important because the authors claim that "long-term mitotic NA damage specifically stabilized kinetochore-microtubule attachments in cancer cells (page 10, line 288)" in the discussion.
5. For the Mad1 assay, such as in Fig. 4A, the authors analyzed the CENP-C pair with two or one Mad1 foci formation. However, in some representative pictures, for example, Fig S4A-Etoposide, I found pairs of CENP-C signals on the polar chromosome without any Mad1 foci (the one next to the pairs shown in the square). As the authors argue, these kinetochores may represent polar chromosomes that eventually satisfy SAC and may be important. I, therefore, wonder why those kinetochores are omitted from the assay. Please explain this point in the manuscript if there is any reason.

Minor comments:

1. Page 7, line 168: the authors claim that "regardless of the type of DNA lesion, long-term mitotic DNA damage persists throughout mitosis and promotes micronuclei formation from polar chromosomes." However, the former claim is not fully supported by Figure S3, which addressed the effect of Etoposide only; the latter claim is not fully supported by Figure 2C, which lacks clarity (as pointed out in comment 2) and statistical analysis. Please revise this sentence.
2. Line 182: it would be helpful for readers to explain why MG132 was used.
3. Line 210: it would be helpful for readers to explain briefly what PA-GFP means and how the assay works.
4. Figure 6E-G: I wonder whether siKid+siKif4a affected %polar chromosomes or not.
5. Page 10, line 287: the authors claim that "we show that long-term mitotic DNA damage..., causing the missegregation of polar chromosomes due to the action of arm-ejection forces by chromokinesisns,...." However, only Mad1 localization data is provided in Figure 6E-G, and whether siKid + siKif4a rescues the missegregation of polar chromosomes is not clear. The authors should either provide supporting evidence or revise this sentence for clarity.
6. Figure 1E: some color codes for each compound are difficult to distinguish. I also found it challenging to locate some lines on the graph. I recommend separating this graph, for example, by types of DNA lesions caused by compounds, and color codes that are easy to distinguish should be used.

Referees cross-commenting

I generally agree with other reviewers' comments and confirmed that they raised similar concerns.

Significance

It has been described previously that mitotic arrest induces DNA damage and that the DDR pathway during mitosis is attenuated. The data presented in this manuscript provide a potentially novel cellular response against DNA damage during mitosis. The manuscript will be of interest to those in the field of the cell cycle (especially mitosis), the DDR, and tumor chemotherapies. While the finding that DNA damage during mitosis causes polar chromosomes is potentially interesting, the manuscript is still rather descriptive, and data that address the molecular mechanism is insufficient for the level that the authors conclude. Although the data quality is high, I think some essential data supporting their conclusion and clarity of the description are missing from the manuscript, which can be addressed before publication.

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Referee #2

Evidence, reproducibility and clarity

Novais-Cruz et al present an interesting and generally well-performed study on the impact of DNA damage just prior to mitosis on chromosome segregation fidelity. Overall, the experiments are performed and presented to a high standard, and the key findings are potentially of interest. However, in its present form the manuscript is overall quite confusing and it is difficult to assess the robustness of their conclusions. Their observations and mechanistic model connecting the observations is not clear at all in the current form. Several key pieces of data are missing that would help craft the story, and more explanation is needed to connect their overarching hypothesis to the data better. The below points serve as an illustration of the missing information that would be needed in order to make a proper judgement of whether the data support their main conclusions.

1. The term 'long-term DNA damage during mitosis' is confusing. DNA damage occurs when? (before, or during mitosis?). Their live cell data shows they are following cells that underwent mitosis within a certain time window after damage occurred, but it is not clear if it occurs only before, or sometimes during mitosis.
2. All damage occurred in cells treated with nocodazole - could this have impacted the results? Was similar DNA damage induced if cells were arrested in monastrol/STLC, or MG132 for example? They show the distal Mad2 data in STLC but not the damage. Also Figure S4A/B appears to be from one experiment only which makes it difficult to interpret.
3. Why not show the RPE1 data for polar chromosomes?
4. Confusing interpretation - monotelic attachments, yet also stable attachments,..? Please can they clarify what is meant by these terms.
5. They focus most of the study on understanding why polar chromosomes arise after DNA damage. However, this phenotype seems to be a relatively minor effect. Eg. In Figure 2b only a few cells exhibit very extended mitosis, and in Figure 2c only a small percentage exit mitosis with misaligned chromosomes. Furthermore, in Figure 4B the percentage of polar chromosomes with only distal Mad2 is low. In Figure 4A the images are not clear whether a 'both' or 'distal' is being shown. It does not seem as if any are distal only, and an example of this would be helpful.
6. It is also not clear what 'other' means in Figure 2C.
7. They conclude that chromokinesin depletion rescues the polar chromosomes phenotype. However they do not directly assess the rate of polar chromosome formation, only the % of polar chromosomes that are only distal Mad2 as far as I can see? They need to present the % of cells with polar chromosomes, and it would also be informative to understand the rate of cells with lagging chromosomes, or that underwent anaphase with polar chromosomes with and without chromokinesin depletion.
8. It would be very helpful for them to provide a schematic model between DNA damage, overstable microtubules, satisfied SAC, monotelic attached chromosomes, and the role of chromokinesins. At present these connections are very unclear.
9. It is not clear from how many experiments data are shown for the Mad1 distal experiments in Figures 4 and S4 (there are no error bars, so is this one experiment only?). This should be indicated in figure legends, and repeated if performed only once.

Significance

Novais-Cruz et al present an interesting and generally well-performed study on the impact of DNA damage just prior to mitosis on chromosome segregation fidelity. Overall, the experiments are performed and presented to a high standard, and the key findings are potentially of interest to the mitosis, and genomic instability fields.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the presented manuscript, authors investigated consequences of DNA damage on progression through mitosis. In agreement with previous reports, they observed a mitotic delay that was dependent on activation of the spindle assembly checkpoint (SAC). Starting with a high throughput screening authors concluded that the SAC-dependent mitotic delay is a common feature and is not limited to a specific type of DNA damage. They followed with a more detailed analysis using selected compounds and showed that mitotic DNA damage promotes formation of polar chromosomes with stable kinetochore-microtubule attachments. The live-cell imaging revealed that the cells carrying DNA damage eventually exited mitosis with the misaligned chromosomes forming micronuclei in the daughter cells. Most of the conclusions are supported by the experimental data with some exceptions detailed below.

Major comments:

1. In the opinion of the reviewer, the study is somewhat unbalanced as it starts with a high throughput analysis of a large number of compounds but only etoposide treatment is investigated in detail in the key experiments shown in Figures 5 and 6. The effect of topoisomerase II inhibitor on kinetochore-MT stability has already been demonstrated by Bakhoum et al, 2014. If authors wish to generalize that similar phenotypes are observed after various types of DNA damage, they should test additional compounds (such as Lomustine, Mitomycin C, and Carboplatin). In addition, measuring of the kinetochore-MT half-life in figure 5 should be performed with better time resolution within the first 5 minutes. This would allow better comparison of the measured half lives that are much shorter than 5 minutes.
2. Authors claim that the observed phenotype of the chromosomal missegregation following the mitotic DNA damage occurs specifically in cancer cells but the data supporting this statement is poor. They need to show more data in non-transformed cells or remove the statement.
3. Involvement of Kid and Kif4A in arm ejection of the polar chromosomes is an interesting observation in context of mitotic DNA damage. However, it is unclear how the distribution of the chromokinesines was evaluated in Figure 6A-D. Was the signal quantified at the metaphase plate or at polar chromosomes? It seems that Kif4A localizes to the polar chromosome caused by etoposide treatment whereas no signal is visible in DMSO control (Fig. 6C).
4. Authors convincingly showed that SAC is activated by mitotic damage and this is also consistent with previous reports. However they did not address if DDR pathways contribute to the activation of SAC. This would be interesting especially in context of a recent report that showed Bub3 as a direct substrate of ATM (Xiao et al. 2022, JBC). I wonder if the polar chromosomes are formed and missegregate also in the absence of ATM activity.

Minor comments:

1. Specificity of Aurora-B pT232 antibody should be validated to exclude cross-reactivity with Aurora-A at spindle pole (Fig S8C)

Significance

This study addresses the impact of mitotic DNA damage on chromosome segregation which is an important but largely unexplored topic. Authors extend earlier observations by Bakhoum et al, 2014 and demonstrate that also the misaligned polar chromosomes result in formation of micronuclei and may promote chromosomal instability. The study will be of interest mainly for the mitosis filed. The possibility that the described phenotype may have implications for cancer therapies is interesting but will surely require more detailed studies.

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Reply to the reviewers

Manuscript number: RC-2022-01406

Corresponding author(s): Harris, Reuben

1. General Statements [optional]

We would like to thank all three reviewers for their time and thorough assessment of our manuscript. We appreciate their constructive feedback and believe our work has been considerably strengthened by addressing the comments, suggestions, and concerns raised during peer review. In the following responses, we address the reviewer’s critiques point-by-point.

2. Point-by-point description of the revisions

Reviewer 1

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

Moraes et al. build upon their recent studies of APOBEC3 antagonism by EBV BORF2 by showing that additional RNR subunits encoded by other herpesviruses share this activity, suggesting that the host-virus arms races involving APOBEC3 proteins is more widespread than previously thought. Furthermore, the authors show that herpesviruses infecting primates that lack A3B (New World Monkeys) do not apparently exhibit a capacity to antagonize human A3B, suggesting that this function was not required during the evolution of those viruses (while it seemingly was important for viruses infecting hosts that encode A3B). Overall, this is a technically sound submission that combines confocal immunofluorescence, co-immunoprecipitation, and enzymatic assays to comprehensively test the sensitivity of different A3s to counteraction by viral RNRs. The enzymatic (deamination) assays performed prove to be the most insightful, since co-IP and colocalization microscopy was not entirely sufficient to reveal which domains of A3 are important for targeting by RNRs. It is well-written, well-organized, and well-referenced, and will be of interest to readers who study APOBEC3s, herpesviruses, and host-virus arms races more generally.

Response: Thank you for appreciating the technical aspects and broader impact of our studies.

Major points:

1. Figure 4B: the fluorescence microscopy data does not match well with the Co-IP (in Figure 4A). For example, L1B in A3A enhances the A3A-BORF2 co-IP but no clear differences are observed in colocalization. Or are the authors claiming the presence of L1B results in greater colocalization between A3A and BORF2, because there is slightly less diffuse BORF2 in the cytoplasm under these conditions? If that is the case, then quantitative colocalization analysis will need to be performed. In general, virtually none of the colocalization analysis in Figure 4B matches well with the co-IP results of Figure 4A. The authors take this to suggest that L7, and not L1, is most important determinant for BORF2 binding to A3s, but in that case, then the colocalization data is disconnected functionally from co-IP results. This is not necessarily a large problem, since the authors ultimately test the enzymatic activity of A3s in the presence of different RNRs. These latter functional experiments more objectively define what regions of A3s are important for antagonism by RNRs.

Response: Thank you for giving us an opportunity to clarify these important points. We understand how the fluorescence microscopy data in Figure 4B may at first appear to disagree with the co-IP results in Figure 4A. However, we would like to point out that WT A3A—which has a shorter L1 region and binds less strongly to BORF2 compared to A3B—is nevertheless efficiently relocalized by BORF2 (PMID 35476445, 31534038, 31493648). We believe that this observation can be explained by compensatory avidity interactions during cytoplasmic aggregate formation in living cells, a process mediated by the formation of a non-canonical BORF2-BORF2 dimer as detailed in our recent cryo-EM studies (PMID 35476445). These avidity interactions explain how a weaker interaction (as indicated by weaker co-IP levels) can still result in the formation of large cytoplasmic aggregates. We have therefore revised our text to explain this apparent incongruity (page 11, lines 10-13).

Can the authors discuss/cite more about the actual subcellular compartments that the A3s are being relocated towards by the RNPs? In general, the authors' comments are limited to whether the A3 is predominantly in the nucleus, or not.

Response: Previous imaging studies with markers for cytoplasmic organelles by our lab suggested that BORF2-A3B aggregates accumulate within the endoplasmic reticulum (ER) (PMID 30420783). However, in our recent cryo-EM studies of the BORF2-A3B complex (PMID 35476445), we discovered that disrupting BORF2-BORF2 dimerization prevents aggregate formation but does not affect EBV BORF2’s ability to bind to A3B and relocalize the complex to the cytoplasmic compartment. In other words, dimerization-deficient mutants of BORF2 clearly cause A3B-BORF2 heterodimers to appear diffusely cytoplasmic. Therefore, we no longer have a reason to implicate the ER and we aim to clarify this in future studies aiming to define the full molecular composition of the large cytoplasmic aggregates.

Since the authors draw a connection between the absence of A3B in New World Monkeys and the fact that New World Monkey-specific viruses don't seem to counteract A3s, can the authors discuss what could be learned by studying human individuals who lack A3B and the evolution of herpesviruses in those individuals?

Response: This is a very interesting point, but we would prefer not to speculate on this in our manuscript. Although there is indeed an A3B deletion allele in the human population (predominantly southeast Asia), its worldwide allele frequency is quite low and most people still have 1 or 2 copies of this antiviral gene. Thus, the deletion allele frequency is not high enough to remove the selective pressure on the virus to maintain A3B counteraction activity through its RNR.

        However, we did discover one Old World monkey species that completely lacks *A3B* (*Colobus angolensis*). We showed that the RNR from the gamma-herpesvirus that infect these monkeys (ColHV-1) lacks the ability to antagonize human A3B, ancestral A3B, human A3A, or the endogenous A3A of its natural host (__Figure 8__ and __Figure 8—figure supplement 3__). Thus, as you predicted, relieving the selective pressure within a species over an evolutionary period of time likely resulted in loss of A3B-antagonism activity by the viral RNR (page 19, lines 8-16).

Minor points:

1. I'm not sure it makes sense to call out Figures 1A-D in the Introduction section, rather than the Results section.

Response: We have changed the Introduction and removed the original Figure 1 completely. We have however added a new Figure 1, which provides a structural rationale for our overall experimental approach.

Reviewer #1 (Significance (Required)):

This work represents a step-wise advance from the authors' previous work on herpesvirus RNPs and counteraction of host APOBEC3s. I study host-virus molecular arms race on evolutionary scales and this article is of interest and significance to me, and I assume to others in the field as well. The findings found within the submission are interesting but not necessarily informative about human health and disease. However, the subsequent work that this manuscript inspires is likely to tell us more about herpesvirus evolution in human patients and the mechanisms by which APOBEC3s promote cancer.

Response: We thank you again for appreciating the broader significance of our work and how the results present here may inspire important future studies.

Reviewer 2

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

Summary: Building off the groups prior work on A3B and EBV BORF2 interactions, here they have expanded their studies to examine additional herpesvirus RNRs, demonstrating which features are conserved. Using a combination of IP experiments and IF, they have included KSHV ORF61 and HSV-1 ICP6 RNRs, and demonstrated that the A3 loop structures, L1, L3, and L7 from A3A, A3B, and A3G play varying roles in determining the ability to interact with the different RNRs. They then go on to demonstrate that the ability of BORF2 to block the deaminase activity of A3B is dependent on the tyrosine at position 481. Lastly, and most interestingly, they show that RNRs from Old World monkeys, but not New World monkeys, can bind to A3A and A3B, lead to their re-localization, and block deaminase activity.

Response: We thank you for appreciating the molecular details and broader impact of our studies. Please note that we have revised the paper to focus on gamma-herpesviruses by removing the less informative results with HSV-1 and adding new studies on Old/New World viral RNRs including comparisons with ancestral A3B.

Major comments: The vast majority of this work is very convincing. The authors claims are clearly reflected in the data presented for the most part. However, the work done with HSV-1 ICP6 co-IP is not very convincing. The authors claim that L7 and L3 swaps from A3Bctd to A3Gctd decreases pulldown (lines 5-12, p.7; lines 18-21, p.8; line 17, p.16). The figures (2A, 3A, 4A) however show only A3A being pulled down with ICP6. The re-localization data however does seem more consistent with the above claims. The authors note this in line 9, p.8. However, they come to a different conclusion in line 2, p.8, regarding the discrepancy between IP and IF data.

Response: As mentioned above, we have removed the less convincing results with HSV-1 ICP6. We believe uncovering the mechanistic details of HSV-1 ICP6 interaction with A3B will require significant additional work and, therefore, would prefer to address this question in future studies.

The data and methods are clearly presented, with the exception of the supplemental figures, where it is unclear how the predicted modeling was conducted.

Response: We apologize for the brief description in our earlier submission. We have revised our Methods section and included a more detailed description regarding the generation of protein structural models (page 29, lines 20-23; page 30, lines 1-6).

Experiments all seem to be sufficiently replicated.

Response: Thank you.

Minor comments:

The references to prior studies seem comprehensive. Text and figures were all very clear. Introducing the supplemental figure 1 earlier, may provide clarity to the argument about degree of relatedness (line 2, p.7).

Response: We agree with this suggestion and have made changes to introduce the structural model of KSHV ORF61 in our new Figure 1.

The suggestion of ORF61 interaction with L3 as an anchor region (line 10-12, p.9) was not very clear/could benefit from a bit more elaboration.

Response: We agree with this comment and have placed the predicted structural model of KSHV ORF61 bound to A3Bctd in our new Figure 1 and we have changed the text to clarify the role of A3B L3 in binding to KSHV ORF61 (page 10, lines 4-8).

Reviewer #2 (Significance (Required)):

This work builds on the conceptual framework of host-pathogen interactions and co-evolution, adding new examples of co-divergence of primate herpesviruses with their respective host restriction factors. Following up on past findings (Cheng et al., 2019; Shaban et al., 2021), and reports from others (Stewart et al., 2019), they outline the degree to which their initial findings (BORF2 and A3B interactions) are conserved across other herpesvirus RNRs, and place them in the context of the evolution of the A3 gene locus and expansion.

This work will be of great interest to virologists. Especially those that work in the field of host pathogen evolution and the molecular arms race.

My background is in host-pathogen interactions and herpesvirus evolution. I lack the sufficient expertise to evaluate the predicted modeling.

Response: We thank you again for appreciating the novelty and significance of our work. We are also hopeful that it will be of great interest to virologists.

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Reviewer 3

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

In this manuscript, Moraes and colleagues build upon previous publications from this group to 1) characterize the variation in the ability of orthologs of BORF2 from six different herpesviruses to bind and/or relocalize and/or inhibit the deaminase activity of A3A and A3B; 2) use swaps and other mutagenesis to measure whether various regions and amino acids in A3A, A3B, and A3G contribute to the observed variation in the ability of RNR subunits from different viruses to bind these A3s.

The data convincingly show that different regions of different A3s contribute differently to binding of RNRs from different viruses. These same regions also have variable effects on RNR-mediated relocalization and inhibition of the deamination activity of A3A, A3B, and A3G. In the last set of experiments presented in the manuscript, the authors show that the RNR from the four viruses isolated from humans and rhesus macaques are able to bind human A3B, while the RNRs from two New World monkey viruses are unable to bind human A3B. Finally, the authors suggest a correlation between the timing of the birth of A3B in the branch leading to the last common ancestor of hominoids/Old World monkeys and the gain of A3 binding/antagonism by herpesvirus RNRs. However, these evolutionary implications are not convincingly supported by the current datasets and would require a significant burden of initial experiments to test.

Response: We thank the reviewer for the nice summary of our work and for appreciating the loop swaps experiments showing differential RNR binding to APOBEC3s. In our original submission, we compared the RNRs of 4 viruses infecting Catarrhini primates and 2 viruses infecting New World primate species. We found that only the RNRs from viruses that infect Catarrhini primates bind, relocalize, and inhibit human A3B. We have now performed additional experiments to further investigate this remarkable association (Figures 7, 8, and associated supplementary material) which are detailed in our revised manuscript and summarized below:

First, we have expanded the scope of our experiments to include all publicly available RNR sequences from primate gamma-herpesviruses (i.e., 11 RNRs in contrast to our initial 6 RNRs). Second, we tested this whole panel against human A3B and found that only the RNRs from viruses that infect Old World primates that encode A3B are able to bind, relocalize, and inhibit human A3B (Figures 6 & 8). In comparison, binding to human A3A in co-IP experiments is invariably weaker and/or not detectable, relocalization phenotypes are less pronounced, and DNA deaminase activity is not inhibited (Figure 6 and Figure 8—figure supplement 2B). __Third, a subset of this RNR panel was tested against the A3A enzymes of their natural host species (__Figure 7) and, again, only the RNRs form viruses that infect Old World primates bind and relocalize the A3A enzymes tested. Fourth, as an addition test of this idea, we grafted a short helical loop structure (HLS) from EBV BORF2 into the marmoset CalHV-3 RNR and showed that this small change enabled the chimeric protein to bind to both human A3B and A3A (likely through L7), though not to the natural marmoset A3A protein. Fifth, we used all available present-day primate A3B sequences to reconstruct the most likely ancestral A3B sequence and showed that this enzyme is nuclear and as active (if not more active) than human A3B (Figure 8). This ancestral A3B protein is also bound, relocalized, and inhibited by most present day RNRs from gamma-herpesviruses that infect species with A3B, but not by the RNRs of any of the NWM-infecting viruses tested. The only exception to this association between A3B and Catarrhini-infecting gamma-herpesviruses is the RNR of the African Colobus virus ColHV-1, which we found can likely be explained by the loss of A3B in its host species due to a deletion that occurred approximately 10-14 mya after the split of the Colobinae subfamily into African and Asian tribes, which further supports the idea that A3-antagonism by gamma-herpesvirus RNRs is maintained by the selective pressure imposed by the antiviral activity of A3B.

Major Comments

1) The use of only the human orthologs of A3A and A3B limit the inferences that can be made regarding the ability of RNRs from various viruses to bind the A3s from the host species of that virus. For example, human A3A (and other hominoid A3As) have a rather distinct Loop 1 sequence, where that same loop in rhesus A3A is a much more similar to A3B. It follows that the RNRs from rhesus-tropic viruses could very well bind and inhibit A3A from rhesus. Likewise, the A3B-RNR interactions within and between species could differ markedly. Indeed, we know that the loops of A3s are some of the most rapidly evolving regions of these genes.

Response: We agree fully with these points and have addressed them through several new experiments. We have now tested the RNRs from rhesus macaque and NWM gamma-herpesviruses against the A3A enzymes of their natural host species (Figure 7) and found that only RNRs form viruses that infect Old World primates bind and relocalize the A3A enzymes tested. In addition, we used all available present-day primate A3B sequences to reconstruct the most likely ancestral sequence and showed that this ancestral A3B enzyme is antagonized exclusively by the RNRs of present-day gamma-herpesviruses that infect A3B-encoding primates.

2) If RNR's ability to bind A3s correlated or was driven by the birth of A3B in catarrhine primates, the evolution of the binding/antagonism trait would be highly unparsimonious. The most parsimonious scenario would be emergence of A3 antagonism in the LCA of alpha and gammaherpesviruses (since the authors show A3 binding in HSV-1 and several gammaherpesviruses) with a loss of the trait in NWM-infecting viruses; alternatively, the trait could have been horizontally transferred gained 3 independent times, but this is certainly unlikely and not supported by any data. However, it is also possible that the RNRs from NWM infecting viruses do, in fact, bind/antagonize the A3 orthologs from NWMs. This needs to be tested before addressing the complexities of the birth of the antagonism trait.

Response: Please see our responses above. All of our results support a model in which the birth of A3B in an ancestral primate selected for a gamma-herpesvirus with A3B binding and neutralization activity and that this activity has been maintained through evolution and still manifests today in all of the tested present-day RNRs of gamma-herpesviruses that infect species with A3B.

Minor Comments

1) The authors should state more discreetly what is new to this paper and what was shown in previous paper and in some cases repeated here. For example, figure 1 is all repeated experiments from previous papers which is unusual for a manuscript.

Response: This is a fair point and we have removed the original Figure 1 and replaced it with a structural model that provides a strong rationale for the rest of our studies. For the sake of clarity, we have also revised our text and made the necessary changes to ensure a clear distinction between new and repeated results.

2) The authors conclude that RNRs bind to A3s via partially distinct surfaces, but they don't actually test binding. Swaps and mutations do not show that the site of mutation is a site of interaction. but they do test the requirement of these AAs or regions for binding. Formally, these mutations could be exerting an allosteric effect on the binding interface of RNR and A3. In combination with the CryoEM data, these new data do support the model that these are different surfaces of interaction, but the wording should be more precise to present this.

Response: In our revised manuscript we use a combination of in silico protein structure prediction and docking to model the binding interface between human A3Bctd and KSHV ORF61 (new Figure 1). This approach predicts an interaction with the L3 region of A3B, which we validate through co-IP and co-localization experiments (Figure 3). In contrast, EBV BORF2 requires the L7 region to bind to A3Bctd and this interaction is additionally strengthened by L1 residues (Figures 2 & 4). Taken together with our prior cryo-EM data, these results point to a model in which EBV BORF2 and KSHV ORF61 bind to different surfaces of A3B (albeit near the active site and likely due to evolutionary “wobbling”). We therefore believe it to be unlikely that this mechanism is allosteric given our prior structural studies and the likely common evolutionary origin of this A3B antagonism mechanism.

3) Similar to point 1, the authors repeatedly discuss the "most critical determinant of EBV BORF2 binding" and other "most critical" interactions. This is not supported by the data and should be changed to something along the lines of 'the site of largest effect among the sites we analyzed'.

Response: We have endeavored to change this text as suggested except in cases referring to the interactions between EBV BORF2 and A3Bctd, since the results presented here together with our cryo-EM structure of the BORF2-A3Bctd complex (PMID 35476445) allow us to confidently say that L7 and L1 are the most critical determinants.

4) All microscopy figures need an A3 only panel (no RNR) to be able to judge relocalization.

Response: Changed as suggested.

5) The matrix of labels above each IP blot is excessive since each lane only has one component that differs from the other lanes. A single label for each lane would make the plot easier to discern. These figures would also benefit from clearer labels including which virus each blot panel corresponds to (these could be along the left side of each blot; currently, the RNR gene name is provided, but this is a bit hard to find within the figure). Figures 2-4 would benefit from a label above each panel A indicating "L1" "L3" "L7".

Response: Changed as suggested.

6) If the authors comment on pg9 ln 8 about intermediate relocalization effect, they should also mention 1C A3B L7G against BORF2

Response: Changed as suggested (page 8, lines 16-19).

7) Why is there no quantification of 6D relocalization? Could be supplemental if needed.

Response: We have performed quantification of the relocalization phenotypes in Figures 2, 3 & 4 in order to allow direct comparison between WT and chimeric A3 enzymes in the presence of the same viral RNR (EBV BORF2 or KSHV ORF61). On the other hand, the images in Figure 6D are representative of the A3B/A relocalization phenotypes elicited by a larger panel of different viral RNRs. These representative images should be interpreted together with the co-IP and ssDNA deaminase activity assay data in Figures 6C & 6E, respectively.

8) Pg 6 ln 13 and Pg 8 ln2-4, ICP6 doesn't coIP w A3B; this should be clarified.

Response: A similar concern was also raised by reviewer #2, and we agree that the ICP6 data present in the original version of this manuscript are not as easily interpretable compared to results with the RNRs from gamma-herpesviruses such as EBV and KSHV. For the sake of clarity and cohesion, we decided to remove all of the HSV-1 ICP6 data from the revised version of our manuscript and focus on the A3B interactions with gamma-herpesviruses.

9) Pg 8 ln21-23, the authors assume loss of function for A3G, but this swap could be functionally equivalent, but necessary for binding; it should be clarified that this is different than changing sequence and still binding.

Response: Rephrased (page 9, lines 13-16).

10) Pg 9, ln 11, what is an anchor region?

Response: We have removed the term “anchor region” and rephrased our text to more clearly describe the importance of L3 in KSHV ORF61 binding (page 10, lines 4-8).

11) Pg 9, ln 23, speculative - this might be explained by this 3 AA motif but it has not been tested.

Response: Changed wording (page 10, lines 17-20).

12) Pg 10 ln 8, this doesn't show that this region is dispensable for binding, only that there is equivalent contribution or lack of contribution of function by the A and B loops, again assuming that the G loop is LOF

Response: Removed the phrase “indicating that this region may be dispensable for the interaction” (page 11, 1-2).

13) Pg 10 ln 10 - "can be explained by presence of bulky tryp" - this should be reworded to 'could or is likely caused by'.

Response: Changed as suggested (page 11, lines 4-6).

14) Pg 11 ln 21, "can be explained by our cryo-EM" should be reworded to 'is supported by these contacts in cryo-EM'

Response: Changed as suggested (page 12, lines 15-18).

15) Pg 13 ln 10 (and other places) dissociation rates are only part of affinity, Ka is equally important (pg 18 ln 8 also)

Response: We agree and have revised our text account for this suggestion (page 13, lines 22-23; page 14, lines 1-2; page 22, lines 12-15).

16) Pg 14, ln 15 should be reworded to 'relocalize HUMAN cellular A3s'

Response: Changed as suggested (page 15, line 11).

17) Pg 16 Ln 16, this should be reworded as the data can't say it is completely dispensable without deletion of the loop.

Response: Changed as suggested (page 21, lines 10-11).

18) New World monkeys have high activity of transposable elements of distinct types relative to catarrhines. It would be useful to mention that A3s restrict endogenous elements as well and how this might be a factor in the proposed evolutionary model.

Response: This is a very interesting point that we plan to discuss in a future review. In addition, many future experiments will be needed to test the potential relationship between the birth of A3B and its potential impact on different classes of endogenous transposable elements.

19) Are the New World monkey viruses pathogenic in their native hosts? Perhaps not based on previous literature (reviewed in PMID: 11313011). This should be included in the discussion as it could certainly effect the evolutionary model for the birth/retention of A3 antagonism in these viruses.

Response: While interesting, the observation that NWM herpesviruses do not cause disease in their native hosts is not unusual. In fact, most gamma-herpesviruses (including human viruses like EBV and KSHV) have limited pathogenic potential when infecting their natural hosts (Fleckenstein B, Ensser A. Gammaherpesviruses of new world primates. Human Herpesviruses: Biology, Therapy, and Immunoprophylaxis. 2007). Additionally, although the mentioned study (PMID: 11313011) reports asymptomatic infection of squirrel monkeys with SaHV-2, pathogenic infection/ oncogenic transformation have been reported following natural infection of marmosets with CalHV-3 (PMID: 11158621).

20) In previous papers on this topic, the lab has tested the effect of mutations on viral titers. While this may be beyond the scope of this paper, this would certainly elevate the paper and should be more clearly discussed.

Response: As noted by the reviewer, we have previously demonstrated that A3B restricts EBV replication though a mutation-dependent mechanism and that this is counteracted by EBV BORF2 (PMID 30420783). While we completely agree that investigating the effect of A3B-catalyzed mutations on the titers of different gamma-herpesviruses would be interesting, this would be technically challenging as we are currently not equipped to work with KSHV or any non-human primate herpesvirus.

21) What is the degree of sequence similarity among these and other RNRs? Is there any sense of what region of RNR binds A3s from the CryoEM structures and differences within these regions that might explain the functional differences?

Response: We thank the reviewer for raising this important point. We have now included a new Figure 1 where we leverage the cryo-EM structure of the EBV BORF2-A3Bctd complex to make inferences about which regions of KSHV ORF61 may be involved in binding A3B/A. As described above, we also graft a short helical loop structure (HLS) from EBV BORF2 into the marmoset CalHV-3 RNR and showed that this small change enables the chimeric protein to bind to bind both human A3B and A3A (likely through L7), though not to the natural host marmoset A3A protein (Figure 7). Many additional interspecies chimeras could be constructed but we feel these are better suited for future studies (and specially to accompany future structural work in this area).

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Reviewer #3 (Significance (Required)):

Significance

Previous work from the Harris lab showed that a subunit of the ribonucleotide reductase of some herpesviruses acts as an antagonist of several human APOBEC3s. Mechanistically, these viral protein block A3 inhibition by relocalizing nuclear A3s as well as inhibiting A3 deamination by binding and occluding the A3 active site. For Epstein-Barr virus, deletion of the antagonist (BORF2) results in a decrease in viral replication and accumulation of mutations likely introduced by host A3B that is no longer inhibited. However, deletion of the A3 antagonist from herpes simplex virus-1 (ICP6) had no effect on viral titers. Most recently, this group published a cryoEM structure of BORF2 in complex with the c-terminal half of A3B. This structure showed extensive contacts between BORF2 and two loops of A3B - L1 and L7.

The manuscript under review focuses on the previously suggested differences in the ability of different RNRs to bind A3A and A3B. This work provides an important contribution to this topic in defining specific regions of A3A and A3B and A3G that are necessary for viral RNRs to bind them. The variability in these interactions is surprising and likely testament to the impactful coevolution of herpesviruses and primate A3s. This manuscript will be of particular interest to virologists studying A3s or herpesviruses as well as evolutionary biologists interested in the rules of engagement between host restriction factors and viruses.

Response: We thank you again for these thoughtful comments and for appreciating the overall significance of our work.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, Moraes and colleagues build upon previous publications from this group to 1) characterize the variation in the ability of orthologs of BORF2 from six different herpesviruses to bind and/or relocalize and/or inhibit the deaminase activity of A3A and A3B; 2) use swaps and other mutagenesis to measure whether various regions and amino acids in A3A, A3B, and A3G contribute to the observed variation in the ability of RNR subunits from different viruses to bind these A3s.

The data convincingly show that different regions of different A3s contribute differently to binding of RNRs from different viruses. These same regions also have variable effects on RNR-mediated relocalization and inhibition of the deamination activity of A3A, A3B, and A3G. In the last set of experiments presented in the manuscript, the authors show that the RNR from the four viruses isolated from humans and rhesus macaques are able to bind human A3B, while the RNRs from two New World monkey viruses are unable to bind human A3B. Finally, the authors suggest a correlation between the timing of the birth of A3B in the branch leading to the last common ancestor of hominoids/Old World monkeys and the gain of A3 binding/antagonism by herpesvirus RNRs. However, these evolutionary implications are not convincingly supported by the current datasets and would require a significant burden of initial experiments to test.

Major Comments

1. The use of only the human orthologs of A3A and A3B limit the inferences that can be made regarding the ability of RNRs from various viruses to bind the A3s from the host species of that virus. For example, human A3A (and other hominoid A3As) have a rather distinct Loop 1 sequence, where that same loop in rhesus A3A is a much more similar to A3B. It follows that the RNRs from rhesus-tropic viruses could very well bind and inhibit A3A from rhesus. Likewise, the A3B-RNR interactions within and between species could differ markedly. Indeed, we know that the loops of A3s are some of the most rapidly evolving regions of these genes.
2. If RNR's ability to bind A3s correlated or was driven by the birth of A3B in catarrhine primates, the evolution of the binding/antagonism trait would be highly unparsimonious. The most parsimonious scenario would be emergence of A3 antagonism in the LCA of alpha and gammaherpesviruses (since the authors show A3 binding in HSV-1 and several gammaherpesviruses) with a loss of the trait in NWM-infecting viruses; alternatively, the trait could have been horizontally transferred gained 3 independent times, but this is certainly unlikely and not supported by any data. However, it is also possible that the RNRs from NWM infecting viruses do, in fact, bind/antagonize the A3 orthologs from NWMs. This needs to be tested before addressing the complexities of the birth of the antagonism trait.

Minor Comments

1. The authors should state more discreetly what is new to this paper and what was shown in previous paper and in some cases repeated here. For example, figure 1 is all repeated experiments from previous papers which is unusual for a manuscript.
2. The authors conclude that RNRs bind to A3s via partially distinct surfaces, but they don't actually test binding. Swaps and mutations do not show that the site of mutation is a site of interaction. but they do test the requirement of these AAs or regions for binding. Formally, these mutations could be exerting an allosteric effect on the binding interface of RNR and A3. In combination with the CroEM data, these new data do support the model that these are different surfaces of interaction, but the wording should be more precise to present this.
3. Similar to point 1, the authors repeatedly discuss the "most critical determinant of EBV BORF2 binding" and other "most critical" interactions. This is not supported by the data and should be changed to something along the lines of 'the site of largest effect among the sites we analyzed'.
4. All microscopy figures need an A3 only panel (no RNR) to be able to judge relocalization.
5. The matrix of labels above each IP blot is excessive since each lane only has one component that differs from the other lanes. A single label for each lane would make the plot easier to discern. These figures would also benefit from clearer labels including which virus each blot panel corresponds to (these could be along the left side of each blot; currently, the RNR gene name is provided, but this is a bit hard to find within the figure). Figures 2-4 would benefit from a label above each panel A indicating "L1" "L3" "L7".
6. If the authors comment on pg9 ln 8 about intermediate relocalization effect, they should also mention 1C A3B L7G against BORF2
7. Why is there no quantification of 6D relocalization? Could be supplemental if needed.
8. Pg 6 ln 13 and Pg 8 ln2-4, ICP6 doesn't coIP w A3B; this should be clarified.
9. Pg 8 ln21-23, the authors assume loss of function for A3G, but this swap could be functionally equivalent, but necessary for binding; it should be clarified that this is different than changing sequence and still binding.
10. Pg 9, ln 11, what is an anchor region?
11. Pg 9, ln 23, speculative - this might be explained by this 3 AA motif but it has not been tested.
12. Pg 10 ln 8, this doesn't show that this region is dispensable for binding, only that there is equivalent contribution or lack of contribution of function by the A and B loops, again assuming that the G loop is LOF
13. Pg 10 ln 10 - "can be explained by presence of bulky tryp" - this should be reworded to 'could or is likely caused by'.
14. Pg 11 ln 21, "can be explained by our cryo-EM" should be reworded to 'is supported by these contacts in cryo-EM'
15. Pg 13 ln 10 (and other places) dissociation rates are only part of affinity, Ka is equally important (pg 18 ln 8 also)
16. Pg 14, ln 15 should be reworded to 'relocalize HUMAN cellular A3s'
17. Pg 16 Ln 16, this should be reworded as the data can't say it is completely dispensable without deletion of the loop.
18. New World monkeys have high activity of transposable elements of distinct types relative to catarrhines. It would be useful to mention that A3s restrict endogenous elements as well and how this might be a factor in the proposed evolutionary model.
19. Are the New World monkey viruses pathogenic in their native hosts? Perhaps not based on previous literature (reviewed in PMID: 11313011). This should be included in the discussion as it could certainly effect the evolutionary model for the birth/retention of A3 antagonism in these viruses.
20. In previous papers on this topic, the lab has tested the effect of mutations on viral titers. While this may be beyond the scope of this paper, this would certainly elevate the paper and should be more clearly discussed. What is the degree of sequence similarity among these and other RNRs? Is there any sense of what region of RNR binds A3s from the CryoEM structures and differences within these regions that might explain the functional differences?

Significance

Previous work from the Harris lab showed that a subunit of the ribonucleotide reductase of some herpesviruses acts as an antagonist of several human APOBEC3s. Mechanistically, these viral protein block A3 inhibition by relocalizing nuclear A3s as well as inhibiting A3 deamination by binding and occluding the A3 active site. For Epstein-Barr virus, deletion of the antagonist (BORF2) results in a decrease in viral replication and accumulation of mutations likely introduced by host A3B that is no longer inhibited. However, deletion of the A3 antagonist from herpes simplex virus-1 (ICP6) had no effect on viral titers. Most recently, this group published a cryoEM structure of BORF2 in complex with the c-terminal half of A3B. This structure showed extensive contacts between BORF2 and two loops of A3B - L1 and L7.

The manuscript under review focuses on the previously suggested differences in the ability of different RNRs to bind A3A and A3B. This work provides an important contribution to this topic in defining specific regions of A3A and A3B and A3G that are necessary for viral RNRs to bind them. The variability in these interactions is surprising and likely testament to the impactful coevolution of herpesviruses and primate A3s. This manuscript will be of particular interest to virologists studying A3s or herpesviruses as well as evolutionary biologists interested in the rules of engagement between host restriction factors and viruses.

Expertise keywords: restriction factors, APOBEC3 evolution, evolutionary genomics, genetic conflict

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Referee #2

Evidence, reproducibility and clarity

Summary:

Building off the groups prior work on A3B and EBV BORF2 interactions, here they have expanded their studies to examine additional herpesvirus RNRs, demonstrating which features are conserved. Using a combination of IP experiments and IF, they have included KSHV ORF61 and HSV-1 ICP6 RNRs, and demonstrated that the A3 loop structures, L1, L3, and L7 from A3A, A3B, and A3G play varying roles in determining the ability to interact with the different RNRs. They then go on to demonstrate that the ability of BORF2 to block the deaminase activity of A3B is dependent on the tyrosine at position 481. Lastly, and most interestingly, they show that RNRs from Old World monkeys, but not New World monkeys, can bind to A3A and A3B, lead to their re-localization, and block deaminase activity.

Major comments:

The vast majority of this work is very convincing. The authors claims are clearly reflected in the data presented for the most part. However, the work done with HSV-1 ICP6 co-IP is not very convincing. The authors claim that L7 and L3 swaps from A3Bctd to A3Gctd decreases pulldown (lines 5-12, p.7; lines 18-21, p.8; line 17, p.16). The figures (2A, 3A, 4A) however show only A3A being pulled down with ICP6. The re-localization data however does seem more consistent with the above claims. The authors note this in line 9, p.8. However, they come to a different conclusion in line 2, p.8, regarding the discrepancy between IP and IF data.

The data and methods are clearly presented, with the exception of the supplemental figures, where it is unclear how the predicted modeling was conducted.

Experiments all seem to be sufficiently replicated.

Minor comments:

The references to prior studies seem comprehensive. Text and figures were all very clear. Introducing the supplemental figure 1 earlier, may provide clarity to the argument about degree of relatedness (line 2, p.7).

The suggestion of ORF61 interaction with L3 as an anchor region (line 10-12, p.9) was not very clear/could benefit from a bit more elaboration.

Significance

This work builds on the conceptual framework of host-pathogen interactions and co-evolution, adding new examples of co-divergence of primate herpesviruses with their respective host restriction factors. Following up on past findings (Cheng et al., 2019; Shaban et al., 2021), and reports from others (Stewart et al., 2019), they outline the degree to which their initial findings (BORF2 and A3B interactions) are conserved across other herpesvirus RNRs, and place them in the context of the evolution of the A3 gene locus and expansion.

This work will be of great interest to virologists. Especially those that work in the field of host pathogen evolution and the molecular arms race.

My background is in host-pathogen interactions and herpesvirus evolution. I lack the sufficient expertise to evaluate the predicted modeling.

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Referee #1

Evidence, reproducibility and clarity

Moraes et al. build upon their recent studies of APOBEC3 antagonism by EBV BORF2 by showing that additional RNR subunits encoded by other herpesviruses share this activity, suggesting that the host-virus arms races involving APOBEC3 proteins is more widespread than previously thought. Furthermore, the authors show that herpesviruses infecting primates that lack A3B (New World Monkeys) do not apparently exhibit a capacity to antagonize human A3B, suggesting that this function was not required during the evolution of those viruses (while it seemingly was important for viruses infecting hosts that encode A3B). Overall, this is a technically sound submission that combines confocal immunofluorescence, co-immunoprecipitation, and enzymatic assays to comprehensively test the sensitivity of different A3s to counteraction by viral RNRs. The enzymatic (deamination) assays performed prove to be the most insightful, since co-IP and colocalization microscopy was not entirely sufficient to reveal which domains of A3 are important for targeting by RNRs. It is well-written, well-organized, and well-referenced, and will be of interest to readers who study APOBEC3s, herpesviruses, and host-virus arms races more generally.

Major points:

1. Figure 4B: the fluorescence microscopy data does not match well with the Co-IP (in Figure 4A). For example, L1B in A3A enhances the A3A-BORF2 co-IP but no clear differences are observed in colocalization. Or are the authors claiming the presence of L1B results in greater colocalization between A3A and BORF2, because there is slightly less diffuse BORF2 in the cytoplasm under these conditions? If that is the case, then quantitative colocalization analysis will need to be performed. In general, virtually none of the colocalization analysis in Figure 4B matches well with the co-IP results of Figure 4A. The authors take this to suggest that L7, and not L1, is most important determinant for BORF2 binding to A3s, but in that case, then the colocalization data is disconnected functionally from co-IP results. This is not necessarily a large problem, since the authors ultimately test the enzymatic activity of A3s in the presence of different RNRs. These latter functional experiments more objectively define what regions of A3s are important for antagonism by RNRs.
2. Can the authors discuss/cite more about the actual subcellular compartments that the A3s are being relocated towards by the RNPs? In general, the authors' comments are limited to whether the A3 is predominantly in the nucleus, or not.
3. Since the authors draw a connection between the absence of A3B in New World Monkeys and the fact that New World Monkey-specific viruses don't seem to counteract A3s, can the authors discuss what could be learned by studying human individuals who lack A3B and the evolution of herpesviruses in those individuals?

Minor points:

1. I'm not sure it makes sense to call out Figures 1A-D in the Introduction section, rather than the Results section.

Significance

This work represents a step-wise advance from the authors' previous work on herpesvirus RNPs and counteraction of host APOBEC3s. I study host-virus molecular arms race on evolutionary scales and this article is of interest and significance to me, and I assume to others in the field as well. The findings found within the submission are interesting but not necessarily informative about human health and disease. However, the subsequent work that this manuscript inspires is likely to tell us more about herpesvirus evolution in human patients and the mechanisms by which APOBEC3s promote cancer.

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Reply to the reviewers

1. General Statements [optional]

See cover letter for more details.

Summary of response to reviewers:

We were immensely pleased that the reviewers considered our conclusions “well supported” and our study “beautifully executed”. Reviewers also recognized the significance of our work. Reviewer 1 stated that “building a model that describes one of these pathways will allow us to begin to test therapies to treat or prevent scoliosis” then noted that we “help to build a larger model of normal spine morphogenesis” and that this is “important”. Reviewer 2 called our work an “exciting advance in our understanding of one of the essential signaling pathways that help regulate body axis straightening and spine morphogenesis in zebrafish” and mentioned that our work “may also help to further our understanding of the etiology and pathophysiology of multiple forms of neuromuscular scoliosis in humans”. Reviewer 3 agreed, stating that our work “adds important information on the role of urotensin signaling in spine formation” and noted that it is timely: “findings are of special significance in the light of recent reports that mutations in UTS2R3 show association with spinal curvature in patients with adolescent idiopathic scoliosis”.

We thank the three reviewers for reading our research and providing feedback. In all cases, we have incorporated (or plan to incorporate) their suggestions, and we believe this has (will) make our manuscript much stronger. Indeed, reviewers had only a small number of “major points”, and all are easily addressed as summarized below. We have already addressed some of those “major points”, as well as the majority of “minor points” raised by reviewers, in our current draft. We expect that all comments can be fully addressed within around 1 month.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are plannedto address the points raised by the referees.

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We have divided our responses by whether the reviewers considered their points major or minor. All points have already been, or will soon be, fully addressed.

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Major points

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Reviewer 1

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The key conclusions are well supported, see below for my two major issues.

Please don't call this lordosis. Lordosis or hyperlordosis effects lumbar vertebra. The curve in the lumbar region shifts body weight so that human gait is more efficient that that in the great apes, or so the story goes. Zebrafish do not have lumbar vertebra equivalents or a natural curve in the caudal region. Similarly, fish do not have the equivalent vertebra to generate kyphosis, which is again a hyper flexion of a normal human spinal curve. Instead zebrafish have Weberian, precaudal and caudal vertebra. It would be so much more useful for the field if the authors used these terms and specified ranges, i.e. numbered vertebrae, that are effected so we can directly and accurately compare regions of defects between zebrafish mutants. It would help to make the point that the uts2r3 mutant has more caudally located curves than urp1/2 double mutants. We appreciate this point and agree with the reviewer. Lordosis (or hyperlordosis) is indeed the accentuation of a curve which naturally exists in humans but not zebrafish. We called the phenotype of Urotensin pathway mutants ‘lordosis’ or ‘lordosis-like’ because of the position of the curves — in caudal vertebrae, which are evolutionarily and positionally equivalent to lumbar vertebrae, though they are structurally different to human lumbar vertebrae. To address this comment, we will no longer refer to the phenotype as lordosis in our Introduction or Results sections and we will expand our Discussion to include this point raised by the reviewer.

1. The observation that urp1/2 double mutants have curves only in the D/V plane and almost completely lack side-to-side curves is noteworthy. Does the urp1-/-urp2-/- mutant uncouple two systems for posture? If this separate a DV from side-to-side postural control system, that would be very interesting. It is particularly important to describe how penetrant the phenotype is and how many times it was observed. See 9 minor comments. It would help the reader if the authors explicitly described the features that they see in the cfap298 mutant that constitute lateral curves and that are lacking in urp1/2 (e.g. in figure 4E).

We plan to expand the figure and analysis describing D/V curves and M/L curves. While our first draft included only cfap298 and urp1-∆P;urp2-∆P mutants, our next draft will also incorporate uts2r3 and pkd2l1 mutants. We have already scanned cohorts of all mutant fish, and so the remaining work to render and quantify the degree of lateral curvature will not take long. This will allow us to conclusively determine whether these different mutations indeed uncouple two systems controlling posture in different directions. As the reviewer requests, we will include all fish analyzed in either main or supplementary figures, include numbers in figure legends, and quantify the penetrance of M/L and D/V curves.

We have also generated cfap298;urp1-∆P;urp2-∆P triple mutants and are currently scanning them to reveal skeletal form. Preliminary data suggests triple mutants have three-dimensional curves but D/V curves are more severe in triple mutants than in cfap298 mutants alone. This makes sense if Urp1/Urp2 are important for controlling D/V spinal shape and, as our qPCR shows, Urp1/Urp2 are downregulated but not lost completely in cfap298 mutants. It also furthers the notion that cilia motility controls D/V and M/L curves by separable mechanisms. * *

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Reviewer 2

Need to show that the CRISPANT targeting was effective for mutagenesis at each loci screened in the work presented in Figure 1E. In Figure 1E, we presented the phenotypes of crispant embryos (i.e. embryos injected with four gRNAs targeting a specific gene alongside relatively high doses of Cas9 protein; see schematic in Figure 1G). In positive controls (cfap298 and sspo), crispants showed the expected phenotype in all cases (Figure 1E and see Figure 1H for quantitation). As for germline mutants, urp1 and urp2 crispants showed no early axial phenotypes (Figure 1E and 1H). As such, the reviewer requests that we perform molecular assays to determine whether mutagenesis was successful in these embryos. To do so, we will perform either T7 assays or next-generation/Sanger sequencing of mutated loci. This will allow us to determine and quantify the effectiveness of our mutagenesis. Results will be shared in a new supplementary figure. These assays are straightforward and we expect they will not take very long to complete. Indeed, we have performed these assays previously for other genes (e.g. Grimes et al., 2019 and several unpublished genes). We have achieved high levels of mutagenesis in all cases, making us very confident that we will achieve similarly high levels of mutagenesis in this case.

Reviewer 3

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The addition of the F0 crispant experiment to show that the pro-peptide of urp1/2 does not have a function and is responsible for the difference between the observed morpholino and the crispr phenotype was important. However, since no phenotype was observed in crispants it is important to add evidence of induced cuts for all guide RNAs used in the crispant experiment. These control experiments might have been done already. If not, they can easily be done in a short period of time by performance of T7 assays on injected fish and would not require additional reagents. This is the same point raised by reviewer 2 and so we refer to the response above. In summary, we agree with the reviewer and we are currently performing these suggested experiments which are straightforward and working well.

The authors claim that there were no structural defects observed in urp1/2 double mutants. However, the hemal arch in figure 3 E seems to be deformed. This could be normal variance or a phenotype. This can be addressed by simple reinspection of the scans.

We believe there are no major vertebral structural defects that could be attributed to causing the spinal curves because vertebrae are well-formed in mutants and we see no defects in the initial patterning of vertebrae in our calcein experiments. However, since urp1-∆P;urp2-∆P and uts2r3 mutant spines are curved, the vertebrae are a little misshapen. We plan two revisions, one textual and one analytical.

First, we will make clear in our textual edits that some vertebrae are slightly misshapen, as occurs in non-congenital forms of human spinal curve disease (in congenital forms, the shape defects are more striking and likely causative in the curvature). We agree with the reviewer that stating that there is a lack of vertebral structural defects lacked nuance, so we will expand on this in our next draft.

Second, we will quantify vertebral shapes in spinal curve mutants and report these data in our next draft. After reinspection of the scans, as the reviewer suggested, we believe it would be informative for our readers to see quantitation of vertebral shape. We expect these data to more rigorously back up our statements about ‘minor structural differences’ of vertebrae between uncurved and curved individuals. We have already begun this work, and completing it should only take a few more weeks. As an example, we have measured the shape of centra by calculating aspect ratios in wild-type and urp1-∆P;urp2-∆P double mutants in curved regions of the spine:

These preliminary data already make clear that there are indeed subtle morphological differences between vertebrae in mutants and wild-type, as occurs in human spinal curve deformities. We will present completed versions of these data (several parameters that describe vertebral shape) in our next draft and provide comments about whether such changes could be causative in spinal curve etiology as occurs in congenital-type scoliosis.

Minor points

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Reviewer 1

Supplementary FigS3B How to measure the Cobb Angle is unclear. Why is the first curve not counted? I count 3 curves. First a ventral displacement, then a dorsal to ventral return, then a sharp flex before the tail. How to measure Cobb angle might be easier to explain if the figure is expanded into steps. Identify the apical vertebra, then showing how the lines are drawn parallel to those vertebrae, then where the measured angle forms between the lines perpendicular to the drawn parallel lines.

We will more thoroughly explain how Cobb angle is measured in our next draft.

5a. I think we (zebrafish biologists) need be explicit about what we mean with "without vertebral defects." What do we count as defects? Vertebrae can be fused, bent, shortened or the growing edges can be slanted. In Figure 3E, and movie7, it is clear that the highlighted mutant vertebrae are shorter than WT. The growing ends of normal vertebra are perpendicular to the long axis of the vertebra. In the mutants the ends are slanted. Please define in the text what you consider a relevant vertebral defect, because these vertebrae have defects. Or are you only considering the calcein stained centra at 10dpf?

We strongly agree with the reviewer. As described more thoroughly above in response to Major Comment – Reviewer 3, we plan both textual edits and new quantitation of vertebral shape to address this comment. Our quantitation indeed shows some vertebrae are shorter in mutants as the reviewer noticed. We also plan a new paragraph in the Discussion section which will speak about the issue of what zebrafish biologists might mean by “without vertebral defects”.

5b. Do you want to base your patterning conclusion on primarily the calcein data as these are closer to the notochord patterning time window. Please anchor this conclusion to a specific time or standard length e.g. 10dpf/5.6mm.

When we edit our descriptions of vertebral defects, and include new quantitative data on the shape of vertebrae, we will be clear that the vertebrae are slightly structurally malformed. In addition, when we speak of the calcein data, we will anchor those conclusions to the specific timepoint best studied by this method, as the reviewer suggests.

"At 30 dpf... several mutants exhibited a significant curve in the pre-caudal vertebrae, in addition to a caudal curve (Fig. 3D and S3C). Since pre-caudal curves were rare in mutants at 3-months, this suggested that curve location is dynamic".The frequency of this observation is important. Does it effect all or a fraction of mutants? Can you provide some numbers to anchor these observations? Maybe fractions e.g.. 3 of 4 fish had precaudal curves at 30pdf, and 0 of 10 fish had precaudal curves by 3 mpf?

In our next draft, we will provide numbers of fish examined at 30 dpf and also show graphical summaries of curve position (as we did for younger fish). Last, all scans will be included in a new supplementary figure.

The description of the pkd2l1 mutant, instead of terming it kyphosis can you tell the reader the vertebra number at the peak of the curve. The authors say the pkd2l1 mutant is highly distinct from urp1/urp2-/-, but the reader needs to hear exactly what is distinct. For example, does this mutant have both lateral and D/V curves?

We have now scanned several pkd2l1 mutant fish and we will include images of pkd2l1 mutants at two different timepoints together with quantitation of curve position. Our results agreed with those previously published for this mutant line (Sternberg et al., 2018) but we believe it is important for our readers to see side-by-side images and quantitation so they can see the distinctions.

At 3-months of age, pkd2l1 mutants essentially appear wild-type but by around 12-months they have developed a D/V curve in the pre-caudal vertebrae. They do not exhibit M/L curves; we will quantify this and include these data in our Figure about M/L deviation.

We called the phenotype displayed by pkd2l1 mutants “kyphosis” to be in line with a previous publication describing these mutants (Sternberg et al., 2018). We will add new wording in the Discussion about whether or not zebrafish can truly model kyphosis and lordosis (see response to Reviewer 1 major comment above), and we make clear in our Results that the phenotype has “been argued to model kyphosis (Sternberg et al., 2018)” rather than “is kyphosis”.

It is intriguing that pkd2l1 mutants do not exhibit any curves until much later in life than urp1-∆P;urp2-∆P and uts2r3mutants. Inspired by this finding, we aged urp1-∆P and urp2-∆P single mutants and found that they go on to develop D/V curves by 12-months i.e.

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• *3-months 12-months Position of curve

urp1-∆P no curves mild D/V curves Mostly caudal

urp2-∆P mild D/V curves intermediate D/V curves Mostly caudal

urp1-∆P;urp2-∆P severe D/V curves severe D/V curves Mostly caudal

uts2r3 severe D/V curves severe D/V curves Mostly caudal

cfap298 severe 3D curves severe 3D curves Caudal and pre-caudal

pkd2l1 no curves mild D/V curves Mostly pre-caudal

Phenotypes in urp1-∆P and urp2-∆P single mutants upon aging shows: 1) Urp1 and Urp2 are not entirely redundant in long-term spine maintenance and 2) proper Urp1/Urp2 dose is essential. We will include these new data in our next draft.

Does uts2r3-/- have no /minimal side-to-side curves like urp1/urp2-/-?

This is an interesting question. To address it, we will add images of uts2r3 mutant spines from the dorsal aspect and include them with our new quantitation of lateral curvature. To sum, the reviewer’s suggestion is correct – there are minimal side-to-side curves in uts2r3 mutants.

One finding that deserves more discussion is the observation that urp1/urp2 double mutants have almost no side-to-side defects and all the obvious bends are in the D/V plane. Does this uncouple two systems for posture? Please consider the following paper. It shows a proprioception system that maintains normal side-to-side posture. A spinal organ of proprioception for integrated motor action feedback. Picton LD, Bertuzzi M, Pallucchi I, Fontanel P, Dahlberg E, Björnfors ER, Iacoviello F, Shearing PR, El Manira A. Neuron. 2021 Apr 7;109(7):1188-1201.e7. doi: 10.1016/j.neuron.2021.01.018. Epub 2021 Feb 11. PMID: 33577748

Thank you for pointing out this manuscript. We will include it in our expanded Discussion.

Reviewer 2

Fig 3F: might be improved by making the images black and white and possibly inverted. It is not easy to clearly see the vertebrae as is. * *

Thanks for the suggestion, we will make this change.

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

Minor points

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Reviewer 1

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Figure 1D legend says urp1 is expressed in dorsal while urp2 is express in all CSF-cNeurons, but the image for urp1 shows only ventral cells in WT, while the image for urp2 shows the same cells ...and more dorsal cells. Please replace image with one that matches the text. Apologies for this, we have now corrected it. The image was correct but we accidentally wrote “dorsal” instead of “ventral” when describing the CSF-cN sub-population harboring urp1 transcripts.

In Figure 2H, the position of curve apex graphic, how many fish were examined? In 2f it looks like n=8 and n=9. Can this info be added to the figure?

We have now included the number examined in the legend.

I did not find legends for the movies. The first call to the movies calls movies 1-3 without explaining what each shows. The labels on the downloaded files are not informative.

Apologies for forgetting to submit these. We have now added informative Movie legends.

Reviewer 3

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It would be helpful to the reader to add a little more information on urp1 and upr2 proteins and their processing to make it clear while only the 3' region of the protein was targeted to induce mutations. We have incorporated textual edits to make this more clear. We now state in the second sentence of the Results section:

Urp1 and Urp2 are encoded by 5-exon genes with the final exon coding for the 10-amino acid peptides that are released by cleavage from the pro-domain (Fig. 1A).

Together with Fig. 1A and Supplementary Fig. 1, we hope it is now clear to readers how Urp1 and Urp2 are generated from a 5-exon gene encoding the pro-domain and the peptide, which are separated by cleavage.

It would also be helpful to the reader to have a schematic indicating the guide target sites (they could be added to figure S1 C + D) in the protein to be able to interpret the result more easily.

Done!

Figure 5: Addition of a square to H would help understand were the pictures in D-F were taken.

Done!

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

N/A. We are performing all experiments/analyses requested by reviewers.

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Referee #3

Evidence, reproducibility and clarity

The presented work by Bearce et al. is based on the hypothesis that urp1 and urp2, and their receptor uts2r3 play a role during zebrafish spine development. Previously it had been shown that cilia function as well as Reissner fiber formation are important for spine development and that both cilia motility and the Reissner fiber influence urp1/2 expression. Further, morpholino knock-down of upr1/2 did show the typical curly down phenotype observed in cilia and RF mutants. The authors generate CRISPR mutants for urp1, urp2 by targeting the 10-amino acid secreted peptides and do not find an early phenotype in single, double or maternal zygotic mutants or cripants. However, they observe a late onset curvature of the spine in urp1/2 double mutants and in generated uts2r3 single mutant. Spinal curvature was assessed through measurement of the Cobb angel in microCT scans and compared with other scoliosis mutants. This analysis revealed similarities between urp1/2 and uts2r3 mutants and differences with curvatures observed in cilia motility (cfap298) or Reissner fiber (sspo) mutants, which did show decreased expression levels of urp1 and 2. These differences in spine curvature do indicate that the phenotypes are not caused by the same mechanism. Analysis of the Reissner fiber in transgenic animals did show no defects.

Major points:

The paper is generally well written and easy to follow. All experiments are described in sufficient detail and reagents are listed. However, there are two points that should be addressed to strengthen the conclusion of the paper.

1. The addition of the F0 crispant experiment to show that the pro-peptide of urp1/2 does not have a function and is responsible for the difference between the observed morpholino and the crispr phenotype was important. However, since no phenotype was observed in crispants it is important to add evidence of induced cuts for all guide RNAs used in the crispant experiment. These control experiments might have been done already. If not, they can easily be done in a short period of time by performance of T7 assays on injected fish and would not require additional reagents.
2. The authors claim that there were no structural defects observed in urp1/2 double mutants. However, the hemal arch in figure 3 E seems to be deformed. This could be normal variance or a phenotype. This can be addressed by simple reinspection of the scans.

Minor points:

1. It would be helpful to the reader to add a little more information on urp1 and upr2 proteins and their processing to make it clear while only the 3' region of the protein was targeted to induce mutations.
2. It would also be helpful to the reader to have a schematic indicating the guide target sites (they could be added to figure S1 C + D) in the protein to be able to interpret the result more easily.
3. Figure 5: Addition of a square to H would help understand were the pictures in D-F were taken.

Significance

While scoliosis in human patients is very prevalent, our understanding on the mechanism that lead to the development of spinal curvature are very limited and so are the treatment strategies. The zebrafish has emerged as an important model to study spine development and formation of scoliosis. While not all findings in the presented work are novel, this work adds important information on the role of urotensin signaling in spine formation. These findings are of special significance in the light of recent reports that mutations in UTS2R, the human ortholog of uts2r3, show association with spinal curvature in patients with adolescent idiopathic scoliosis. As such, this work will be of interest not only to basic researches but also the medical field.

My field of expertise: zebrafish, CRISPR/Cas, genetics, skeletal development, spine formation

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Referee #2

Evidence, reproducibility and clarity

Major concern:

1. Need to show that the CRISPANT targeting was effective for mutagenesis at each loci screened in the work presented in Figure 1E.

Minor Concern:

1. Fig 3F : might be improved by making the images black and white and possibly inverted. It is not easy to clearly see the vertebrae as is.

Significance

Summary:

This is a beautifully executed study on the role of Urp signaling in spine morphogenesis in zebrafish. This work also challenges the model that Urp1/ 2 controls the extension and straightening of the body axis of the zebrafish embryos. Here, using a double mutant in urp1 and urp2, they show that urp1/2 are dispensable for axial straightening. Moreover, they provide redundant roles during larval development in particular for maintaining a straight spine. They go on to show that scoliosis observed in urp1/2 double mutant fish are distinct - showing only dorsal-ventral lordosis , whereas previously published scoliosis phenotypes _showing curvates in dorsal-ventral and medial-lateral axes as observed in cilia- and Reissner fiber-related scoliosis mutants. They provide clear evidence that loss of Urp signaling does not affect the stability of the Reissner fiber as it does in cilia-related scoliosis mutants. Underscoring the distinct regulation of Urp signaling on spine morphology during larval development. Altogether, this is an exciting advance in our understanding of one of the essential signaling pathways that help to regulate body axis straightening and spine morphogenesis in zebrafish. These studies may also help to further our understanding of the etiology and pathophysiology of multiple forms of neuromuscular scoliosis in humans. I recommend it for publication after revisions.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors investigate the role of Urotensin Related Peptides (Urp1 and Urp2) on zebrafish spine straightness. One model of normal spinal morphogenesis proposes that when the spine bends, material in the central canal of the spinal cord (the Reissner Fiber, RF, mostly composed of scospondin) stimulates surrounding Cerebral Spinal Fluid contacting neurons (CSF-cN), that in turn release Urotensin like peptides that cause dorsl muscles to contract and straighten the spine. It is clear that motile cilia in the central canal are responsible for forming/compacting the RF from monomers of scospondin. Mutations were generated that removed the peptide-coding portion of Urp1, Urp2 and that removed most of the Urp receptor Uts2r3 and made a missense scospondin gene. They used cfap298-/- as an immotile cilia control and scospondin-/- as a Reissner Fiber absent control. The authors show Urotensin peptides and receptor Uts2r3 function in juvenile but not embryonic axis straightening. They defined the timecourse of spinal curves onset and change during larval life, i.e., 9 dpf to 17 dpf and found that curves were dynamic between 30dpf and 3 mpf. Unlike cfap mutants, urotensin mutants show no sex bias in scoliosis expression. The authors used a temperature sensitive mutation in cfap298 and the GFP-tagged scospondin gene to show that active cilia are required for both initial formation of the RF before 28 hpf and to maintain the RF between 6 and 12 dpf. Finally the authors demonstrated that the receptor Uts2r3 is not required for establishment or maintenance of the RF at 28 hpf and 12 dpf.

Major comments

The key conclusions are well supported, see below for my two major issues.

1. Please don't call this lordosis. Lordosis or hyperlordosis effects lumbar vertebra. The curve in the lumbar region shifts body weight so that human gait is more efficient that that in the great apes, or so the story goes. Zebrafish do not have lumbar vertebra equivalents or a natural curve in the caudal region. Similarly, fish do not have the equivalent vertebra to generate kyphosis, which is again a hyper flexion of a normal human spinal curve. Instead zebrafish have Weberian, precaudal and caudal vertebra. It would be so much more useful for the field if the authors used these terms and specified ranges, i.e. numbered vertebrae, that are effected so we can directly and accurately compare regions of defects between zebrafish mutants. It would help to make the point that the uts2r3 mutant has more caudally located curves than urp1/2 double mutants.
2. The observation that urp1/2 double mutants have curves only in the D/V plane and almost completely lack side-to-side curves is noteworthy. Does the urp1-/-urp2-/- mutant uncouple two systems for posture? If this separate a DV from side-to-side postural control system, that would be very interesting. It is particularly important to describe how penetrant the phenotype is and how many times it was observed. See 9 minor comments. It would help the reader if the authors explicitly described the features that they see in the cfap298 mutant that constitute lateral curves and that are lacking in urp1/2 (e.g. in figure 4E).

Minor comments

1. Figure 1D legend says urp1 is expressed in dorsal while urp2 is express in all CSF-cNeurons, but the image for urp1 shows only ventral cells in WT, while the image for urp2 shows the same cells ...and more dorsal cells. Please replace image with one that matches the text.
2. In Figure 2H, the position of curve apex graphic, how many fish were examined? In 2f it looks like n=8 and n=9. Can this info be added to the figure?
3. Supplementary FigS3B How to measure the Cobb Angle is unclear. Why is the first curve not counted? I count 3 curves. First a ventral displacement, then a dorsal to ventral return, then a sharp flex before the tail. How to measure Cobb angle might be easier to explain if the figure is expanded into steps. Identify the apical vertebra, then showing how the lines are drawn parallel to those vertebrae, then where the measured angle forms between the lines perpendicular to the drawn parallel lines.
4. I did not find legends for the movies. The first call to the movies calls movies 1-3 without explaining what each shows. The labels on the downloaded files are not informative.
5. a. I think we (zebrafish biologists) need be explicit about what we mean with "without vertebral defects." What do we count as defects? Vertebrae can be fused, bent, shortened or the growing edges can be slanted. In Figure 3E, and movie7, it is clear that the highlighted mutant vertebrae are shorter than WT. The growing ends of normal vertebra are perpendicular to the long axis of the vertebra. In the mutants the ends are slanted. Please define in the text what you consider a relevant vertebral defect, because these vertebrae have defects. Or are you only considering the calcein stained centra at 10dpf?

5b. Do you want to base your patterning conclusion on primarily the calcein data as these are closer to the notochord patterning time window. Please anchor this conclusion to a specific time or standard length e.g. 10dpf/5.6mm. 6. "At 30 dpf... several mutants exhibited a significant curve in the pre-caudal vertebrae, in addition to a caudal curve (Fig. 3D and S3C). Since pre-caudal curves were rare in mutants at 3-months, this suggested that curve location is dynamic" The frequency of this observation is important. Does it effect all or a fraction of mutants? Can you provide some numbers to anchor these observations? Maybe fractions e.g.. 3 of 4 fish had precaudal curves at 30pdf, and 0 of 10 fish had precaudal curves by 3 mpf? 7. The description of the pkd2l1 mutant, instead of terming it kyphosis can you tell the reader the vertebra number at the peak of the curve. The authors say the pkd2l1 mutant is highly distinct from urp1/urp2-/-, but the reader needs to hear exactly what is distinct. For example, does this mutant have both lateral and D/V curves? 8. Does uts2r3-/- have no /minimal side-to-side curves like urp1/urp2-/-? 9. One finding that deserves more discussion is the observation that urp1/urp2 double mutants have almost no side-to-side defects and all the obvious bends are in the D/V plane. Does this uncouple two systems for posture? Please consider the following paper. It shows a proprioception system that maintains normal side-to-side posture. A spinal organ of proprioception for integrated motor action feedback. Picton LD, Bertuzzi M, Pallucchi I, Fontanel P, Dahlberg E, Björnfors ER, Iacoviello F, Shearing PR, El Manira A. Neuron. 2021 Apr 7;109(7):1188-1201.e7. doi: 10.1016/j.neuron.2021.01.018. Epub 2021 Feb 11. PMID: 33577748

Significance

Scoliosis effects about 3% of children worldwide. Mammals have not been good models for this condition. Zebrafish seem to have an intrinsic susceptibility to scoliosis, as well as several technical advantages. Scoliosis is likely caused by disruption of several different and independent pathways. Building a model that describes one of these pathways will allow us to begin to test for therapies to treat or prevent scoliosis.

1. The authors demonstrate that urp1 and 2 are required for normal adult spine straightness. While loss of the uts2r3 receptor (A.K.A. uts2ra, Zhang et.al., Nat Genet, 2018) and the uts4 (receptor, Alejevski, et.al, Open Bio, 2021) lead to adult spinal bends or scoliosis, of the four described urotensin ligand paralogs, only urp, not uts2, urp1 or urp2 have been tested by deletion for a role in scoliosis (Quan et.al., Peptides 2021). In the current work, the authors help to build a larger model of normal spine morphogenesis and show that mutations effecting later steps do not have typical cilia associated phenotypes. Contributing a step to this model is important.
2. The authors show that juvenile or adult scoliosis can be independent of the embryonic curves, Curly Tail Down phenotype. This result is somewhat in conflict with previous work from Zhang, in which Curly Tail Down phenotype from a cilia defective mutant (ZMYND10) was rescued by overexpression of urp1 peptide. It is possible that urp1 functions in place of the natural peptide for this function. As before there are four paralogs of urotensin peptides. The second conflicting observation from Zhang is that embryos injected with morpholino to urp1 shows Curly Tail Down phenotype. It is well known that morpholinos can have off-target effects.
3. The authors observe that urp1/urp2 double mutants have almost no side-to-side defects and all the obvious bends are in the D/V plane. Does this uncouple two systems for posture? If this separate a DV from side-to-side postural control system, that would be amazing.
4. The authors provide evidence that curves are dynamic and erasable between 30 dpf and 3 mpf. This could be a time window to apply therapeutics.
5. The authors provide a new graphic tool, a chart that logs the location of the apical curve vertebra (Figure 2H and SFigure 3C). This will allow better comparison between various scoliosis mutants.
6. The authors describe 3 different version of scoliosis in 3 mutants. In cfap298 mutants (immotile cilia) curves effect all 3 dimensions. In urp1/urp2-/- mutants, curves only appear in the D/V plane. In uts2r3 mutants, curves appear more caudal than those in urp1-/-,urp2-/- mutants, though it is not clear if these are 3D curves.

Audience: Biologists and physicians interested in 1) scoliosis, 2) normal morphogenesis, and 3) maintenance of the spine, 4)neurophysiologists interested in postural control and regulation of repetitive movements, like walking and swimming.

My expertise: zebrafish genetics, scoliosis, gastrulation

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Reply to the reviewers

Manuscript number: RC-2022-01574

Corresponding author(s): Casey, Greene

1. General Statements [optional] We thank the reviewers for their thorough feedback. We have addressed all the points raised, revised the manuscript accordingly, and explained our changes below. To aid readability, the reviewers’ comments have been converted to italics, and our responses have been bolded.

Point-by-point description of the revisions

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

The authors systematically evaluate the performance of linear and non-linear ML methods for making predictions from gene expression data. The results are interesting and timely, and the experiments are well designed.

I have a few minor comments:

- It was hard for me to understand Figure 1B. I think a figure like this would be very helpful however. What do the numbers represent? If sample ID, then I am not sure why x-axis label is also "samples"

- For analysis of GTEx data, not sure what "studywise splitting" would mean, since the GTEx dataset is one study? Do you leave out the same individuals from all tissues for evaluation?

We thank the reviewer for their input on these two points. To make Figure 1B clearer and to elaborate on our stratified splitting methods, we have amended its description to “We stratify the samples into cross-validation folds based on their study (in Recount3) or donor (in GTEx). We also evaluate the effects of sample-wise splitting and pretraining (B).”

- I found the sample size on x-axis of Fig 2a confusing. If I understand correctly, GTEx has a total of ~1000 subjects. So in some sense, effective sample size can not be bigger than 1000. If you are counting subjects x tissue as sample, then it can be misleading in terms of the effective sample size.

We thank the reviewer for this point. To incorporate it into the manuscript, we’ve added the following text to the description of Fig. 2: “It is worth noting that "Sample Count" in these figures refers to the total number of RNA-seq samples, some of which share donors. As a result, the effective sample size may be lower than the sample count. “

- Would be interesting to assess out-of-sample generalizability of linear and non-linear models. Have you tried training on GTEx and predicting on Recount3 or vice versa?

This question intrigued us. We reran the tissue prediction experiments from the manuscript on a subset of the GTEx and Recount3 datasets in which we performed an intersection over tissues and genes. We found that in the out-of-sample domain the logistic regression model and the three layer neural network performed similarly, while the five layer net generally had a lower accuracy despite having similar accuracy in the training domain. We also found (consistent with our results in the paper) that GTEx predictions are an easier task than their Recount counterparts. Below are plots demonstrating these findings:

[These plots appear in the PDF but do not appear to work in the ReviewCommons Form].

Reviewer #1 (Significance (Required)):

Important and timely study, evaluating linear vs non-linear methods for predicting phenotype from gene expression datasets.

We appreciate the reviewer’s positive comments on the timeliness of our manuscript.

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

Summary

The authors want to assess the presence of non-linear signal in gene expression values in the task of tissue and sex classification. They use logisitic regression classifiers and two types of neural networks, with 3 and 5 layers, and assess classification performance on two large expression datasets from Recount3 and GTEX and three simulated datasets.

The authors carefully construct their learning setup in such a way that one can reason about the removal of linear signal from the expression features. The interesting conclusion is, that although the linear approach works well on both datasets, and sometimes even better than the more complex models. The authors convingly show, that there is a significant non-linearity in the gene expression data. However, just because it is "there" does not imply that any non-linear methods performs better.

Major comments:

- Are the key conclusions convincing?

The authors did a good job in showing, that there is non-linear signal in gene expression features for the classification problems studied.

We thank the reviewer for their positive feedback.

- Should the authors qualify some of their claims as preliminary or speculative, or

remove them altogether?

The overall claims of the authors are justified, the discussion may be improved.

We appreciate the reviewer’s support for our overall claims and we have adjusted the manuscript as noted point by point below.

- Would additional experiments be essential to support the claims of the paper?

No, additional experiments are not essential. But the authors did not compare to other non-linear methods such as SVM or knn-classifiers in the resulst or conclusion section. It is unlikely that the main conclusion would change if those methods were tried. But it is possible that other "simpler" non-linear methods, such as knn for example, are able to outperform the logistic regression classifier on the GTEX and Recount3 data set. Thus, the authors should at least mention this as part of the conclusion and could extend their discussion on the implications of their study concerning other tasks or models.

We agree that there should be more discussion of other models in the conclusion section. We have updated the fifth paragraph of the conclusion accordingly:

“We are also unable to make claims about all problem domains or model classes. There are many potential transcriptomic prediction tasks and many datasets to perform them on. While we show that non-linear signal is not always helpful in tissue or sex prediction, and others have shown the same for various disease prediction tasks, there may be problems where non-linear signal is more important. It is also possible that other classes of models, be they simpler nonlinear models or different neural network topologies are more capable of taking advantage of the nonlinear signal present in the data.”

- Are the suggested experiments realistic in terms of time and resources?

Not applicable.

- Are the data and the methods presented in such a way that they can be reproduced?

There is a separate github repo which has the code to reproduce the analyses. This is good. However, would be nice to explain in more detail in the manuscript how the limma function was used for removing the linear signal, as they mention the "removeBatchEffect" function was used, but it would be good to tell the reader how that works, as this is their way for assessing the effect of linear-signal removal. Are there any limitations for the assessment of signal removal in this way?

We thank the reviewer for their input, and have updated the model training section on signal removal to read: “We also used Limma[24] to remove linear signal associated with tissues in the data. We ran the ‘removeBatchEffect’ function on the training and validation sets separately, using the tissue labels as batch labels. This function fits a linear model that learns to predict the training data from the batch labels, and uses that model to regress out the linear signal within the training data that is predictive of the batch labels.”

We have also elaborated on the limitations of signal removal by updating the sentence “This experiment supported our decision to perform signal removal on the training and validation sets separately, as removing the linear signal in the full dataset induced predictive signal (supp. fig. 6)” to read “This experiment supported our decision to perform signal removal on the training and validation sets separately. One potential failure state when using the signal removal method would be if it induced new signal as it removed the old. This state can be seen when removing the linear signal in the full dataset(supp. fig. 6).”

- Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

- Specific experimental issues that are easily addressable.

no

- Are prior studies referenced appropriately?

Yes

- Are the text and figures clear and accurate?

*Also, they conducted 3 different experiments in Figure 3. It would be useful to separate the figure into 3) A, 3) B, and 3) C and link that specifically in the text. Figure 4 is an extended version of Figure 2, just with the additional results of the signal removed performances. *

We appreciate the feedback. To make the figure and the text more clear, we have added A, B, and C subheadings to figure 3, and updated the subfigure’s references within the text accordingly.

First, the pairwise results in 4B are hard to read as the differences in colors and line type are difficult to see as some lines are short. Second, we did not find it helpful to reproduce the full signal approach in Figure 4. We would suggest to make Figure 4 as Figure 2, and simply only talk about the Full signal mode in the beginning, how it is in the text.

We agree. We have made Figure 4 our new Figure 2 and updated the references in the text.

Further, it would be nice to give better names in the legends of these plots. Pytorch_lr is not a nice name.

We thank the reviewer for pointing this out. We have updated the names in the legends to be “Five Layer Network”, “Three Layer Network”, and “Logistic Regression”

- Do you have suggestions that would help the authors improve the presentation of

their data and conclusions?

As the Recount3 dataset is different in quality and complexity it would be reasonable to show the results of the binary classifcation also in the main paper. In particular, as this behaves different to the GTEX binary classification.

We have now moved the Recount binary classification figure from the supplement to join the GTEx binary classification data as the new figure 4.

-The title is somewhat unprecise. It may induce the impression that the paper is about expression-prediction, although that is not the case. Further, in the abstract they don't mention what prediction problem they solve and that these are classification problems. After reading the paper it is clear why the authors choose that, but we are suggesting an alternative title that the authors may consider:

The effect of nonlinear signal in classification problems using gene expression values

We agree with the reviewer’s comment and have updated our title to “The effect of non-linear signal in classification problems using gene expression”

Further, they should give more details on the problem learned in the abstract.

We thank the reviewer for their feedback, and have added details to the abstract about the problem domains. The relevant sentence now reads “We verified the presence of non-linear signal when predicting tissue and metadata sex labels from expression data by removing the predictive linear signal with Limma, and showed the removal ablated the performance of linear methods but not non-linear ones.”

*-In addition, the conclusion section, which may be title as Disucssion and Conclusion, could contain additional points concerning the topology and training of the neural networks. *

We have updated the heading of the final section to Discussion and Conclusion. To expand on the potential drawbacks of our neural network topologies, we have also updated the limitation portion of Discussion and Conclusion to read “We are also unable to make claims about all problem domains or model classes. There are many potential transcriptomic prediction tasks and many datasets to perform them on. While we show that non-linear signal is not always helpful in tissue or sex prediction, and others have shown the same for various disease prediction tasks, there may be problems where non-linear signal is more important. It is also possible that other classes of models, be they simpler nonlinear models or different neural network topologies are more capable of taking advantage of the nonlinear signal present in the data.”

Obviously, it is possible that other simpler or more complex neural networks have a better performance on the GTEX and Recount3 data sets compared to logistic regression. In fact, the results from Figure4 suggest that, as there is clearly useful non-linear signal in those datasets for the classification problems studied. However, optimizing a non-linear model is inherently more complex and time-consuming, and thus may not be done thoroughly in previously published papers. Compared to a linear model that is easier and faster to optimize, this may be one reason why studies find that, despite non-linear signal, the linear model performs better. Other factors such as the samples size, which the authors already mention, of course also plays a big role, and if hundreds of thousands of datasets would be there , e.g. from single cell measurements, non-linear methods may have a better chance of outcompeting linear models.

We agree, which is why we consider the signal removal experiment to be so important. By demonstrating that the non-linear methods we used were in fact learning non-linear signal we were able to show that there was something that non-linear models were able to learn that logistic regression was unable to. That is to say that while the presence of non-linearity in the decision boundary is necessary for non-linear models to outperform linear ones, it is not by itself sufficient. Perhaps with more data or a different model non-linear methods would perform better, but there is certainly a class of models and problems where logistic regression is preferable.

Reviewer #2 (Significance (Required)):

The submitted manuscript adds to the discussion of the necessity of non-linear models when solving classification problems using gene expression data. The significance is mostly technically, as a comparison of logistic regression and two neural network topologies that are being compared on two large expression datasets. However, there is also a conceptual part of the contribution, which is with regards to the implications of their experiments.

Interested audience would be computer scientists and bioinformaticians or others, that are involved in creating or interpreting these or similar prediction models.

Our field of expertise is in the creation of machine learning models using different types of OMICs data. All aspects of the work could be assessed.

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

In this manuscript, the authors discuss an interesting problem regarding the comparative performance of linear and non-linear machine learning models. The main conclusion is that logistic regression (linear model) and neural networks (non-linear model) have comparable performance if the data contain both linear and non-linear relations between the features (X) and the prediction target (Y), however, if the linear component in the X-Y relation is removed (e.g. regressed out) the neural networks will outperform logistic regression. This conclusion implies that linear models such as logistic regression mainly relies on the linearity in the X-Y relation.

However, whether X-Y relation has a linear component and whether the data (e.g. for different Y classes) are linearly separable are two different questions. For example, consider a data generating mechanism, y=x^2+x and label the data points using two classes (y1). Clearly, the data is linearly separable, and any machine learning algorithm should perform very well on this problem. Now remove the linear component form the X-Y relation and use y=x^2 to generate the data. The data is still linearly separable, and the performance of logistic regression should not be affected.

We agree that there is a difference between optimal linear decision boundaries and linear relationships between elements in the training data. Our use of the term “relationship” in place of “decision boundary” was imprecise. To make this more clear, we have made the following changes:

Introduction:

“Unlike purely linear models such as logistic regression, non-linear models should learn more sophisticated representations of the relationships between expression and phenotype.” -> “Unlike purely linear models such as logistic regression, non-linear models can learn non-linear decision boundaries to differentiate phenotypes.”

“However, upon removing the linear signals relating the phenotype to gene expression we find non-linear signal in the data even when the linear models outperform the non-linear ones.” -> “However, when we remove any linear separability from the data, we find non-linear models are still able to make useful predictions even when the linear models previously outperformed the nonlinear ones.”

Discussion and conclusion:

We removed the following paragraph: “Given that non-linear signal is present in our problem domains, why doesn’t that signal allow non-linear models to make better predictions? Perhaps the signal is simply drowned out. Recent work has shown that only a fraction of a percent of gene-gene relationships have strong non-linear correlation despite a weak linear one [23].”

The point is that the performance of linear models is mainly dependent on whether the data are linearly separable instead of the linearity in X-Y relation as the manuscript suggests.

We agree that this is the key point and appreciate the reviewer for helping us to more carefully hone the language to convey this point.

Reviewer #3 (Significance (Required)):

The performance comparison between linear and non-linear machine learning models is important.

We appreciate the reviewer’s recognition of the significance of the work.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors discuss an interesting problem regarding the comparative performance of linear and non-linear machine learning models. The main conclusion is that logistic regression (linear model) and neural networks (non-linear model) have comparable performance if the data contain both linear and non-linear relations between the features (X) and the prediction target (Y), however, if the linear component in the X-Y relation is removed (e.g. regressed out) the neural networks will outperform logistic regression. This conclusion implies that linear models such as logistic regression mainly relies on the linearity in the X-Y relation. However, whether X-Y relation has a linear component and whether the data (e.g. for different Y classes) are linearly separable are two different questions. For example, consider a data generating mechanism, y=x^2+x and label the data points using two classes (y<=1 and y>1). Clearly, the data is linearly separable, and any machine learning algorithm should perform very well on this problem. Now remove the linear component form the X-Y relation and use y=x^2 to generate the data. The data is still linearly separable, and the performance of logistic regression should not be affected. <br /> The point is that the performance of linear models is mainly dependent on whether the data are linearly separable instead of the linearity in X-Y relation as the manuscript suggests.

Significance

The performance comparison between linear and non-linear machine learning models is important.

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

Summary

The authors want to assess the presence of non-linear signal in gene expression values in the task of tissue and sex classification. They use logisitic regression classifiers and two types of neural networks, with 3 and 5 layers, and assess classification performance on two large expression datasets from Recount3 and GTEX and three simulated datasets. The authors carefully construct their learning setup in such a way that one can reason about the removal of linear signal from the expression features. The interesting conclusion is, that although the linear approach works well on both datasets, and sometimes even better than the more complex models. The authors convingly show, that there is a significant non-linearity in the gene expression data. However, just because it is "there" does not imply that any non-linear methods performs better.

Major comments:

• Are the key conclusions convincing?

The authors did a good job in showing, that there is non-linear signal in gene expression features for the classification problems studied. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The overall claims of the authors are justified, the discussion may be improved. - Would additional experiments be essential to support the claims of the paper?

No, additional experiments are not essential. But the authors did not compare to other non-linear methods such as SVM or knn-classifiers in the resulst or conclusion section. It is unlikely that the main conclusion would change if those methods were tried. But it is possible that other "simpler" non-linear methods, such as knn for example, are able to outperform the logistic regression classifier on the GTEX and Recount3 data set. Thus, the authors should at least mention this as part of the conclusion and could extend their discussion on the implications of their study concerning other tasks or models. - Are the suggested experiments realistic in terms of time and resources?

Not applicable. - Are the data and the methods presented in such a way that they can be reproduced?

There is a separate github repo which has the code to reproduce the analyses. This is good. However, would be nice to explain in more detail in the manuscript how the limma function was used for removing the linear signal, as they mention the "removeBatchEffect" function was used, but it would be good to tell the reader how that works, as this is their way for assessing the effect of linear-signal removal. Are there any limitations for the assessment of signal removal in this way? - Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

no - Are prior studies referenced appropriately?

Yes - Are the text and figures clear and accurate?

Also, they conducted 3 different experiments in Figure 3. It would be useful to separate the figure into 3) A, 3) B, and 3) C and link that specifically in the text. Figure 4 is an extended version of Figure 2, just with the additional results of the signal removed performances. First, the pairwise results in 4B are hard to read as the differences in colors and line type are difficult to see as some lines are short. Second, we did not find it helpful to reproduce the full signal approach in Figure 4. We would suggest to make Figure 4 as Figure 2, and simply only talk about the Full signal mode in the beginning, how it is in the text. Further, it would be nice to give better names in the legends of these plots. Pytorch_lr is not a nice name. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

As the Recount3 dataset is different in quality and complexity it would be reasonable to show the results of the binary classifcation also in the main paper. In particular, as this behaves different to the GTEX binary classification. - The title is somewhat unprecise. It may induce the impression that the paper is about expression-prediction, although that is not the case. Further, in the abstract they don't mention what prediction problem they solve and that these are classification problems. After reading the paper it is clear why the authors choose that, but we are suggesting an alternative title that the authors may consider:

The effect of nonlinear signal in classification problems using gene expression values

Further, they should give more details on the problem learned in the abstract. - In addition, the conclusion section, which may be title as Disucssion and Conclusion, could contain additional points concerning the topology and training of the neural networks. Obviously, it is possible that other simpler or more complex neural networks have a better performance on the GTEX and Recount3 data sets compared to logistic regression. In fact, the results from Figure4 suggest that, as there is clearly useful non-linear signal in those datasets for the classification problems studied. However, optimizing a non-linear model is inherently more complex and time-consuming, and thus may not be done thoroughly in previously published papers. Compared to a linear model that is easier and faster to optimize, this may be one reason why studies find that, despite non-linear signal, the linear model performs better. Other factors such as the samples size, which the authors already mention, of course also plays a big role, and if hundreds of thousands of datasets would be there , e.g. from single cell measurements, non-linear methods may have a better chance of outcompeting linear models.

Significance

The submitted manuscript adds to the discussion of the necessity of non-linear models when solving classification problems using gene expression data. The significance is mostly technically, as a comparison of logistic regression and two neural network topologies that are being compared on two large expression datasets. However, there is also a conceptual part of the contribution, which is with regards to the implications of their experiments.

Interested audience would be computer scientists and bioinformaticians or others, that are involved in creating or interpreting these or similar prediction models.

Our field of expertise is in the creation of machine learning models using different types of OMICs data. All aspects of the work could be assessed.

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

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors systematically evaluate the performance of linear and non-linear ML methods for making predictions from gene expression data. The results are interesting and timely, and the experiments are well designed.

I have a few minor comments:

• It was hard for me to understand Figure 1B. I think a figure like this would be very helpful however. What do the numbers represent? If sample ID, then I am not sure why x-axis label is also "samples"
• For analysis of GTEx data, not sure what "studywise splitting" would mean, since the GTEx dataset is one study? Do you leave out the same individuals from all tissues for evaluation?
• I found the sample size on x-axis of Fig 2a confusing. If I understand correctly, GTEx has a total of ~1000 subjects. So in some sense, effective sample size can not be bigger than 1000. If you are counting subjects x tissue as sample, then it can be misleading in terms of the effective sample size.
• Would be interesting to assess out-of-sample generalizability of linear and non-linear models. Have you tried training on GTEx and predicting on Recount3 or vice versa?

Significance

Important and timely study, evaluating linear vs non-linear methods for predicting phenotype from gene expression datasets.

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Reply to the reviewers

Reply to the Reviewers

We thank the reviewers for their excellent suggestions and constructive comments. We now added new data on PE15/PPE20 binding to Ca2+, the PDIM status of mutant strains, additional controls, added to the discussion, added detail to the Methods, and provide all RNA-seq data. Please see replies to the comments in detail below:

Reviewer 1:

Major points

1. Cellular localization:
2. “The authors do not describe the cellular fractionation method…”, “The authors show some Western blot data in Fig. S3, though the legend is superficial (abbreviations not explained) and the controls with markers for cellular localization appear to be lacking”. “Further, the authors do not prove that FLAG-tagged PE20 is functional.”

We included a description of the fractionation method in Materials and Methods (lines 475-485). We also added detail to the legend of Fig. 4A to explain the abbreviations and controls used. The same cell fractions were used in Fig. 4A and Fig. S3A, as mentioned in the Figure S3 legend (“The same cell fractions as in Fig. 4A were used, see controls therein”). We know that the FLAG-tagged PPE20 is functional because the strain used in this experiment is the same we used for genetic complementation experiments in which FLAG-tagged PPE20 functionally complements ppe20 deletion in all three assays (ATP consumption, biofilm, Ca2+ influx, Fig.4 B,C,D,G).

• “The authors should extend discussion part of the manuscript. Several proteomic studies.” “Did authors analyze culture filtrate fraction by Western?

We thank the reviewer for the references and extended the Discussion to include results from existing proteomic studies on PE15/PPE20 (lines 229-234). We did not test for PE15/PPE20 in culture filtrate, and previous proteomic results are contradictory. Several PE/PPE proteins, including PE15/PPE20 have been detected in the cell wall and in the CFP, but not consistently. The functional significance of this dual localization is unclear.

1. Is PE15/PPE20 a channel?

2. “PPE20 purified alone from the cytosol of E. coli?”

We did not purify either protein by itself. As the reviewer correctly notes, PE/PPE proteins are refractory to individual purification. We clarified that we purified and used the complex for experiments even if only PPE20 is shown, as in Figure 3C,D, and E (Lines 124-127). See also Methods line 382 ff.

• “…a positive control of a mutant that is indeed deficient in Mg2+ import (and thus showing a phenotype) is lacking.”

Lacking a specific Mg2+ import mutant, and because it is a relatively minor point, we removed the statements about selectivity.

1. Thermal melting assay

2. It is surprising to see that the thermal melting assays was done for PPE20 and PE15 as separately purified proteins.

We co-purified PE15 and PPE20 for all biochemical experiments. We clarified that point (see also point 2 above).

• “the thermal melting assay only seemed to give some results for PPE20 alone, and not for PE15”

PE15 did not produce interpretable results in this assay, as mentioned in line 144. We clarified in the Fig. 3 legend that the complex was used although only PPE20 is detected by Western blot and shown in Figure 3C.

• “…the results are counter-intuitive… How can the authors be sure that the presence of Ca2+ does not simply lead to more protein precipitation (via rather unspecific interactions) at elevated temperatures? Some positive controls with bona fide calcium binding protein in the same thermal melting setup would have helped to clarify this.”

The effect of Ca2+ on PPE20 is somewhat counterintuitive, although not unprecedented. Proteins can be stabilized or destabilized by ligand binding, and a recent proteome-wide study on the basis of thermal shift analysis showed that ~17% of proteins were destabilized by ligand (ATP). For a channel in particular, ligand binding might be expected to be coupled to protein relaxation in the process of channel opening, which could well translate to lower thermal stability. We added the positive control showing the behavior of a known Ca2+ binding protein (new Fig. S2A). In addition, we included a negative control showing that Ca2+ does not generally increase protein denaturation (Fig. S2B). We think that this control addresses the reviewer’s concern more directly.

• If the authors want to stick to their claims regarding Ca2+ binding to PE15/PPE20, they have to perform additional assays (e.g. equilibrium dialysis or ITC) with the entire PE15/PPE20 complex. Further, they have to show that PE15/PPE20 forms a proper oligomeric protein that is membrane bound and reasonably behaved on size exclusion chromatography, when expressed in and purified from E. coli.

Detecting Ca2+ binding to proteins is not trivial, and we thank the reviewer for suggesting equilibrium dialysis as another, orthogonal assay. We now show an equilibrium dialysis experiment that confirms Ca2+ binding by the PE15/PPE20 complex. Please see the new Fig. 3F. and G. and lines 146-152 (Results) and 429-443 (Methods).

The PE/PPE proteins are generally difficult to express and purify recombinantly, likely due to the typically large unstructured regions. Also, the yield of PE15/PPE20 when expressed in E. coli was very low so that we were not able to detect the complex by SEC. However, data in Fig. 3 conclusively show that PE15 and PPE20 bind.

1. RNA-seq data

2. The authors should include a table with all other identified genes that are potentially involved in calcium homeostasis

We provided all other significant differentially expressed genes in the new Table S1.

Minor points:

1. “what is the binding affinity of the Ca sensor?”

We added the Ca2+ binding affinity of Twitch-2B (KD: 200nM) in line 176.

1. Figure 4D: “one would expect a drop in FRET signal after EGTA addition… Can the authors explain?”

We do see a clear drop in FRET signal after EGTA addition, in particular in 7H9 medium (black versus red line, Fig. 5B). Given the high affinity of Twitch-2B for Ca2+ (200nM), however, it is not surprising that the drop is not more pronounced, as intracellular Ca2+ is expected to be tightly bound to Twitch.

1. The experiments showing outer membrane localization of PE15/PPE20 are very important, but results of these experiments (western-blot and FRET) are shown in supplementary figures. They should be transferred/integrated into the main Figures.

We agree and moved Figure S3A to the main Figures as Figure 4A.

1. Line 166: the authors claim that the assay did not work in 7H9 due to low Ca2+ concentration in this medium. Why did the authors not just add a bit more calcium to show whether this claim holds true?

7H9 is not a suitable medium for these experiments because the baseline Ca2+ concentration is too high, not too low (see Fig. 5B, grey versus black line). Adding more Ca2+ to 7H9 medium resulted in precipitation, probably due to its interaction with phosphates. Our use of “low” in this context was confusing, we changed the wording of this sentence (line 180-181).

1. Line 183: more detailed description on cellular fractionation and subsequent anti-FLAG Western needed here.

We added more detail in the Materials section (lines 475 ff).

Reviewer 2:

• A major concern regarding the importance of the data: there are considerable technical challenges in generating Ca2+ depleted media. This is clear in that M. tuberculosis seems to be unaffected by Ca2+ in the medium - similar growth seems in Ca2+-free media to media with up to 10mM Ca2+ (Fig. S1). This raises a concern about the physiological relevance of the data (mammalian cells have intracellular Ca2+ of 0.01-0.1mM, extracellular free Ca2+ is around 1mM).

If we correctly understand this comment, the reviewer is unconvinced that we fully and reproducibly depleted Ca2+ from medium based on a lack of an effect of Ca2+ on in vitro growth. We tested for baseline Ca2+ levels and depletion in media by inductively coupled plasma optical emission spectrometry and added these data showing precise quantitation of Ca2+ in medium (see new Fig. S1B).

• The role of PE15/PPE20 in Ca2+ acquisition may be clearer if the authors ensure that the PDIM layer is intact. Specifically, there is a technical issue: The authors use Tween80 as a detergent. Tween-80 partially strips the outer cell wall of M. tuberculosis resulting in shedding of PDIM and PE/PPE proteins. Tyloxapol is a somewhat milder detergent. Some of the experiments would possibly show clearer phenotypes by use of Tyloxapol.

We share the concern about PDIM, as PDIM loss is common in in vitro culture. We analyzed the total lipids by thin layer chromatography and confirmed the presence of PDIM in all three strains (Fig S3C, lines 198-201). We repeated experiments with Tyloxapol and did not see differences to Tween-80. We nonetheless now show the Tyloxapol data (Fig 5D).

• The authors could increase the impact of their work be exploring the role of PE15/PPE20 during pathogenesis of resting versus activated bone marrow macrophages where Ca2+ fluxes of the host cell play a role in host responses.

We agree. In vivo or macrophage experiments are a logical next step to fully characterize the function of PE15/PPE20, but we think it is beyond the scope of this manuscript. The main contribution of this paper is the identification of channel function of a PE/PPE protein pair that extends the novel channel paradigm for these proteins. These data support that transport might indeed be a shared function of the entire PE/PPE family with 169 members.

Minor:

• The authors should consider citing Sharma et al (2021)

We cited the paper.

• Are there Ca2+ binding motifs in PPE20?

We did not detect canonical Ca2+ binding motifs in PPE20.

• RNAseq data may need to be deposited in a public database.

RNA-seq data have been deposited to NCBI - GEO accession GSE214266

Link: https://urldefense.com/v3/https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE214266;!!NuzbfyPwt6ZyPHQ!tCf4MS_HRKJFn6qV2orkDAkXTWvx9IIU11fAV7TguYE2ietoMBpBgRC7rvfnM9bsoiVdIvDBUHdPmHZliDP2o5sRZR2ziK4$

Token: cvmhakcgbpmbfuz

• In its current state, the work is somewhat incremental

The function of the large PE/PPE protein family of Mtb has been one of the most longstanding and perplexing puzzles in Mtb biology. For more than 20 years, speculation about their potential role, for example in antigenic variation, abounded but no conclusive evidence for this or another shared function emerged. A recent landmark paper then conclusively showed that a subset of the PE/PPE proteins function as nutrient channels (Wang et al., Science 2020). However, whether transporter function is a general function of the family of 169 PE/PPE proteins remains untested. Our PE/PPE pair is associated with a different type VII secretion system (Esx-3) and belongs to a different subfamily than the previous examples, suggesting a shared function across families and perhaps even all of these proteins. Given the intense interest and many false leads that have plagued the identification of PE/PPE function in the last 20 years, the difficulty of working with them biochemically, as well as the almost complete absence of understanding of Ca2+ homeostasis in Mtb, we do not consider our work incremental.

Reviewer 3

• My only slight concern is the meaning attached to the "biofilm" assays. It is never very clear to me that this is anything more than formation of a surface pellicle and general hydrophobicity of the mycobacterial cells.

We fully agree that Mtb biofilms remain poorly defined. However, the term biofilm as used in our study has already found its way into the literature and we would rather not cause confusion by calling the same phenomenon by a different name. Whatever the term used, we do not suggest any other relevance other than it being a Ca2+-dependent phenotype that serves as one of several tests to parse PE15/PPE20’s role in Ca2+ homeostasis.

Cross-consultation comments:

• We agree with the concerns of reviewer#2 that the role of PDIM and use of detergent should be looked at more closely.

We tested the roles of PDIM and detergent, see reviewer 2.

• Likewise, the paper would strongly benefit from some further insights into the potential physiological role of PPE20/PE15 in calcium homeostasis.

We show PE15/PPE20 function in the transport of Ca2+ and the first Ca2+-related cellular phenotypes in Mtb. Testing the role of the complex in an infection model is outside of the scope of this manuscript and mouse infection experiments would take many months and would likely be intractable because of the expected extensive redundancy among the 169 PE/PPE proteins.

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Referee #3

Evidence, reproducibility and clarity

Review of Boradia et al, "Calcium transport by the Mycobacterium tuberculosis PE15/PPE20 proteins" This manuscript describes studies aimed at understanding the role of calcium in the pathogenesis of tuberculosis. The authors begin by showing that, analogous to the situation in other bacteria, ATP levels are directly (and rather dramatically) affected by extracellular calcium levels. The authors then look at the effect on "biofilm formation" and, again analogous to other bacteria, find a link. The authors then perform RNAseq on bacterial cells with and without 1mM Ca++ and identify a pair of genes that is strongly downregulated by calcium sufficiency. These genes are PE/PPE family members which have been recently associated with channel formation in the mycomembrane to allow transport of small molecule solutes across the outer cell envelope. The authors show these proteins are associated in a complex by reciprocal pull-down experiments in tagged proteins and show directly that they bind calcium by a thermal stability change of this complex in the presence of calcium. Finally, they show, using a calcium sensitive FRET reporter expressed in Mtb, that these two proteins allow calcium influx and that such an influx is blocked in a strain where they have been deleted.

Overall, the study is excellent and convincingly establishes the transport function of another pair of PE/PPE proteins. My only concern with this is that they stop just short of delving into the actual infection biology of calcium, but I suppose that will be next. The tools they developed in this study, specifically the knockout strain and the FRET reporter, put them in a strong position to explore the role of calcium during growth in macrophages and other in vivo studies that are surely planned.

My only slight concern is the meaning attached to the "biofilm" assays. It is never very clear to me that this is anything more than formation of a surface pellicle and general hydrophobicity of the mycobacterial cells. I wonder if the presence of calcium alters the aggregation state of the bacilli and or affects the surface in some more subtle manner. I am not convinced that the word "biofilm" as it is used commonly in other bacteria, has anything to do with the physical properties that are being observed in the case of Mtb.

Significance

The manuscript clearly establishes that this pair of PE/PPE proteins plays a direct role in calcium transport in MTB and provides several useful tools to begin to understand the role of calcium in TB pathogenesis. The work is outstanding and novel.

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Referee #2

Evidence, reproducibility and clarity

The authors demonstrate that M. tuberculosis responds to increasing Ca2+ concentrations by increasing ATP levels as well as increased ability to form biofilms. Culturing of M. tuberculosis with Ca2+ results in downregulation of pe15/ppe20. The proteins are recombinantly expressed and the results show that PE15 and PPE20 form a complex. In addition, PPE20 seems to be destabilized by Ca2+ suggesting that it interacts with this metal ion. A pe15/ppe20 knockout shows lower levels of ATP increase upon incubation with Ca2+ although the differences with would-type are very modest. Similarly, the knockout shows an impaired ability to form biofilms at 1mM and 10mM Ca2+. Finally, the authors make a FRET reporter of intracellular Ca2+ concentrations based on the Twitch system which nicely shows that intracellular Ca2+ levels are lower in the knockout mutant.

Overall, the data suggest that PE15/PPE20 are involved in Ca2+ uptake which contributes to our evolving understanding of the role of the different PE/PPE proteins in nutrient acquisition. The highlight of the paper is the Twitch bioreporter for Ca2+ which could be useful in exploring the role of Ca2+ in mycobacteria.

A major concern regarding the importance of the data: there are considerable technical challenges in generating Ca2+ depleted media. This is clear in that M. tuberculosis seems to be unaffected by Ca2+ in the medium - similar growth seems in Ca2+-free media to media with up to 10mM Ca2+ (Fig. S1). This raises a concern about the physiological relevance of the data (mammalian cells have intracellular Ca2+ of 0.01-0.1mM, extracellular free Ca2+ is around 1mM). The role of PE15/PPE20 in Ca2+ acquisition may be clearer if the authors ensure that the PDIM layer is intact. Specifically, there is a technical issue: The authors use Tween80 as a detergent. Tween-80 partially strips the outer cell wall of M. tuberculosis resulting in shedding of PDIM and PE/PPE proteins. Tyloxapol is a somewhat milder detergent. Some of the experiments would possibly show clearer phenotypes by use of Tyloxapol. In experiments where clumping is not a concern (ATP measurement), the cells can be pre-grown as indicated but then transferred to the multiwell plates in detergent-free media. At the time of processing of the cells for readout of, for example ATP, detergent can be used as needed. The authors could increase the impact of their work be exploring the role of PE15/PPE20 during pathogenesis of resting versus activated bone marrow macrophages where Ca2+ fluxes of the host cell play a role in host responses.

Minor:

The authors should consider citing Sharma et al (2021): PGRS Domain of Rv0297 of Mycobacterium tuberculosis functions in A Calcium Dependent Manner

Are there Ca2+ binding motifs in PPE20?

RNAseq data may need to be deposited in a public database.

Significance

In its current state, this work is somewhat incremental: the authors have provided data that suggest that PE15/PP20 are involved in Ca2+ uptake (data could be strengthened as suggested above). The physiological relevance of the PE15/PPE20 system remains unclear - no data on its role in pathogenesis.

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Referee #1

Evidence, reproducibility and clarity

PE/PPE proteins build up 10% of genome of Mtb, but the function of these proteins is only currently investigated in more detail. Recent studies show the involvement of individual PE/PPE proteins in the transport of nutrients, and more data supporting this functional role are about to emerge. Using RNA-seq, Boradia et al identified the pe15/ppe20 genes to be downregulated in response to calcium exposure. Purified PPE20 (but not PE15) appear to bind calcium in a thermal stability assay (though this claim needs further experimental support). The authors generated a Mtb pe15/ppe20 knockout strain and convincingly show in three types of assays (ATP levels, biofilm formation and lower signal in FRET measurements corresponding to lower calcium concentrations compared to the wild type strain) that the PE15/PPE20 proteins are involved in cellular calcium import, but do not appear to import magnesium. All phenotypes could be restored to the behavior of wildtype Mtb by complementing the KO strain with pe15/ppe20.

The manuscript is clearly written and easy to follow. The authors combined molecular biology (RNA-seq), biochemistry (proteins purification), biophysics (FRET) and microbiology (knockout generation, in vivo measurements) to reach their conclusions. Overall, the study reports novel and interesting data and as such is of high interest for the mycobacterial research community. However, some of the claims have a rather experimental basis, and thus the study needs to be strengthened with further experiments (or statements have to be removed) as outlined below.

Major points:

1. Cellular localization of PE15/PPE20.

The authors do not describe the cellular fractionation method they applied (no mentioning of cellular localization experiments in materials and methods). The same applies to the main text (very superficial description). The authors show some Western blot data in Fig. S3, though the legend is superficial (abbreviations not explained) and the controls with markers for cellular localization appear to be lacking. Further, the authors do not prove that the FLAG-tagged PPE20 is functional.

The authors should extend discussion part of the manuscript. Several proteomic studies did not identify PE15 or PPE20 in the cell wall - doi: 10.1021/pr1005873, doi: 10.1091/mbc.E04-04-0329. At the same time PE15 (but not PPE20) is membrane or membrane-associated protein according to this work: doi: 10.1186/1471-2180-10-132. Quite recent work (https://doi.org/10.1073/pnas.1523321113) showed that PE15/PPE20 are secreted substrates of ESX-3 and these proteins have been found in the culture filtrate. Did authors analyze culture filtrate fraction by Western blotting? 2. Is PE15/PPE20 a channel?

A major claim of the authors is that PE15/PPE20 forms a (specific) channel for Ca2+ and not a porin-like protein that is permeable to a large set of solutes. However, this claim has its main experimental backing that PPE20 (purified alone from the cytosol of E. coli?) binds to Calcium in a (rather weirdly looking) "thermal melting assay" (further comments on these assays, see below). The second experiment supporting this idea is a lack of difference between wt and KO strain of Mtb in an assay that should report Mg2+ transport deficiency (Fig. S3). But here, a positive control of a mutant that is indeed deficient in Mg2+ import (and thus showing a phenotype) is lacking. In conclusion, the experimental basis on the grounds of which the authors claim PE15/PPE20 to be a specific Mg2+ channel is weak. On the other hand, the functional data clearly show a link between PE15/PPE20 and calcium uptake: Hence the data are solid enough to claim that PE15/PPE20 facilitates Ca2+ transport across the mycomembrane. 3. Thermal melting assay.

It is surprising to see that the thermal melting assays was done for PPE20 and PE15 as separately purified proteins. How did you purify PPE20 alone for this assay? It is broadly accepted for PE/PPE proteins that they only can be purified as pairs, including for PE15/PPE20 (https://doi.org/10.1073/pnas.0602606103). As for the cellular localization, the method section falls short in providing relevant information on how PPE20 and PE15 were purified in separate forms (it states they were co-expressed using a pETDuet vector). Further, the thermal melting assay only seemed to give some results for PPE20 alone, and not for PE15. There is no mentioning of the PE15/PPE20 complex in this assay. Further, the results are counter-intuitive, as Ca2+ addition leads to more precipitation at higher temperatures (and it does seem to weaken the stability of PPE20 instead of stabilizing it). How can the authors be sure that the presence of Ca2+ does not simply lead to more protein precipitation (via rather unspecific interactions) at elevated temperatures? Some positive controls with bona fide calcium binding protein in the same thermal melting setup would have helped to clarify this.

If the authors want to stick to their claims regarding Ca2+ binding to PE15/PPE20, they have to perform additional assays (e.g. equilibrium dialysis or ITC) with the entire PE15/PPE20 complex. Further, they have to show that PE15/PPE20 forms a proper oligomeric protein that is membrane bound and reasonably behaved on size exclusion chromatography, when expressed in and purified from E. coli. As it is doubtful that the authors can meet such quality standards, I would recommend to remove all statements regarding Ca2+ binding to PPE20 from the manuscript, as the underlying experiments are of poor quality. 4. RNA-seq data

The authors should include a table with all other identified genes that are potentially involved in calcium homeostasis. This is of interest because the KO strain is still capable of calcium import, hence other Ca2+ transport systems likely exist.

Minor comments:

1. FRET experiments What is the binding affinity of the sensor for calcium?
2. Figure 4D: one would expect a drop in FRET signal after EGTA addition, because this reverts the Ca2+ gradient from out-to-in (thus facilitating calcium flow into the cells) to in-to-out (EGTA actually acting as a sink into which all Ca2+ (also the one from within the cell) would flow). Can the authors explain?
3. The experiments showing outer membrane localization of PE15/PPE20 are very important, but results of these experiments (western-blot and FRET) are shown in supplementary figures. They should be transferred/integrated into the main Figures.
4. Line 166: the authors claim that the assay did not work in 7H9 due to low Ca2+ concentration in this medium. Why did the authors not just add a bit more calcium to show whether this claim holds true?
5. Line 183: more detailed description on cellular fractionation and subsequent anti-FLAG Western needed here.

Referees cross-commenting

We agree with the concerns of reviewer#2 that the role of PDIM and use of detergent should be looked at more closely.

Likewise, the paper would strongly benefit from some further insights into the potential physiological role of PPE20/PE15 in calcium homeostasis.

Significance

Slow-growing mycobacteria like Mtb lack porins. Therefore, it is not clear how nutrients can be transported through the outer membrane. More and more data hint on PE/PPE protein family that can fulfill this function (Wang et al., Science 367, 1147-1151 (2020)). In the current work, the authors show that PE15/PPE20 are involved in calcium transport in Mtb. Mtb is a difficult model organism to work with because of its pathogenicity and slow rate of growth. Therefore, any information on nutrients transport in Mtb is highly appreciable.

The RNA-seq experiments as well as the genetic/functional experiments clearly show that PE15/PPE20 facilitates calcium import in Mtb. The corresponding sections and figures are convincing.

The experimental data attempting to show PE15/PPE20's cellular localization and its interaction with Ca2+ are currently weak, and need to be strengthened.

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Reply to the reviewers

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

This paper demonstrates a link between oxidative stress, lipid biosynthesis, and targeted histone acetylation in fission yeast. In mutant cells with defects in lipid synthesis (cbf11, mga2 lacking transcription factors, and cut6 lacking acetyl-CoA carboxylase), transcripts of a number of genes implicated in resistance to oxidative stress are increased. This is associated with higher levels of H3K9 acetylation and increased tolerance to oxidative stress. These effects are mediated through Sty1, a stress-activated MAP kinase and the transcription factor Atf1.

It is also shown that H3K9 acetylation levels in the promoter region and just downstream of the transcriptional start site are increased in cbf11 mutants (Fig. 5A).

By mutational analysis, the authors implicate the acetyl transferases Mst1 and Gcn5 in this transcriptional effect. Other related acetyl transferases, Hat1, Elp3, Mst2, Rtt109 have been ruled out as main contributors to the dysregulation in unstressed cbf11 mutants. That specific acetyl transferases have been shown to be required is a strength of the investigation.

Major comments:

The hypothesis is put forward in the manuscript that altered acetyl-CoA levels in cbf1 mutants would underlie the dysregulation of genes induced by oxidative stress. Histone acetyl transferases compete for acetyl-CoA with lipid biosynthesis, and so with increased demand for acetyl-CoA underacetylation in the concerned promoters would result - specifically at H3K9. These results do not directly support the hypothesis, on the other hand they are not sufficient to rule it out.

Actually, we view this phenomenon the other way round: We primarily focus on exponentially growing cells, which have substantial demand for fatty acid (FA) production (= high acetyl-CoA consumption). So the level of promoter histone acetylation under these conditions is our baseline, or “normal” state. When FA production is decreased (cbf11 or cut6 mutants; inhibition of FA synthase by cerulenin…), stress gene promoters get *hyper*acetylated. We do not have any data on (or claims about) histone underacetylation compared to the baseline. Nevertheless, we now show that overexpression of Cut6/ACC results in decreased resistance to oxidative stress (Fig. 5C), which is compatible with the notion that increased acetyl-CoA consumption would result in insufficient histone acetylation at stress gene promoters during stress.

Acetyl-CoA levels were measured only in undisturbed cells, and the possibility remains that under oxidative stress there would be changes in acetyl-CoA pools that could explain this apparent contradiction - why did not the authors examine that?

Under oxidative stress, the Sty1 stress MAPK is activated, leading to a massive Atf1-dependent transcription wave, which is also associated with increased SAGA-dependent H3K9 acetylation (PMID: 21515633). This well-studied cellular response, however, is not the main focus of our study. Rather, we found a novel connection between perturbed lipid metabolism and increased expression of stress genes in cells *not challenged* by oxidative stress (i.e. Sty1-Atf1 are not hyperactivated). This is why we only measured acetyl-CoA concentrations in untreated cells.

The authors argue that although the global acetyl-CoA levels are not increased, local concentrations might be altered in a way to permit higher H3K9 acetylation levels at selected promoters. Although a formal possibility, this is rather far-fetched as a small and freely diffusible molecule like acetyl-CoA should quickly equilibrate within one cellular compartment. I think that although the overall relationships that the authors have established between oxidative stress, H3K9 acetylation levels with increased expression, and lipid biosynthesis, are compelling, the role of acetyl-CoA concentrations is not clear and should be de-emphasized.

Interestingly, acetyl-CoA production in the nucleus has been published by several studies (reviewed in PMID: 29174173), suggesting that local acetyl-CoA concentrations (microgradients) within the cell are functionally relevant. We agree that acetyl-CoA is a small molecule which, in theory, should diffuse quickly throughout the nucleocytoplasmic space. However, empirical evidence shows that the lipid synthesis in the cytosol and histone acetylation in the nucleus may not access a uniform nuclear-cytosolic pool of acetyl-CoA (PMID: 28099844, PMID: 28552616). This is related to the fact that the acetyl-CoA sink is large and acetyl-CoA may react with many proteins (i.e. any extra amounts will be consumed rapidly).

Even though we provide strong evidence that HAT activity is critical for the crosstalk between FA synthesis and stress gene expression, we do agree that we have not conclusively established the role of acetyl-CoA in the process. However, we still feel that it is justified to point out acetyl-CoA is a “possible” mediator molecule for the crosstalk in the Results and Discussion sections.

Minor comments:

In many of the bar diagrams, only a borderline statistical significance is indicated (p ~ 0.05) despite seemingly large numerical differences between the means. In the legends it is stated that one-sided Mann-Whitney U tests were used. This is a non-parametric test with low power - would it not have been better to use a t test?

We do agree that the non-parametric Mann-Whitney U test is rather conservative and, therefore, less sensitive for small sample sizes, such as n = 3. Our reason for using this particular test instead of the parametric t-test is that qPCR fold-change values come from a log-normal distribution, which is incompatible with t-test (requires normal distribution of data). Importantly, using conservative statistical testing does not invalidate our conclusions.

What do the error bars in the diagram show, SEM? If a non-parametric test is used, a parametric measure of variability is irrelevant.

The error bars represent standard deviation (SD). We do not see an issue here as, in our opinion, the visual style of numeric data presentation is independent from any chosen statistical testing methods.

It would be helpful to the reader to indicate directly in the diagram panels what is actually shown, not just "fold change vs ..." In Fig. 1, 2, 4 D and 5 we see mRNA levels, in Fig. 3 chromatin IP.

Done

Reviewer #1 (Significance (Required)):

The paper represents conceptual advances for our understanding of how stress responses, metabolism and transcriptional regulation are linked, although one of the links (acetyl-CoA levels in this case) is tenuous.

This manuscript belongs in a rich literature on stress responses on the gene expression level, mostly from studies in yeast. Potentially, it adds entirely new information on how cellular stress may be mechanistially linked to stress responses.

These results are potentially general and of broad interest to the biological community.

This reviewer is familiar with yeast genetics, stress responses, and quantification of gene expression.

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

As more and more metabolic intermediates are found to also serve as co-factors for epigenetic modifications, it has been widely accepted that regulating the levels of these key metabolites can be an effective way to control nutrient related gene expression. Acetyl-CoA is one of those early examples. Increased acetyl-CoA was shown to promote local acetylation at growth genes (Mol Cell 2011 PMID: 21596309), and ACC deletion funnels more Acetyl-CoA towards histone acetylation reactions and causes global hyperacetylation (Ref 17). However, whether those increased metabolite/co-factor can exert signal-specific effects remains elusive. For instance, although increased acetyl-CoA stimulates the SAGA complex enzymatic activity, it is not clear whether it also causes SAGA to be targeted to new sites without external cues to induce new transcription factor binding. Does increased acetyl-CoA cause broad hyperacetylation at all inducible genes which are the primary targets for those HAT complexes?

In this manuscript, Princová et al. found that deletion of fatty acid synthesis transcriptional factors Cbf11 and Mga2 increases cell survival under H2O2 induced oxidative stress in S. pombe. They further showed that several stress-related genes increased upon Cbf11 deletion, and H3K9 acetylation at their promotor regions were elevated. They argued that FA-TF deletion may indirectly regulate stress-related genes potentially through influencing Acetyl-CoA level, although they failed to detect significant changes of global Acetyl-CoA levels. While it's interesting to see yet another example of metabolite-mediated gene expression regulation, the current manuscript only made incremental advance towards mechanistic principles of how these co-factors finetune specific gene expression program.

Specific comments:

1. This work showed convincingly that deletion of CBF11 or MGA2 leads to resistance to oxidative stress. However, it provides little mechanistic insight into how deletion of Cbf11 increased the expression of stress response genes and why some HATs are involved but others not (Figure EV5).

We respectfully disagree with the notion that we only provide “little mechanistic insight” into the process whereby FA metabolism affects stress gene expression.

• First, we show that not only deletion of cbf11, but also a very specific manipulation of the rate-limiting FA-producing enzyme (Cut6/ACC; Fig. 4D), or chemical inhibition of FA synthase by cerulenin (new Fig. 4F) all lead to increased stress gene expression. On the other hand, overproduction of Cut6/ACC results in decreased stress gene expression and lower resistance to ox. stress (new Fig. 5B-C). These findings clearly show the specific and tight mutual relationship between FA synthesis and expression of stress genes.

• Second, we show that the DNA-binding activity of Cbf11 is critical for affecting stress gene expression levels, yet Cbf11 does not act as a stress gene repressor.

• Third, we show that, compared to e.g. peroxide treatment, stress gene mRNA levels are only moderately increased upon downregulation of FA synthesis. So the situation can be called stress gene “derepression”. At the same time the major stress-response regulators (Sty1-Atf1, Fig. 2A-C; Pap1, new Fig. 2D-E) are required for the derepression, but, importantly, neither of them shows increased activation compared to unstressed WT cells (Fig. 3A-C). These data suggest a qualitative difference between the two phenomena (canonical stress response vs dysregulation of FA synthesis). Furthermore, they hint at an important role of the chromatin environment.

• Fourth, we show that Gcn5/SAGA and Mst1, but not 4 other HATs, mediate the connection between FA metabolism and stress gene expression (Fig. 5D-E), and we show clear and specific H3K9 hyperacetylation of stress gene promoters in FA metabolism mutants (Fig. 5A), arguing that this is not a general acetylome issue.

• Fifth, we show that the stress genes affected by changes in FA metabolism show unusually high nucleosome (H3) occupancy in their transcribed regions (even in unperturbed WT cells; Fig. 5A bottom panels), which could dictate the observed specificity in regulation.

While we agree that our understanding is not yet complete, we have already described many mechanistic aspects of the link between FA metabolism and stress gene expression.

1. Although in Cbf11 deletion cells, increased resistance to H2O2 is relied upon the Sty1/Atf1 pathway, the authors did not establish a link between lipid synthesis and Atf1 activity because Cbf11 deletion does not affect the phosphorylation of Atf1.

Sty1 and/or Atf1 show non-zero activity even in normal, healthy, unstressed cells. Importantly, Atf1 is bound to many target promoters even in the absence of stress (Fig. 3B; PMID: 20661279, PMID: 28652406). Moreover, Sty1 is actually needed for orderly cell cycle progression (sty1KO cells are elongated, a result of postponed mitotic entry; e.g. PMID:7501024), which we now mention in the Introduction and Discussion. Our point is that Sty1-Atf1 are not hyperactivated under normal conditions - this only happens during major stress insults. Thus, in unstressed cbf11KO cells, stress gene promoters are hyperacetylated, which may facilitate their (Sty1-Atf1 and Pap1-dependent) transcription, without the need for hyperactivation of the stress response regulators. Such increased transcriptional competence of stress promoters is consistent with our findings that upon peroxide treatment stress gene mRNA levels in cbf11KO exceed those in WT (Fig. 1B). We have amended the corresponding section of the Discussion to more clearly explain our conclusions and hypotheses.

1. Cbf11 deletion causes elevated H3K9 acetylation at the promotor regions of a number of stress respond genes, the author did not mention whether demonstrate how lipid synthesis defect causes the hyperacetylation at these promoters.

As discussed in our manuscript, we suggest that following downregulation of FA synthesis, the surplus acetyl-CoA is used by Gcn5 and Mst1 HATs to hyperacetylate stress gene promoters.

1. As all lipid-metabolism mutants show increased stress response, it would helpful to examine whether H2O2 induction of WT cells influence lipid synthesis, thus establish physiological links between FA synthesis and stress response.

We now mention in the Discussion section that, curiously, cut6/ACC mRNA levels are downregulated upon peroxide treatment. However, the significance of this finding is unclear as FA metabolism is strongly regulated at the post-translational level (PMID: 12529438). Unfortunately, we are not in a position to measure changes in metabolic fluxes upon stress. In any case, we believe that such experiments would be outside the scope of the current study.

Beside, fatty acid may be beneficial to fight oxidative stress because they maintain the integrity of cell membrane. What is the potential effect of CBF11 deletion in this aspect? The author may want to discuss it.

The reviewer suggests that higher production of FA would result in higher resistance to oxidative stress. However, our data do not indicate this - we show that under low FA synthesis the stress resistance is actually higher. Nevertheless, we acknowledge in the Discussion that the scenario suggested by the reviewer can occur, for example, in cancer cells which become more resistant to oxidative stress following increased lipid biosynthesis/storage.

1. Since H2O2 treatment also causes change in glucose metabolism including upregulation of glucose transporter Ght5 (PMID: 30782292), it would be enlightening to see if there is a crosstalk between the lipid and glucose metabolisms. Does Ght5 expression increase upon H2O2 treatment in CBF11 deletion strain?

While the topic is interesting, we strongly believe that the relationship between glucose metabolism and stress gene expression is outside the scope of this study.

According to our data used in Fig. 4A, ght5 expression in cbf11KO at 60 min after 0.74 mM H2O2 treatment is downregulated 3-fold.

5 Different H2O2 concentration causes different stress response in pombe: Pap1 and Sty1 mediate responses for low and high H2O2, respectively. For fully activated Sty1 response, the concentration of H2O2, needs to reach 1mM (PMID: 17043891). In this study, the H2O2 concentration ranges from 0.5-1.5mM and Pap1 regulated Ctt1 does show increase upon H2O2 treatment. To test if suppressed lipid synthesis facilitates Sty1 dependent activation, it would be helpful to examine the activation of Pap1 (its nuclear translocation) to eliminate other influences.

We agree with the reviewer. We have now included data on the role of Pap1 in the crosstalk between lipid metabolism and stress gene expression. We show that Pap1 is required for increased expression of gst2 and ctt1 in untreated cbf11KO cells (Fig. 2D). We note that ctt1 is coregulated by both Pap1 and Atf1 (Fig. 2B, D). Also, Pap1 is partially required for H2O2 resistance of cbf11KO cells (Fig. 2E). Importantly, similar to Sty1-Atf, Pap1 is not hyperactivated (no nuclear accumulation) by 10 or 60 min of cerulenin treatment (Fig. 3C), while stress gene expression is upregulated at 60 min in cerulenin (Fig. 4F) and keeps increasing after 120 min (data not shown). These data collectively support our hypothesis that upon decreased FA synthesis, stress gene promoters become more transcription-competent without the requirement for hyperactivation of the corresponding stress gene regulators.

Reviewer #2 (Significance (Required)):

see above

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

This study examines the intriguing phenomenon that perturbation of fatty acid biosynthesis induces expression of stress-response genes by increased intracellular levels of acetyl-CoA and hyperacetylation of histones at the promoters of these genes. Loss of the CSL transcription factor Cbf11 results in induced expression of a subset of stress-response genes in unperturbed conditions and resistance to H2O2. These stress-response genes are not direct targets of Cbf11, but their upregulation is dependent on the Sty1-Atf1 pathway. Similar effects in upregulation of stress-response genes were observed in the cut6 hypomorph and mga2 deletion strain, however no change in global levels of acetyl-Co-A in the former as well as in the cbf11 deletion was detected. The upregulated stress-response genes appear to be linked to increased H3K9 acetylation in their promoters and dependent on the Gcn5 and Mst1 HATs.

The authors present good supportive evidence linking fatty acid biosynthesis to epigenetic regulation of stress response genes potentially mediated by intracellular levels of acetyl-CoA. This is an exciting area and the fission yeast model system is ideal to elucidate the molecular mechanisms behind this process. This is a substantial body of work with state-of-the art functional genomics approaches and LC-MS analysis. The data is of high quality and the manuscript is well written and relatively easy to read. Below are my comments for the manuscript.

It was determined that increased expression of stress-response genes in the cbf11 deletion is dependent on the presence of Sty1, and partially dependent on Atf1. How about Pap1 (or Prr1) - would this transcription factor that is also regulated by Sty1 be involved in the upregulation of the stress-response genes in the cbf11 deletion? Activation of Sty1 and Atf1 by phosphorylation was not observed in unperturbed cbf11 deletion cells which would be expected in the proposed model. This discrepancy was not well explained. Could activation of Sty1/Atf1/Pap1 in unperturbed cbf11 cells be assayed in a different way such as nuclear localization?

As these concerns were also raised by Reviewer 2, to avoid duplication, we kindly ask you to read our detailed responses above. Briefly, we have now included new data clarifying the role of Pap1 in the increased expression of selected stress genes in cbf11KO cells (or when FA synthesis is chemically inhibited) - comment #5 of Reviewer 2 above. Also, we explain why Sty1-Atf1 and/or Pap1 hyperactivation (i.e. above their activity level in untreated WT) is actually not needed in order for decreased FA synthesis to trigger a mild/moderate increase in stress gene expression - comment #2 of Reviewer 2 above. We have now also clarified this issue in the Discussion section.

As for the use of alternative methods for measuring the activation status of Sty1-Atf, we have already provided data from multiple independent and very sensitive methods (western blot, ChIP-qPCR; Fig. 3A-B). Also, it is questionable whether microscopy would be more sensitive than our current methods. Moreover, our H2O2-sensitive reporter does not indicate an increasingly oxidative environment inside cbf11KO cells, quite on the contrary (Fig. 1D).

It would strengthen the model that perturbation of fatty biosynthesis induces expression of stress-response genes and H2O2 resistance if more mutant strains other than cut6 and two of its known regulators were tested. Does the proposed model apply to any deficiency in fatty acid synthesis in general or only those that result in increased levels of acetyl-CoA? For example, would deletion strains of fas1, fas2, lsd90, lcf1, lcf2 or the4 show the same stress response as cut6, mga2, and cbf11 mutants?

The roles of lsd90, lcf1, lcf2 and the4 have been only poorly characterized so far, making it potentially difficult to interpret any stress-related phenotypes of these mutants. However, the role of the fatty acid synthase Fas1/Fas2 complex in FA production is well established. We have therefore inhibited FAS using cerulenin and found that this treatment also leads to increased stress gene expression (Fig. 5F), without causing Pap1 hyperactivation (Fig. 3C). Importantly, fas1/fas2 are not Cbf11 target genes, and FAS inhibition by cerulenin represents an acute intervention, very different from the long-term effects in cbf11/mga2/cut6 mutants.

Also, does overexpression of cut6+ confer sensitivity to H2O2?

Yes, our new data show that ~2-fold overexpression of cut6 both partially abolished the derepression of stress genes in cbf11KO cells (Fig. 5B), and increased sensitivity to H2O2 of WT cells (new Fig. 5C).

The authors hypothesize that induced expression of stress-response genes in the cbf11 deletion and cut6 hypomorph is due to H3K9 hyperacetylation because of increased acetyl-CoA abundance in the cell. However, LC-MS analysis showed no change in global abundance of acetyl-CoA in the cbf11 deletion and cut6 hypomorph although differential levels of acetyl-CoA in the nucleus relative to the rest of the cell cannot be ruled out. The authors mentioned that ppc1-537 and ssp2 null are known to have lower abundance of acetyl-CoA and the latter could suppress the cbf11 deletion-induced gene expression for two of three genes tested by qPCR. Can ppc1-537 also suppress the cbf11 deletion-induced gene expression? Are ppc1-537 and the ssp2 null sensitive to H2O2?

The ppc1-537 mutant is sick and has a growth defect, making it difficult to interpret any findings regarding its survival/resistance phenotype (see a similar issue with the cut6-621 mutant in Fig. 4E). Ssp2/AMPK has a pleiotropic role in the cell and its activity is actually controlled by Sty1-Atf1 under some stress conditions (PMID: 28515144) and the ssp2KO is resistant to osmotic stress (PMID: 28600551). All this makes it potentially difficult to derive reliable conclusions about ppc1 and ssp2. However, our current data on cut6 (ts hypomorph, Pcut6MUT, overexpression) and FAS/cerulenin are derived from precisely targeted and specific interventions, and support the proposed connection between FA synthesis and stress gene expression, and are consistent with the suggested role of acetyl-CoA (and its microgradients) in mediating the connection.

I think Rtt109 is H3K56 specific.

Indeed, H3K56 is the characterized specificity of Rtt109, and we indicate this explicitly in the manuscript. We wanted to make our HAT screen comprehensive since we could not presume which histone or even non-histone acetylation target(s) is involved in lipid metabolism-mediated stress gene expression. Even though we have observed increased H3K9ac (Gcn5/SAGA target), other modifications are likely involved since Mst1 affects stress gene expression in lipid mutants, but Mst1 is not known to target H3K9.

Reviewer #3 (Significance (Required)):

The authors present good supportive evidence linking fatty acid biosynthesis to epigenetic regulation of stress response genes potentially mediated by intracellular levels of acetyl-CoA. This is an exciting area and not all the molecular details have been elucidated in this process. S. pombe is ideal to study this fundamental process and discoveries would be applicable to other eukaryotic study organisms.

My expertise is in eukaryotic gene regulation, molecular genetics and functional genomics, so I am quite qualified to critically review this paper.

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Referee #3

Evidence, reproducibility and clarity

This study examines the intriguing phenomenon that perturbation of fatty acid biosynthesis induces expression of stress-response genes by increased intracellular levels of acetyl-CoA and hyperacetylation of histones at the promoters of these genes. Loss of the CSL transcription factor Cbf11 results in induced expression of a subset of stress-response genes in unperturbed conditions and resistance to H2O2. These stress-response genes are not direct targets of Cbf11, but their upregulation is dependent on the Sty1-Atf1 pathway. Similar effects in upregulation of stress-response genes were observed in the cut6 hypomorph and mga2 deletion strain, however no change in global levels of acetyl-Co-A in the former as well as in the cbf11 deletion was detected. The upregulated stress-response genes appear to be linked to increased H3K9 acetylation in their promoters and dependent on the Gcn5 and Mst1 HATs.

The authors present good supportive evidence linking fatty acid biosynthesis to epigenetic regulation of stress response genes potentially mediated by intracellular levels of acetyl-CoA. This is an exciting area and the fission yeast model system is ideal to elucidate the molecular mechanisms behind this process. This is a substantial body of work with state-of-the art functional genomics approaches and LC-MS analysis. The data is of high quality and the manuscript is well written and relatively easy to read. Below are my comments for the manuscript.

It was determined that increased expression of stress-response genes in the cbf11 deletion is dependent on the presence of Sty1, and partially dependent on Atf1. How about Pap1 (or Prr1) - would this transcription factor that is also regulated by Sty1 be involved in the upregulation of the stress-response genes in the cbf11 deletion? Activation of Sty1 and Atf1 by phosphorylation was not observed in unperturbed cbf11 deletion cells which would be expected in the proposed model. This discrepancy was not well explained. Could activation of Sty1/Atf1/Pap1 in unperturbed cbf11 cells be assayed in a different way such as nuclear localization?

It would strengthen the model that perturbation of fatty biosynthesis induces expression of stress-response genes and H2O2 resistance if more mutant strains other than cut6 and two of its known regulators were tested. Does the proposed model apply to any deficiency in fatty acid synthesis in general or only those that result in increased levels of acetyl-CoA? For example, would deletion strains of fas1, fas2, lsd90, lcf1, lcf2 or the4 show the same stress response as cut6, mga2, and cbf11 mutants? Also, does overexpression of cut6+ confer sensitivity to H2O2?

The authors hypothesize that induced expression of stress-response genes in the cbf11 deletion and cut6 hypomorph is due to H3K9 hyperacetylation because of increased acetyl-CoA abundance in the cell. However, LC-MS analysis showed no change in global abundance of acetyl-CoA in the cbf11 deletion and cut6 hypomorph although differential levels of acetyl-CoA in the nucleus relative to the rest of the cell cannot be ruled out. The authors mentioned that ppc1-537 and ssp2 null are known to have lower abundance of acetyl-CoA and the latter could suppress the cbf11 deletion-induced gene expression for two of three genes tested by qPCR. Can ppc1-537 also suppress the cbf11 deletion-induced gene expression? Are ppc1-537 and the ssp2 null sensitive to H2O2?

I think Rtt109 is H3K56 specific.

Significance

The authors present good supportive evidence linking fatty acid biosynthesis to epigenetic regulation of stress response genes potentially mediated by intracellular levels of acetyl-CoA. This is an exciting area and not all the molecular details have been elucidated in this process. S. pombe is ideal to study this fundamental process and discoveries would be applicable to other eukaryotic study organisms.

My expertise is in eukaryotic gene regulation, molecular genetics and functional genomics, so I am quite qualified to critically review this paper.

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Referee #2

Evidence, reproducibility and clarity

As more and more metabolic intermediates are found to also serve as co-factors for epigenetic modifications, it has been widely accepted that regulating the levels of these key metabolites can be an effective way to control nutrient related gene expression. Acetyl-CoA is one of those early examples. Increased acetyl-CoA was shown to promote local acetylation at growth genes (Mol Cell 2011 PMID: 21596309), and ACC deletion funnels more Acetyl-CoA towards histone acetylation reactions and causes global hyperacetylation (Ref 17). However, whether those increased metabolite/co-factor can exert signal-specific effects remains elusive. For instance, although increased acetyl-CoA stimulates the SAGA complex enzymatic activity, it is not clear whether it also causes SAGA to be targeted to new sites without external cues to induce new transcription factor binding. Does increased acetyl-CoA cause broad hyperacetylation at all inducible genes which are the primary targets for those HAT complexes?

In this manuscript, Princová et al. found that deletion of fatty acid synthesis transcriptional factors Cbf11 and Mga2 increases cell survival under H2O2 induced oxidative stress in S. pombe. They further showed that several stress-related genes increased upon Cbf11 deletion, and H3K9 acetylation at their promotor regions were elevated. They argued that FA-TF deletion may indirectly regulate stress-related genes potentially through influencing Acetyl-CoA level, although they failed to detect significant changes of global Acetyl-CoA levels. While it's interesting to see yet another example of metabolite-mediated gene expression regulation, the current manuscript only made incremental advance towards mechanistic principles of how these co-factors finetune specific gene expression program.

Specific comments:

1. This work showed convincingly that deletion of CBF11 or MGA2 leads to resistance to oxidative stress. However, it provides little mechanistic insight into how deletion of Cbf11 increased the expression of stress response genes and why some HATs are involved but others not (Figure EV5).
2. Although in Cbf11 deletion cells, increased resistance to H2O2 is relied upon the Sty1/Atf1 pathway, the authors did not establish a link between lipid synthesis and Atf1 activity because Cbf11 deletion does not affect the phosphorylation of Atf1.
3. Cbf11 deletion causes elevated H3K9 acetylation at the promotor regions of a number of stress respond genes, the author did not mention whether demonstrate how lipid synthesis defect causes the hyperacetylation at these promoters.
4. As all lipid-metabolism mutants show increased stress response, it would helpful to examine whether H2O2 induction of WT cells influence lipid synthesis, thus establish physiological links between FA synthesis and stress response. Beside, fatty acid may be beneficial to fight oxidative stress because they maintain the integrity of cell membrane. What is the potential effect of CBF11 deletion in this aspect? The author may want to discuss it.
5. Since H2O2 treatment also causes change in glucose metabolism including upregulation of glucose transporter Ght5 (PMID: 30782292), it would be enlightening to see if there is a crosstalk between the lipid and glucose metabolisms. Does Ght5 expression increase upon H2O2 treatment in CBF11 deletion strain? 5 Different H2O2 concentration causes different stress response in pombe: Pap1 and Sty1 mediate responses for low and high H2O2, respectively. For fully activated Sty1 response, the concentration of H2O2, needs to reach 1mM (PMID: 17043891). In this study, the H2O2 concentration ranges from 0.5-1.5mM and Pap1 regulated Ctt1 does show increase upon H2O2 treatment. To test if suppressed lipid synthesis facilitates Sty1 dependent activation, it would be helpful to examine the activation of Pap1 (its nuclear translocation) to eliminate other influences.

Significance

see above

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Referee #1

Evidence, reproducibility and clarity

This paper demonstrates a link between oxidative stress, lipid biosynthesis, and targeted histone acetylation in fission yeast. In mutant cells with defects in lipid synthesis (cbf11, mga2 lacking transcription factors, and cut6 lacking acetyl-CoA carboxylase), transcripts of a number of genes implicated in resistance to oxidative stress are increased. This is associated with higher levels of H3K9 acetylation and increased tolerance to oxidative stress. These effects are mediated through Sty1, a stress-activated MAP kinase and the transcription factor Atf1.

It is also shown that H3K9 acetylation levels in the promoter region and just downstream of the transcriptional start site are increased in cbf11 mutants (Fig. 5A).

By mutational analysis, the authors implicate the acetyl transferases Mst1 and Gcn5 in this transcriptional effect. Other related acetyl transferases, Hat1, Elp3, Mst2, Rtt109 have been ruled out as main contributors to the dysregulation in unstressed cbf11 mutants. That specific acetyl transferases have been shown to be required is a strength of the investigation.

Major comments:

The hypothesis is put forward in the manuscript that altered acetyl-CoA levels in cbf1 mutants would underlie the dysregulation of genes induced by oxidative stress. Histone acetyl transferases compete for acetyl-CoA with lipid biosynthesis, and so with increased demand for acetyl-CoA underacetylation in the concerned promoters would result - specifically at H3K9.

These results do not directly support the hypothesis, on the other hand they are not sufficient to rule it out. Acetyl-CoA levels were measured only in undisturbed cells, and the possibility remains that under oxidative stress there would be changes in acetyl-CoA pools that could explain this apparent contradiction - why did not the authors examine that?

The authors argue that although the global acetyl-CoA levels are not increased, local concentrations might be altered in a way to permit higher H3K9 acetylation levels at selected promoters. Although a formal possibility, this is rather far-fetched as a small and freely diffusible molecule like acetyl-CoA should quickly equilibrate within one cellular compartment. I think that although the overall relationships that the authors have established between oxidative stress, H3K9 acetylation levels with increased expression, and lipid biosynthesis, are compelling, the role of acetyl-CoA concentrations is not clear and should be de-emphasized.

Minor comments:

In many of the bar diagrams, only a borderline statistical significance is indicated (p ~ 0.05) despite seemingly large numerical differences between the means. In the legends it is stated that one-sided Mann-Whitney U tests were used. This is a non-parametric test with low power - would it not have been better to use a t test? What do the error bars in the diagram show, SEM? If a non-parametric test is used, a parametric measure of variability is irrelevant.

It would be helpful to the reader to indicate directly in the diagram panels what is actually shown, not just "fold change vs ..." In Fig. 1, 2, 4 D and 5 we see mRNA levels, in Fig. 3 chromatin IP.

Significance

The paper represents conceptual advances for our understanding of how stress responses, metabolism and transcriptional regulation are linked, although one of the links (acetyl-CoA levels in this case) is tenuous.

This manuscript belongs in a rich literature on stress responses on the gene expression level, mostly from studies in yeast. Potentially, it adds entirely new information on how cellular stress may be mechanistially linked to stress responses.

These results are potentially general and of broad interest to the biological community.

This reviewer is familiar with yeast genetics, stress responses, and quantification of gene expression.

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Reply to the reviewers

1. General Statements

We are grateful to the reviewers for their time and expertise, and we have addressed all points they raised as detailed in our point-to-point response and highlighted the changes in the main manuscript. We have addressed all points raised by the reviewers and elaborated how this was done in a point-by-point reply. There are two new tables and a new supplementary figure. The figures and the text have been reshaped, according to the suggestions.

  We are looking forward to your reply.

   Best regards, Yannick Schwab and Anna M Steyer

2. Point-by-point description of the revisions

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

**Summary:**

Serra Lleti et al. report a new software (CLEMSite) for fully automated FIB-SEM imaging based on locations identified beforehand in LM. The authors have implemented routines for automatically identifying common reference patterns and an automated FIB-SEM quality control. This allows autonomous data acquisition of multiple locations distributed over the entire sample dish. CLEMSite has been developed as a powerful tool for fast and highly efficient screening of morphological variations.

**Major comments:**

The performance of CLEMSite has been demonstrated by the authors with two typical biological example applications. The stated performance parameters such as correlation precision and reproducibility are highly convincing and supported by the presented data. The authors give detailed information on their workflow and how on to use CLEMSite, which should allow other researchers to implement this for their own applications. The only comment I have in this regard, and I might have overlooked it, but how will CLEMSite be made available to the scientific community?

Reply 1.1

We would like to warmly thank Reviewer #1 for their very supportive feedback. It is important to us to share our work with the community. Our prime intention is to offer CLEMSite as a proof of concept that has been demonstrated on a specific instrument, thus linked to a company (Zeiss). Because we are convinced this code can be adapted to other APIs provided by other vendors, we made it fully available via a Github repository (https://github.com/josemiserra/CLEMSite).

To make this more visible in the manuscript, we have modified this sentence to the first paragraph of the Results section:

“To control the FIB-SEM microscope, CLEMSite-EM interfaces commercial software (SmartSEM and ZEISS Atlas 5 from Carl Zeiss Microscopy GmbH) via a specific Application programming interface (API) provided by Zeiss. CLEMSite code is openly accessible and free to download from a Github repository (https://github.com/josemiserra/CLEMSite ).”

**Minor comments:**

The author mention that decreasing the z-resolution to 200 nm steps was critical to achieve high throughput. For applications that require higher resolution: is the only disadvantage a longer data acquisition time or are there also other limitations?

Reply 1.2:

Reviewer #1 is right, we have designed CLEMSite as a screening tool, where we emphasize the number of cells versus the resolution at which each cell is acquired. By acquiring images every 200 nm, we are gaining speed, but also stability. We have indeed noticed that below 50 nm, on occasions the beginning of the acquisition is not stable enough (the milling has to hit the front of the cross-section at view precisely), and it requires manual intervention to retract/advance the milling. In addition, to gain time in our current workflow, we have opted to not cover the region of interest with a platinum protective layer, which has no consequences when imaging at larger z steps because the overall time spent on one cell is very short. At higher z resolution regimes though, a non-protected block surface is inevitably damaged during the successive numerous mill & view cycles. We have added one sentence in the Methods section to make this point clearer.

“Note that to gain time in the preparation process for a run, we have not covered the ROI with a platinum protective layer and alternatively we increased the thickness of the gold coating of the full sample. In such cases, only low z-resolution acquisition is possible, as acquiring at a higher resolution would require sputtering of the sample surface.”

Finally, we may argue that if an experiment requires high-resolution acquisition, the time overhead spent to switch from one cell to the next (a few minutes) is not significant anymore relative to the time spent to acquire one cell (from several days to weeks). In such cases, automation for multi-site acquisitions would lose its relevance.

I would assume that locating the finer structural details in a much larger data set might also introduce additional challenges in the data analysis pipeline.

Reply 1.3:

We fully agree with Reviewer #1. In this proof of concept study though, we are not addressing the image analysis part but assess ultrastructural phenotypes manually using established stereology protocols. At the image resolution that we are using, our analysis is restricted to features such as volumes, surfaces, number of rather large organelles. Finer details, such as microtubules or fine contact sites between organelles would require a higher resolution, and indeed very likely other means to extract the morphometric data. State-of-the-art image analysis of isotropic FIB-SEM datasets is based on computer vision/machine learning. With such tools, the analysis of fine details is indeed accessible with very high accuracy, but at the cost of the throughput, at least for now as already mentioned in the Discussion section of the paper.

In Table 1 in the supplements, the units are missing for the targeting positions. On page 4, 4th line from the bottom, there is a typo in "reaaching a global targeting...".

Reply 1.4

We thank Reviewer#1 for their thorough inspection of the paper. We have corrected it accordingly.

Reviewer #1 (Significance (Required)):

With CLEMSite, the authors present a powerful new software tool for the FIB-SEM imaging community. The high level of automation allows high throughput data acquisition with minimal user interaction. To my knowledge, this is the first software that fully automatically recognises reference features and is able to run fully autonomously after points of interest have been selected in FM. This high throughput screening tool for FIB-SEM imaging would make a substantial technical contribution to the field of cellular imaging. My own expertise lies in the field of technical developments for CLEM and super-resolution FM. I am not able to judge the biological content of the manuscript.

We would like to thank Reviewer #1 for their constructive and encouraging feedback.

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

Review on "CLEMsite, a software for automated phenotypic screens using light microscopy and FIB-SEM" by Serra Lleti et al. The manuscript describes a toolset to correlate LM data with automated FIB-SEM of selected regions of interest. This allows 3D correlative microscopy of multiple adherent cells from a single resin block. This allows much needed high throughput in CLEM analysis to become quantitative. Two applications on Golgi apparatus morphology are shown.

**Major questions:**

-The software has been developed in collaboration between Zeiss/ Fibics in collaboration with academic groups and will only function on Zeiss SEMs that have the proper software. Thus, if I understand correct, it will not be of generic use and a more appropriate title would be 'CLEMsite, a software for automated phenotypic screens using light microscopy and Zeiss FIB-SEM"

Reply 2.1.

Reviewer #2 is right about the fact that our work was done on a Zeiss microscope and in CLEMSite’s current version, it would only work with that model, including firmware and software. As already phrased in the manuscript, we would like to stress our work is a proof-of-concept. For example, we wrote in the introduction that CLEMSite is a “software prototype”. We’ve also made clearer the links to Zeiss in the first paragraph of the Results (see also answer to reviewer 1.1)

CLEMSite is by no means designed to become an integrated part of current or future Zeiss microscopes. On the contrary, we have designed the software as an independent unit. All the parts of the software that are sending commands to the Zeiss API are indeed customized to that brand, but other functions are stand-alone units. In particular, the correlation strategy is independent of the microscope type and can be used generically. Similarly, the principles that we developed for finding the FIB-SEM coincidence point, or for selecting features-rich regions to perform the AFAS function would be valid whichever microscope model would be used.

For these reasons, we would prefer to avoid mentioning Zeiss already in the title of the manuscript.

• How is the described approach using FIB-SEM advantageous compared to methods like Serial Block-face EM (SBEM) and array tomography using serial section where larger fields of multiple cells can be imaged? Especially because the axial resolution was set to 200 nm and discussed as essential for the throughput speed.

Reply 2.2.

This is a very important point that we tried to bring across in the introduction of the manuscript. Other volume EM methods, such as SBEM and AT, like conventional TEM, require an ultramicrotome to produce thin sections (AT and TEM) or to remove the top layers from the resin block (SBEM). This inevitably requires trimming large specimens in order to accommodate the dimensions of the diamond knife used in the associated microtomes. FIB-SEMs does not have such limitations and selected volumes can be imaged from samples of any size, providing they fit in the chamber of the microscope. In our case, we were screening cells growing on a 1 cm2 surface area, which is already beyond what standard diamond knives can process. We would even argue that larger surfaces are at CLEMSite reach, but we have not tested this.

• Is the data FAIR available?

Reply 2.3

It is one of EMBL’s ambitions to make all data as FAIR as possible. For this study, we saved all the raw images and their corresponding embedded metadata as they came from the original software (ATLAS 5, Fibics for the SEM images and LAS X, Leica microsystems for the confocal images). The images published in this manuscript will be deposited on the EMPIAR data repository upon acceptance. The raw data and unpublished data, due to their size, will be fully available upon request to the authors. Additionally, their data is specifically generated for the correlation workflow, which is stored together with the image information as separated files. To store the information of logs we used text files, for intercommunication between processes, JSON, and XML to store coordinates in a readable format. As far as we know, there is no standard FAIR protocol yet that describes CLEM workflows in microscopy. We made our best possible efforts to archive our data in an understandable folder architecture, with detailed information on how to navigate through it, such that we are confident that our data could be mined by others in the future, thus reaching the goals of the FAIR charter.

• How is CLEMsite available? Is the code public or for sale?

Reply 2.4

It is important to us that our proof-of-concept can be used or adapted by others in the future. For this reason, we are sharing the full code that was developed for CLEMSite - See Reply 1.1 for further details.

**Other comments:**

• Can you comment on the flexibility of this method? It is described as a flexible method, but only HeLa cells (quite flat cells) and Golgi apparatus targeting was used. What about different cell types and what about targets with a less obvious EM morphology?

Reply 2.5

It is correct that we have demonstrated our workflow only on Hela cells which present a more or less homogeneous topology. Yet our workflow is flexible when it comes to the dimensions of the region of interest and the acquisition field of view, and can accommodate a wide range of cell shapes, as long as they adhere to a culture substrate. Dimensions of ROI and FOV can be adapted in the CLEMSite interface as described in Supplementary Figure 4. Following reviewer 2 question, we realize that this feature may not appear clearly and we have modified the corresponding section of the Result:

“The dimensions of the image stack, as well as the z resolution are set when initializing the run, via the CLEMSite interface (Supplementary Figure 4). Whilst every cell of one run can be acquired with the same recipe (as defined in ZEISS Atlas 5: sample preparation, total volume to be acquired, slice thickness and FIB currents applied at each step), CLEMSite-EM also offers individual definition of recipes, allowing a per cell adaptation of the shape or volume (Supplementary Fig. 4a).”

Changing the ROI size would thus accommodate the surface occupancy of a cell (in the plane parallel to the culture substrate) and changing the FOV would accommodate the cell’s height.

The morphology of the cell as it appears in the EM (SESI) does not alter the targeting strategy, since we are solely relying on the correlation, which means that the position of the target cell is extracted from the light microscopy images and the coordinate system provided by the gridded coverslip. Even if the cells were invisible at the surface of the resin block when inspected in the SEM, CLEMSite would still navigate to the proper region and create an image stack by FIB-SEM imaging.

• For EM acquisition ZEISS smartSEM with ATLAS was used. LM was recorded with a microscope from a different vendor. Can the software be used regardless of microscope type?

Reply 2.6

Yes, the correlation is based on collecting the stage coordinates from the light microscope, and on analyzing the images from the various magnifications and channels. This information can be obtained by most microscope types, but it might involve minor adaptations regarding the specific brand of a microscope (e.g. changes in the coordinate system of the stage used or the naming of the channels).

• Create less variation in the size of scale bars.

Reply 2.7

We have modified all figures to take this comment into account and thank Reviewer #2 for a good suggestion.

• M&M: High-resolution light microscopy: Why call this 'high resolution'?

Reply 2.8

We used this term to differentiate, in the feedback microscopy setup, the first stage where images are acquired at low magnification from the images acquired at high magnification. We agree that the term is misleading, so we decided to update the manuscript and change the term high resolution by higher magnification (the second stage in feedback microscopy).

Specs given seem randomly chosen: For example objective magnification yes, NA not; excitation wavelength yes, emission not.

Reply 2.9

We thank Reviewer #2 for spotting these missing details. We have edited the method section to add the NA and the emission wavelengths.

Reviewer #2 (Significance (Required)): See above: This depends on the availability of code, as well as the usability in FIB-SEM that is not based on Zeiss.

Reply 2.10

We hope our answers have addressed these concerns. When the code is indeed fully available, we can not at this stage presume of the transferability of CLEMSite to microscope from other manufacturers. Yet we would like to stress once more that our main aim is to demonstrate a proof of concept.

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

**Summary:**

Schwab and coworkers present an automation software for correlative light and electron microscopy (CLEM) to acquire high-resolution SEM volume datasets at room temperature. This automation enables large-scale data collection and morphometric analysis of cell phenotypes. The paper is overall well written, but often assumes a lot of prior knowledge of the workflow, which might not be present in a general audience or for newcomers to the technique. This is also seen in the insufficient labeling and explanation of the figures. They seem a bit like presentation slides, which could be well understood with the help of the presenter/narrator, but alone lack a lot of information (see more specific comments below).

**Major Comments (in no particular order):**

• Final accuracy of ~ 5 µm ... is this really sufficient? Given that the size of many mammalian cells is ~10-15 µm, this is still a HUGE error. Of course, there is a tradeoff between throughput and accuracy, the area covered and speed. Nonetheless, this means a serious limitation in terms of the kind of targets / biological questions that can be addressed with this technique! (Especially in the context of "rare events") This should be discussed in more detail. Reply 3.1

We thank reviewer #3 for their constructive criticism of the work. Indeed, our final accuracy is 5 µm at best, which may at first glance appear as a disappointing value. This accuracy is the consequence of a couple of strategic decisions that we have made in designing the workflow, which will be further explained below. We have chosen to constantly opt for a large field of view that would be larger than the average cell size, thus mitigating the potential 5 µm offset in targeting. In our hands, this yielded satisfying results, yet we agree that a higher targeting precision would allow narrower fields of view and potentially an even increased throughput.

Our correlation strategy fully relies on the coordinate system built from the gridded pattern embossed at the surface of the culture dishes. The precision of CLEMSite automated targeting thus relies on i) its ability to properly detect the grid edges, both at the LM and at the ME, and ii) on the mesh size of the grid. To ensure a wide range of applications, we decided to design CLEMSite on commercial culture dishes, of which the MatTek gridded culture dishes appeared the most convenient, for each grid square presented a unique alphanumeric ID together with a relatively large and flat surface area to accommodate a large number of cells away from the grid pattern. Whilst such dishes showed a topology that satisfied our first criteria, the grid spacing was 600 µm. A smaller mesh size would have undoubtedly resulted in higher precision in the targeting but at the expense of losing free areas. Other commercial dishes with denser meshes unfortunately would not have ID engraved directly inside every square or we experienced difficulties in reproducibility during the sample preparation process to detach the glass from the resin block.

We also have excluded the option to design our own grids, which would have created another dependency for potential users from other laboratories.

Another possibility for targeting would be to register the fluorescence maps to the shapes of the cell as visible in the resin block. Adherent cells can be detected in the SEM if high energies are used to scan the surface of the blocks, and also if the block is not coated with a too thick layer of gold. In our experience, switching between voltages for acquiring such overviews and low voltages for acquiring FIB-SEM stacks is another source of imprecision and doesn’t improve the targeting in very confluent areas. Another interesting idea, as shown in Hoffman et al 2020, would be to scan the embedded samples by X-ray prior the FIB-SEM targeting, but not only this would imply that high-end X-ray machines would be available for such tasks, but would still require landmarks to register the X-ray maps to the SEM overviews. This would potentially yield a higher accuracy, but we have opted for the gridded substrates, judged more accessible to a large number of laboratories.

We tried to explain such a choice in the discussion, by adding this sentence in the description :

“Detection of local landmarks imprinted in the culture substrate enables automated correlation and targeting with a 5 µm accuracy. We estimate that this number could still be improved by customizing a gridded substrate with a smaller mesh size, as landmarks would be much closer to the targets. The detection algorithm we developed could be extrapolated to other customized dishes or commercial substrates for cell culture in SEM samples41. An advantage of using local landmarks for the correlation is that they mitigate the impact of sample surface defects or optical aberration across long distances. Alternatively, targeting individual cells with a FIB-SEM has been achieved by mapping the resin embedded cells with microscopic X-ray computed tomography44. We speculate that such tools could be an alternative to a gridded substrate, yet cannot predict its adaptability to large resin blocks such as the ones we used in this study. “

• Given that the whole point of the paper is "large scale automation", I would have preferred a few more examples/higher n-count. A comment on which type of targets the authors envision/have validated would be nice (also in the context of the limitation in accuracy). Reply 3.2

To our best knowledge, no one has ever imaged multiple cells automatically. So even 5 in a row is a high number.

In addition to this, we added an extra paragraph in the discussion.

“We believe that other research questions could benefit from this type of screening. As an example, the 2021 Human Protein Atlas Image Classification competition61 managed to classify multiple organelles of individual cells in fluorescence microscopy. Such machine learning models could be used to find rare events or particularly interesting phenotypes. In another example, in host-pathogen interactions, early infected cells might start to display a recognizable phenotype in a small subpopulation of cells62. In both cases, those marked cells could be used to establish a FIB-SEM screening to discover new morphological differences at the micrometer level.

To expand the applicability of these screenings beyond the proof-of-concept here presented, we propose two directions of improvement. First, by acquiring smaller enclosed volumes with isotropic resolution, we could target area-delimited organelles, like centrioles21. In this case, the full cell volume is neglected in favor of a small portion of it, but with higher z resolution. At the software level, that would require improving targeting accuracy by using smaller grids and extending the maps to 3D coordinates. 3D registration against a light microscopy Z-stack would considerably help to constrain the field of view during acquisition, thus reducing the imaging time and keeping the field of view position during tracking. At the instrument level, this would require, first, stabilizing the ion beam before the critical region is acquired, to compensate for the change between high currents for milling and fine currents for sectioning. Second, to make sure that the fine current beam hits exactly the front face of the milled cross-section, and then prevent milling artifacts. Finally, the second direction is to increase the number of samples acquired per session. That would imply ion beams that automatically reheat the Gallium source when it is exhausted (like proposed in Xu et al. 60), with faster algorithms for autofocus and autostigmatism in SEM.”

• It should be mentioned somewhere that "commercial dishes or coverslips" contain an imprinted grid pattern with numbers and letters to locate specific squares. [Again: probably clear to "aficionados" of the technique but totally unclear to newcomers/outsiders] Reply 3.3

We have added an explanation of the layout of the coordinate system in the part of the correlation strategy and the methods section “gridded dish with numbers and letters' to explain the correlation and targeting strategy better.

• "It is important to keep the initial number high in order to compensate for the loss of targets" - what % of targets is lost exactly in the final step (FIB-SEM imaging)? The 10 cells out of 35 (29%!) that were not "of sufficient quality for further downstream analysis", were they lost/discarded because of problems in the automation (e.g. autofocus/tracking failure) or for other reasons (e.g. preservation of the cells during fixation/embedding)? Reply 3.4 In the main text we decide to explain the process of filtering better. We have added a supplementary figure showing different causes for problems of coordinate system detection due to scratches, cracks, or dirt. None of the cells in the study were discarded due to bad preservation, but the system being a proof of concept, we dealt with multiple difficulties that forced us to filter the acquired stacks for getting the ones showing the best quality. We also added supplementary material (Sup. Tables 3 and 4 with explanation) about the possible causes of cell losses during different experiments.

• "One essential paradigm shift for increasing the acquisition throughput is the decision to decrease the resolution in the z-dimension, thus prioritizing the speed of acquisition and ultimately the total number of cells acquired in one run.". Surely, reducing z-resolution is an obvious way to speed up acquisition times. But this is not tied to the use of this software and obviously comes at a price ... this has been discussed before and is nothing novel. Hence "paradigm shift" might be a bit too strong. I however fully agree with CLEMSite's potential as a screening tool. Could a "high resolution" (isotropic) mode not be implemented, too? [then it would be up to the user to decide what to prioritize - throughput or resolution] Reply 3.5

We have replaced the word “paradigm shift” with “original strategy”. It is indeed up to the user to decide if higher z resolution or higher speed should be achieved by setting up different recipes.

Additionally, we direct the reviewer to read Reply 1.2.

• There is no mentioning of why this specific hardware was used. Are there any limitations that currently restrict the approach to Zeiss machines? Any plans supporting other vendors? Of course, there are always certain benefits with certain instruments. Or just simply no others were available... A comment on which part was performed by/at Zeiss and which in the labs would be useful to understand specific contributions. (Since a conflict of interest statement seems missing). Reply 3.6

The original plan was to set up a proof-of-principle study developing a program that is fully open source. We created an interface, which could plug any control via proprietary API, by simply adapting commands from the API to our interface. The idea is very similar to what is done in light microscopy open-source controllers, like the Micropilot software (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3086017/).

That interface would be the place where to modify the software and add the external API and requires only that such API can be used with a .NET framework in C#. The programmer would have to modify only the following file:

https://github.com/josemiserra/CLEMSite/blob/master/CLEMSiteServer/TestApp/AtlasCom.cs.

We expect that FIB-SEMs are very similar across companies, at least in basic functionality (get images, get positions, mill execution for trench digging with a recipe file, ...). We thus believe our software could be adapted to other vendors. As an example, we used the Fibics API, but we could also program the same functionality with the Zeiss API to achieve the same goal.

Zeiss’s contribution to the project was i) providing a system during the initial phase of the project, and allocating time with programmers from FIBICS to help to provide the control API to be used by CLEMSite.

All experiments were performed at the European Molecular Biology Laboratory or Max-Planck Institute of Experimental Medicine.

**Figures:**

Figures should be improved. They often contain too little information to understand the concepts/results discussed and there's lots of white space. The legends should be improved accordingly. In general, a more concise and structured figure design could go a long way of improving the quality of the manuscript. Please find a few suggestions (for the main figures) below (but the same should be applied to the supporting figures):

Reply 3.7

We thank the reviewer for the suggestions on the figures in general. We have revisited all the figures and made corresponding changes as highlighted below.

Fig. 1: While I believe it is clear to me what each scheme is supposed to represent, someone less immersed in this topic (or just entering the field) may have problems navigating the figure. For example: what are all the different letters and numbers? What's the blue box with the trapezoid ("EM targets" - it may become clear later, but here it is not), what are the blue and the red arrowhead, respectively (I suppose EM and focused ion beam?). This should be improved and labeled accordingly.

We have addressed the queries by explaining the figure more explicitly in the legend (e.g. blue box, blue and red arrowhead). We have added i, ii, iii to separate b into subsections and adjusted the text accordingly.

Fig. 2: Again, a lot of annotation is missing. E.g. what is the 3rd insert in b exactly (edge-detection? After CNN identification?)? For most of the figure, yellow squares are used to indicate the zoom-in region, why not for b) 1st row? With the "zoo" of scale bars, wouldn't it make sense to either always show the same bar (e.g. 200 µm), or scale the images so things become more comparable? In this regard: a) 2nd column and e) 1st column represent the same FOV. Why are they shown with different magnification/cropping?

Reply 3.8

The scale bars have been homogenized when possible, in the case of b the image was zoomed to match a (first image in both cases). A yellow box was added for the zoom in b as suggested. We added descriptions in the figure legend.

Fig. 3: a) The procedure is well described in the legend, but no motivation is given in the text, why this is necessary. c) There's some floating density in the white space. Is this due to thresholding?

Already explained in figure legend.

Reply 3.9

We have adapted the text in the main manuscript to explain better that the coincidence point is normally found manually and for a routine with as little as possible intervention by an operator this had to be automated. We have also explained figure 3c more in the figure legend.

“The following steps, usually performed by a trained human operator, are triggered autonomously: localization of the coincidence point, needed to bring the FIB and SEM beams to point at the same position (Fig. 3a); milling of the trench to expose the imaging surface, detection of the trench to ensure a well-positioned imaging field of view (FOV) (Fig. 3b); automated detection of image features in the imaged surface needed to find an optimal location for the initial autofocus and autostigmation (AFAS) (Fig. 3c); and finally the stack acquisition (Fig. 3d).”

Fig. 4) Again, description/labeling of the figure is poor. E.g. what are the red outlines present in c) row 1-3 (but missing in row 4; why?)? [presumably these are the siRNA spots?] Is there any reason this figure could not be further subdivided into d), e), f) etc? As it stands, a lot of additional descriptors ("second from the left", "two images on the right") are necessary while a simple call to a), b), c) would be much easier...

Reply 3.10

We have more precisely described the siRNA spots in the legend more explicitly and have added headings to divide part c into a grid rather than adding letters/numbers to subdivide to make the figure more clear.

Fig. 5) Additional labeling (a,b,c...) could be helpful here, too. While intuitively I would assume that blue = DAPI and green = GFP, these things should be labeled or described in the legend. Especially in the 3D rendering it is quite unclear what is being portrayed. Is this an overlay of a FIB/SEM segmentation with the confocal 3D-data?

Reply 3.11

We have added headings to subdivide the images in b and explanations in the legends to explain the color-dye relation (blue is DAPI).

**Minor:**

The first element in the filtered list can thus be stored for the subsequent application of autofocus and autostigmation procedures (AFAS) (Supplementary Fig. 3c). [technically this has been defined before]

Reply 3.12

All typos and grammar-related issues have been addressed in the following ways:

A transformation is computed to register together the LM list and EM landmarks list, ...

“A transformation is computed to register the positions from the LM and the EM landmarks list, ... “

“The FOV is changed from a 305 μm by 305 μm, used for the detection of the trench, to a 36.4 μm by 36.4 μm in the exposed cross-section and an image of that cross-section is taken for analysis (Fig. 3c).”

The sample is positioned at the target coordinates of the first cell, and the Multisite module performs the coincidence point alignment of both the electron and ion beams (Fig. 3a and Supplementary Fig. 2a).

Reviewer #3 (Significance (Required)):

**Significance:**

It is clear that the kind of automation outlined here is necessary to elevate correlative SEM volume imaging to a "high-throughput" technique, which could become valuable for many biological questions. CLEMSite offers a valid technical solution and appears to be a solid implementation of the traditional/manual workflow. However, its presentation needs to be improved before we can support publication.

Reply 3.13

We have worked on different aspects of the presentation, rearranged the figures, and extended figure legends and hope this meets the reviewer’s expectations.

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

Summary:

Schwab and coworkers present an automation software for correlative light and electron microscopy (CLEM) to acquire high-resolution SEM volume datasets at room temperature. This automation enables large-scale data collection and morphometric analysis of cell phenotypes.

The paper is overall well written, but often assumes a lot of prior knowledge of the workflow, which might not be present in a general audience or for newcomers to the technique. This is also seen in the insufficient labeling and explanation of the figures. They seem a bit like presentation slides, which could be well understood with the help of the presenter/narrator, but alone lack a lot of information (see more specific comments below).

Major Comments (in no particular order):

• Final accuracy of ~ 5 µm ... is this really sufficient? Given that the size of many mammalian cells is ~10-15 µm, this is still a HUGE error. Of course, there is a tradeoff between throughput and accuracy, the area covered and speed. Nonetheless, this means a serious limitation in terms of the kind of targets / biological questions that can be addressed with this technique! (Especially in the context of "rare events") This should be discussed in more detail.

• Given that the whole point of the paper is "large scale automation", I would have preferred a few more examples/higher n-count. A comment on which type of targets the authors envision/have validated would be nice (also in the context of the limitation in accuracy).

• It should be mentioned somewhere that "commercial dishes or coverslips" contain an imprinted grid pattern with numbers and letters to locate specific squares. [Again: probably clear to "aficionados" of the technique but totally unclear to newcomers/outsiders]

• "It is important to keep the initial number high in order to compensate for the loss of targets" - what % of targets is lost exactly in the final step (FIB-SEM imaging)? The 10 cells out of 35 (29%!) that were not "of sufficient quality for further downstream analysis", were they lost/discarded because of problems in the automation (e.g. autofocus/tracking failure) or for other reasons (e.g. preservation of the cells during fixation/embedding)?

• "One essential paradigm shift for increasing the acquisition throughput is the decision to decrease the resolution in the z-dimension, thus prioritizing the speed of acquisition and ultimately the total number of cells acquired in one run.". Surely, reducing z-resolution is an obvious way to speed up acquisition times. But this is not tied to the use of this software and obviously comes at a price ... this has been discussed before and is nothing novel. Hence "paradigm shift" might be a bit too strong. I however fully agree with CLEMSite's potential as a screening tool. Could a "high resolution" (isotropic) mode not be implemented, too? [then it would be up to the user to decide what to prioritize - throughput or resolution]

• There is no mentioning of why this specific hardware was used. Are there any limitations that currently restrict the approach to Zeiss machines? Any plans supporting other vendors? Of course, there are always certain benefits with certain instruments. Or just simply no others were available... A comment on which part was performed by/at Zeiss and which in the labs would be useful to understand specific contributions. (Since a conflict of interest statement seems missing).

Figures:

Figures should be improved. They often contain too little information to understand the concepts/results discussed and there's lots of white space. The legends should be improved accordingly. In general, a more concise and structured figure design could go a long way of improving the quality of the manuscript. Please find a few suggestions (for the main figures) below (but the same should be applied to the supporting figures):

Fig. 1: While I believe it is clear to me what each scheme is supposed to represent, someone less immersed in this topic (or just entering the field) may have problems navigating the figure. For example: what are all the different letters and numbers? What's the blue box with the trapezoid ("EM targets" - it may become clear later, but here it is not), what are the blue and the red arrowhead, respectively (I suppose EM and focused ion beam?). This should be improved and labeled accordingly.

Fig. 2: Again, a lot of annotation is missing. E.g. what is the 3rd insert in b exactly (edge-detection? After CNN identification?)? For most of the figure, yellow squares are used to indicate the zoom-in region, why not for b) 1st row? With the "zoo" of scale bars, wouldn't it make sense to either always show the same bar (e.g. 200 µm), or scale the images so things become more comparable? In this regard: a) 2nd column and e) 1st column represent the same FOV. Why are they shown with different magnification/cropping?

Fig. 3: a) The procedure is well described in the legend, but no motivation is given in the text, why this is necessary. c) There's some floating density in the white space. Is this due to thresholding?

Fig. 4) Again, description/labeling of the figure is poor. E.g. what are the red outlines present in c) row 1-3 (but missing in row 4; why?)? [presumably these are the siRNA spots?] Is there any reason this figure could not be further sub-divided into d), e), f) etc? As it stands, a lot of additional descriptors ("second from the left", "two images on the right") are necessary while a simple call to a), b), c) would be much easier...

Fig. 5) Additional labeling (a,b,c...) could be helpful here, too. While intuitively I would assume that blue = DAPI and green = GFP, these things should be labeled or described in the legend. Especially in the 3D rendering it is quite unclear what is being portrayed. Is this an overlay of a FIB/SEM segmentation with the confocal 3D-data?

Minor:

The first element in the filtered list can thus be stored for the subsequent application of autofocus and autostigmation procedures (AFAS) (Supplementary Fig. 3c). [technically this has been defined before]

Typos/grammar:

In our case, we had two of such experiments, reaaching a global targeting accuracy (RMSE) of 8 {plus minus} 5 μm. A transformation is computed to register together the LM list and EM landmarks list, ...

The FOV is magnified from a 305 μm by 305 μm to a 36.4 μm by 36.4 μm surface area and an image of the cross-section is taken (Fig. 3c).

The sample is positioned at the target coordinates of the first cell, and the Multisite module performs the coincidence point alignment of both the electron and ion beams (Fig. 3a and Supplementary Fig. 3a).

To preserve the target, the sample is drifted 50 μm in x. [shifted?]

Significance

Significance:

It is clear, that the kind of automation outlined here is necessary to elevate correlative SEM volume imaging to a "high-throughput" technique, which could become valuable for many biological questions. CLEMSite offers a valid technical solution and appears to be a solid implementation of the traditional/manual workflow. However, its presentation needs to be improved before we can support publication.

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

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

Review on "CLEMsite, a software for automated phenotypic screens using light microscopy and FIB-SEM" by Serra Lleti et al.

The manuscript describes a toolset to correlate LM data with automated FIB-SEM of selected regions of interest. This allows 3D correlative microscopy of multiple adherent cells ¬from a single resin block. This allows much needed high throughput in CLEM analysis to become quantitative. Two applications on Golgi apparatus morphology are shown.

Major questions:

• The software has been developed in collaboration between Zeiss/ Fibics in collaboration with academic groups and will only function on Zeiss SEMs that have the proper software. Thus, if I understand correct, it will not be of generic use and a more appropriate title would be 'CLEMsite, a software for automated phenotypic screens using light microscopy and Zeiss FIB-SEM"
• How is the described approach using FIB-SEM advantageous compared to methods like Serial Block-face EM (SBEM) and array tomography using serial section where larger fields of multiple cells can be imaged? Especially because the axial resolution was set to 200 nm and discussed as essential for the throughput speed.
• Is the data FAIR available?
• How is CLEMsite available? Is the code public or for sale?

Other comments:

• Can you comment on the flexibility of this method? It is described as a flexible method, but only HeLa cells (quite flat cells) and Golgi apparatus targeting was used. What about different cell types and what about targets with a less obvious EM morphology?
• For EM acquisition ZEISS smartSEM with ATLAS was used. LM was recorded with a microscope from a different vendor. Can the software be used regardless of microscope type?
• Create less variation in the size of scale bars.
• M&M: High resolution light microscopy: Why call this 'high resolution'? Specs given seem randomly chosen: For example objective magnification yes, NA not; excitation wavelength yes, emission not.

Significance

See above: This depends on the availability of code, as well as the usability in FIB-SEM that is not based on Zeiss.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Serra Lleti et al. report a new software (CLEMSite) for fully automated FIB-SEM imaging based on locations identified beforehand in LM. The authors have implemented routines for automatically identifying common reference patterns and an automated FIB-SEM quality control. This allows autonomous data acquisition of multiple locations distributed over the entire sample dish. CLEMSite has been developed as a powerful tool for fast and highly efficient screening of morphological variations.

Major comments:

The performance of CLEMSite has been demonstrated by the authors with two typical biological example applications. The stated performance parameters such as correlation precision and reproducibility are highly convincing and supported by the presented data. The authors give detailed information on their workflow and how on to use CLEMSite, which should allow other researchers to implement this for their own applications. The only comment I have in this regard, and I might have overlooked it, but how will CLEMSite be made available to the scientific community?

Minor comments:

The author mention that decreasing the z-resolution to 200 nm steps was critical to achieve high throughput. For applications that require higher resolution: is the only disadvantage a longer data acquisition time or are there also other limitations? I would assume that locating the finer structural details in a much larger data set might also introduce additional challenges in the data analysis pipeline.

In Table 1 in the supplements, the units are missing for the targeting positions.

On page 4, 4th line from the bottom, there is a typo in "reaaching a global targeting...".

Significance

With CLEMSite, the authors present a powerful new software tool for the FIB-SEM imaging community. The high level of automation allows high throughput data acquisition with minimal user interaction. To my knowledge, this is the first software that fully automatically recognises reference features and is able to run fully autonomously after points of interest have been selected in FM. This high throughput screening tool for FIB-SEM imaging would make a substantial technical contribution to the field of cellular imaging.

My own expertise lies in the field of technical developments for CLEM and super-resolution FM. I am not able to judge the biological content of the manuscript.

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Reply to the reviewers

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

This study presents a first structural insight on formin mDia bound to actin filaments in physiological conditions. Based mainly negative stain EM, the authors use 2D and 3D class averaging to describe two main configuration of the formin at the filament barbed end. The two configurations support the previously proposed stair-stepping model, which was based on crystal structures, with an open state where the formin binds two actin monomers and a closed state where three monomers are bound. Because the majority of the structures fall in the first, open state, this supports the existence of this intermediate. The authors also show that the orientation of the free FH2 in this open state is somewhat flexible, as several sub-classes with different angles can be distinguished. Finally, they identify, for the first time, formin densities bound along the length of the filament.

The data is well presented and I don't have any major issue. The only point is that the information that all the initial structural data comes from negative stain EM comes should be put upfront. One gets the feeling that cryoEM is used throughout until one reads the section on cryoEM. Given that the methodology is now also established for cryoEM, it is regrettable that data was not collected with a 300kV microscope, which may have revealed more details of the conformations, but I understand microscope time is hard to come by, and the authors did a remarkable job from negative-stain EM.

The finding of formin densities binding along the length of the actin filament is very interesting. Besides the previous cited finding, it also reminds of the observations made in yeast where Bni1 (in S. cerevisiae; PMID 17344480) and For3 (in S. pombe; PMID 16782006) where shown to exhibit retrograde movement with polymerizing actin cables in vivo. This would be interesting to consider in the discussion.

Reviewer #1 (Significance (Required)):

This study extends our understanding of the mechanism of formin-mediated actin assembly, by providing a first structural observation in physiological conditions. While confirmatory of previously proposed model, but also excludes an alternative model, and offers novel observations of flexibility and binding along the actin filament length. It will be of great interest to researchers on the actin cytoskeleton.

My expertise is in the actin cytoskeleton and formins, but I am no expert in EM structural analysis.

We thank reviewer 1 for the very positive comments and for pointing out the relevance of our study for the actin cytoskeleton field. As advised, we now specify upfront in the abstract and in the introduction that most of the presented results were obtained from negative stain electron microscopy. Following the reviewer’s advice, we have enriched the discussion to highlight the retrograde movements of formins in actin cables observed in vivo.

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

Maufront et al. have used EM to study the conformation of mDia1 at the barbed end and the core of actin filaments to explain the molecular mechanism of the FH2 dimer processivity at these sites. Based on modelled structural data they tried to describe how the conformational changes in FH2 dimer lead to its partial dissociation, and then association with filaments during the process of translocation coupled to subunit addition at actin filaments barbed ends. This supports a previous study (Otomo et al. 2005, Nature), in which using X-ray crystallography structural data were used to propose a stair-stepping model for Bni1p translocation at the barbed ends during actin polymerization. The model for mDia1 binding to core filaments is also given. Moreover, using EM structure and the previously reported structures of actin (PDB: 5OOE), and actin with formin FH2 dimer (PDB: 1Y64), authors explained the dynamic nature of FH2 dimer at barbed ends of the filaments using the flapping model. But due to the low resolution of their structures ~ 26-29A0, the finer details of actin and the FH2 dimer structure at barbed ends could not be resolved, leaving open questions about the orientation of actin helical twist at this end during elongation. The authors tried several conditions to get high density barbed-end filaments, but that did not collect adequate number of particles, resulting in low number of particles selected for structure modelling purposes. However, to attain more physiologically relevant structure they used cryo-EM, but were successful in capturing only the open conformation structure of FH2 dimer (at low resolution). Thus, due to low resolution of structures the key findings have not added much to what we already know about the mechanism of FH2 dimer translocation during actin polymerization, except that their studies support the stair-stepping model (Otomo et al. 2005, Nature) and not that of "stepping second" model ( Paul and Pollard. 2008, Curr. Bio.). Thus, this manuscript does not merit publication in this journal.

We thank reviewer 2 for taking the time to read and review our study. However, we respectfully disagree with the statement that our findings “have not added much to what we already know about the mechanism of FH2 dimer translocation during actin polymerization”. As mentioned in our report, collecting EM data for formins in physiological conditions (at the barbed ends of growing filaments), as we do here for the first time, entails limitations on the number of particles one can observe and on the resulting resolution. Despite this rather low resolution, our data allow us to discriminate between two proposed models accounting for the processivity of formin FH2 domains at filament barbed ends. Being able to determine which of two competing models is valid (as the reviewer says we do) does add a lot to what we already know.

Major comments:

1. Present study does not provide any new insight about the conformation of the actin dimer at the barbed ends of actin filaments when FH2 domains of formin are bound. This study appears to be more like an extension of previous research (Otomo et al. 2005, Nature), in which the authors used X-ray crystallography data to propose a model for actin filaments elongation by formin bound at the barbed ends.

As mentioned above, we respectfully disagree with this remark. First, in Otomo et al. 2005, formins are arranged in a crystal into a non-physiological “daisy chain” arrangement around a non-canonical tetramethyl rhodamine-actin filament. Our observations were made in physiological conditions displaying a single formin dimer at the barbed end of a polymerizing filament. Second, the stair stepping model originating from Otomo et al. was only inferred and extrapolated from the crystal structure and not directly observed. Both the open and the closed conformations were speculations, that had never been observed up to now. In our current report we directly visualize these two conformations. Third, the observations of Otomo et al. were obtained using formin Bni1p from yeast, not the mammalian formin mDia1, for which there is little (PDB 1V9B) structural data available describing the structure of a truncated mDia1 in the absence of actin. Finally, in addition to validating the stair-stepping model experimentally, we make unexpected observations that are totally absent from the model derived from Otomo et al. and subsequent studies.

The low resolution of structures is a major concern.

As mentioned above, the limited resolution is the price we had to pay for being in physiological conditions, with formins interacting with the barbed ends of growing actin filaments. Nonetheless, this resolution is sufficient to discriminate between the two previously existing models, and to make new observations, beyond these models.

Given the low resolution of data, how can the authors decide on the number (4) of classes of FH2 domain (in open state) and present them as "continuum of conformations". They stated "details featured in class 4 do not appear as sharp as in class 2". What was the basis of deciding on the sharpness level?

We agree that this point was unclear, and we thank the reviewer for pointing it out. The choice of the number of sub-classes for the open state is a trade-off between the sharpness (ie signal-to-noise ratio) of the resulting image, which is a direct consequence of the number of particles within each sub-class, and the internal variability within each sub-class. Class 4 might appear more “blurry” because it gathers particles displaying a range of angles. When increasing the number of generated classes in the 2D processing, we observe angular variations of the FH2 domains intermediate to the ones displayed in Figure 3. However, because increasing the number of classes results in averaging less particles per class, the generated classes appeared more noisy or “blurry” and not as “sharp”, as mentioned in the manuscript. Hence, we chose the number of displayed classes so that the signal-to-noise would remain satisfactory and sufficient to be able to determine the relative angle between the two FH2 domains. To make things clearer, “do not appear as sharp” was replaced by “displayed a lower signal-to-noise ratio and thus looked noisier”. The expression “sharp” was replaced by “enough contrast”.

The authors showed 30Å structure of FH2 domain encircling actin filaments towards their pointed ends, but said nothing about the kind of decoration it could be, a "daisy-chain" or "concentric circle"? Also, they did not mention anything about the orientation of actin helical twist and specific sites of binding. These information would provide new in-depth understanding of how formins binds while diffusing along the filaments.

The quality is sufficient to distinguish isolated FH2 dimers along the core of actin.

Accordingly, the FH2 dimers we observed along the core of our actin filaments adopt a conformation similar to that observed at the barbed end, as mentioned in the text (‘concentric circle’). This observation differs from the reported for INF2 which accumulated along filaments and may interact in a ‘daisy-chain‘ manner (Gurel et al, 2014 ; Sharma et al, 2014). From our data, we can thus assume that formins interact with F-actin along the core of filaments similarly to the way they do at the barbed ends, and might translocate in a two-step manner alongside the actin filament. As stated in the manuscript, the actin helical twist could not be deciphered. For docking the crystal structures within our EM envelope, we used the formin-actin contacts described previously in Otomo et al.

The author stated - "The leading FH2 domain likely provides a first docking intermediate for actin monomers that would help their orientation relative to the barbed end, resulting in a higher actin monomer on-rate". This statement was made on the basis of observing 79% times FH2 in the open state in their data set. This seems like an overstatement because they don't have any direct structural data to support such claim.

We agree with the reviewer that our statement, taken from the discussion section, is speculative, and we apologize if this was unclear. Our purpose was to propose a plausible mechanism, based on our structural data, since the FH2 domain stands in front of the barbed end in the “open conformation” and since it likely interacts with actin monomers. We have now rephrased our sentence to state more clearly that is a hypothetical mechanism : “We propose that… could provide…”.

In the Discussion they mentioned "the FH2 dimer would then be "lagging" behind the elongating barbed end if actin twisting back to 180{degree sign} occurs before the addition of actin monomer and this explains the diffusing along the actin filaments". Did authors encounter filaments with two formins bounds to them in their negative stain images? What is their view on this? In current data, they showed structure in which only one FH2 dimer is bound to the pointed ends of actin filaments. Have they tried increasing the concentration of formins to obtain structures with more than one formin is bound towards the pointed ends of actin filaments?

Following the recommendations from reviewer 2, we have performed an additional analysis and we now show typical examples of filaments observed with a formin along their core, including cases where two formins are observed on the same filament (Supplementary Figure 12). As we now explain in the discussion section, five different mechanisms (including lagging) can be invoked to explain how a formin can be located along the core of the filament. These five mechanisms can all account for the possibility to have more than one formin on the same filament.

The lagging mechanism, however, is the only one where we would expect that the filaments with a formin along their core are less likely to also have a formin at their barbed end (because the formin at the core spontaneously departed the bare barbed, that was left bare and with a shorter time to load another formin before fixation of the sample). A simple statistical analysis of our data leads to the estimation that 48 ± 7% (n=50) of actin filaments with a formin within their core also display a formin at their barbed ends. This is significantly less than for the global filament population, where 77 ±0.4% (n=10,461) of barbed ends are decorated with formins. This supports the lagging scenario as a likely mechanism putting formins along the core of the filament.

Regarding the specific suggestion to increase the formin concentration: We did screen different formin concentrations, but with higher concentrations the level of noise due to unbound formins was significantly increased in the image background and impeded a proper analysis. This is why we consistently used 100 nM formins.

To increase the density of short filaments for sample preparation, the authors used additional actin binding proteins "shown in supplementary Figure 2.C". There is no supplementary Figure 2.C. Moreover, it would be nice if the concentrations of these proteins are mentioned in the text.

We apologize for this mistake. Supplementary Figure 2.C has now been added and the protein concentrations have been added in the main text.

Minor comments:

1. Figure 1 legend needs editing. E is missing in the legend.

Thanks for noticing this. We have added the missing legend for 1.E. 2. There is no supplementary Figure 2.C.

We apologize for this mistake. We have now added supplementary Figure 2.C.

It is recommended that the authors report the number of particle used during 2D and RELION 3D classifications in the figures. This would help in better understanding of the probability of the conformations mentioned in the text.

It was mentioned in the text. We have now made this information clearer to the reader.

Reviewer #2 (Significance (Required)):

This is the first direct study showing the two (open and closed) conformations of mDia1 FH2 domain at the barbed ends of actin filaments using EM and cryoEM. The study supports the proposed molecular mechanism of FH2 processivity at the barbed ends during filaments elongation using stair-stepping model reported earlier (Otomo et al. 2005, Nature). For the first time, FH2 has been shown to fluctuate between various angles with respect to static actin filaments, and on this basis they propose a flapping model (Fig 5). They explained the whole mechanism using structural proof, but the low resolution of data raises a question about their quality sufficiency to propose this mechanism. The overall novelty of this manuscripts is insufficient for the publication in this journal. Audience having understanding of the actin and actin binding proteins will be interested in this study. Additionally, researcher from the field of structural biology (EM and CryoEM) will be interested. I have been working in the field of actin and actin binding proteins for past 4 years. Over 10 years' experience in protein biochemistry, structural biology and molecular biology.

We do not fully understand why, on one hand, reviewer 2 indicates that “for the first time, FH2 has been shown to fluctuate between various angles…” and that “Audience having understanding of the actin and actin binding proteins will be interested in this study. Additionally, researcher from the field of structural biology (EM and CryoEM) will be interested.”. On another hand, reviewer 2 states that “The overall novelty of this manuscripts is insufficient for the publication in this journal.”, which seems contradictory with the above statements and comments.

Regarding novelty, we insist on the fact that we have achieved for the first time the direct observation of FH2 formin domains at a resolution sufficient to discriminate between two distinct models at the barbed ends, as well as to observe the presence of formin mDia1 along the core of actin filaments in conditions where nobody has proposed that this could happen.

In addition, we have not specified any specific journal within the possible ones from “review commons”, up to now.

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

Summary:

In this manuscript, Julien et al. use negative stain electron microscopy and cryo-EM to show two conformations of the FH2 domain for the formin mDia1 bound to the barbed end of an actin filament. These conformations support the "stair-stepping" model of FH2 domain movement with an elongating actin filament, as previously postulated by Otomo et al. (reference 1). The two states observe correspond to the "open" (~79%) and closed (~21%). The authors also show the conformational variability of the open state suggesting flexibility in this state. Finally, the authors observe FH2 domains encircling the actin filament at a distance from the barbed end, and suggest that the FH2 can diffuse from the barbed end down the filament.

Major comments:

1) Novel insights into formin function derived from this structure would raise impact. Issues that could be addressed include the following. Simply adding some lines to the discussion would not really add impact, but additional experimental/modeling work would.

We agree that comparing the binding mode of different formins on actin filaments, testing the impact of profilin, and assaying FH2 domains in the absence of FH1, as proposed below, would provide a broad set of interesting additional data. However, without claiming that our results can be generalized to all formins in all conditions, we believe that our findings are novel and should be of interest to a large community. The proposed additional experiments/modeling represent an impressive amount of work, and will be carried out in future investigations. We answer these comments in more details below.

1. Whether this model really holds true for all FH2 domains. Formin FH2 dimerization and processive filament barbed end elongation are widespread features of formins, which have been evidenced for many organisms from metazoan to plants. Since we could dock the FH2 from yeast formin Bni1p to account for mammalian mDia1, we think the FH2 domain conformations may be conserved enough among species to display similar translocation mechanisms at the barbed ends of actin filaments, using a two-state mechanism. We chose to use the crystal structure from Bni1 formin (PDB 1Y64) because this structure was obtained in the presence of an actin filaments and brings some insights about the formin-actin contacts.

In order to convince reviewer 3, we superimposed the existing crystal structure of the FH2 mDia1 domain (PDB: 1V9D) with our model and reconstruction and show (Supplementary Figure 12) that the differences are minor. The mDia1 FH2 domains (atomic structures in red, PDB : 1V9D) are aligned with Bni1p FH2 domains (atomic structures in green and blue, PDB : 1Y64) previously fitted into the electron microscopy envelope of a barbed end capped by a formin in the « open state ». The FH2 domains are well aligned with a slight discrepancy in the knob/actin contact regions (blue arrows). This discrepancy most likely results from the absence of actin partners in the crystals obtained with mDia1 FH2 domains. The Bni1p structure thereby most accurately represents the knob/actin contact region. In addition, the folding of the lasso domain around the post domain is resolved in the Bni1p structure. Note here that the Bni1p lasso domains wrap equally well around the Bni1p post domain and the mDia1 post domain (green arrows).

1. Whether the % time spent in the open and closed states might dictate the vastly different elongation rates mediated by different formins. For example, mDia1 is considered one of the 'faster' elongators (equivalent to actin alone in the absence of profilin), while fission yeast Cdc12 essentially caps filaments in the absence of profilin. We have discussed this aspect thoroughly in the discussion section to conclude that:” Our direct assessment of the open state occupancy rate thus provides important information on the molecular nature of the formin-barbed end conformations which could not be directly inferred from kinetic measurements, with or without mechanical tension, so far. Considering a gating factor of 0.9 and considering that formin mDia1 spends 79% of the time in the open state, we can compute that the on-rate for monomers would be slightly higher (14% higher) for an mDia1-bearing barbed end in the open state, than for a bare barbed end.”

We agree that repeating our set of EM experiments and analysis with other formins, like fission yeast Cdc12, would be interesting. However, this would take a long time, and falls out of the scope of our paper.

1. Whether the % time spent in the open and closed states varies if filaments are actively elongating in the presence or absence of profilin. We have chosen not to include profilin in our experiments, and to limit the concentration of G-actin, in order to reduce the background in our EM micrographs. Also, a rapid filament elongation would increase the amount of F-actin per barbed end, while a dense population of short filaments is key to obtain accurate data (as we explain in the discussion, paragraph 1, p9).

We speculate that, by providing a link between the FH1 domains and the filament barbed end, profilin might very well alter the percentage of time spent in the open state, and mitigate lagging as mentioned in the discussion section. Properly addressing the impact of profilin with our EM experiments is very challenging, for the reasons we have explained. It would require further investigations, beyond the scope of this study.

1. How this model impacts the interactions of formins with other proteins at the barbed end. For example, capping proteins. We did not include capping proteins (or other additional proteins) because we wanted to avoid increasing the number of particles from diverse nature per field of view, as they constitute a background that is detrimental for the analysis of EM micrographs. We would have add to sort out additional populations in the course of image analysis. We thus only mixed actin and formin in our assays.

2. Do these results relate to formin function in disease? Because formins regulate actin polymerization, their malfunction is linked to a variety of diseases. We therefore expect our findings to be useful to researchers in the medical field. However, our study remains in the scope of basic research and primarily aims at understanding the mechanisms of formin-assisted actin polymerization.

2) The observation that formin FH2 domains can bind filament sides has been made several times. In particular, a structural model of the FH2 domain of the INF2 formin along the side of an actin filament (Gurel et al 2014, PMID 24915113). This publication also references other papers showing other formins binding to filament sides. There are two points to this comment:

1. The model in Gurel et al is that the FH2 domain does not slide down the filament from the barbed end. Rather, the FH2 dimer has an appreciable dissociation rate, enabling it to encircle the filament without having to slide. This FH2 dissociation has been observed for another formin that has been shown to bind filament sides, FMNL1 (called FRL1 in the listed publication), in Harris et al 2006 (PMID 16556604). The authors must explain their reasoning for thinking that mDia1's FH2 can slide down the filament from the barbed end. One possibility is to make observations of this FH2 population in filaments that were not sonicated. What is the average distance of FH2s from the barbed end? We thank the reviewer for pointing our attention to this report from Gurel et al. which we now cite. Following this comment, as well as point 6 of reviewer 2, we now discuss the different mechanisms that could lead to our observation of mDia1 along the core of the filament. We provide a new analysis of our data (discussion section), arguing in favor of the lagging mechanism (i.e. ‘sliding down’ from the barbed end), without excluding the competing scenarios. Briefly, we compute that 48 ± 7% (n=50) of actin filaments with a formin within their core also display a formin at their barbed ends. This is significantly less than for the global filament population, where 77 ±0.4% (n=10,461) of barbed ends are decorated with formins. This supports the lagging scenario, which is the only one where a filament with a formin along its core should be less likely to also have a formin at its barbed end.

The distance of FH2s from the barbed end would provide additional information. However, it is difficult to estimate, since we often to not see the entire filament, and since we do not know which end is the barbed end.

1. Interestingly, in some of the works studying formin binding to filament sides, mDia1 was shown to be rather poor in this property. It would be useful to get an idea of what % of the observed FH2s are in the filament core, as opposed to at the barbed end. Along with the additional analysis mentioned in the previous point, we have now estimated that about 8% of actin filaments display a formin within their core. We have added this number in the manuscript (end of the Results section). As a comparison, in our assays, 77% of filament barbed ends bear a formin.

2. The authors must reference the past works showing FH2 binding to filament sides, particularly the structural work. At present, no mention of prior work on FH2 side binding is mentioned. As advised, we have now added additional references and more particularly Gurel et al, 2014.

3) My major technical concern in this manuscript is that the authors use the FH1-FH2-DAD domain of mDia1 for the imaging, but use FH2 structure of Bni1p for 3D characterization (Otomo et al.). Even though Bni1p has been used for functional and structural analysis, mDia1 and Bni1p FH2 domains share low sequence homology. In addition, mDia1 only partially complements loss of Bni1 function in vivo (Moseley et al., 2004 PMID 14657240). Can the authors use the partial structural information of the mDia1 FH2 from Shimada et al 2004 (PDB 1V9D, PMID 14992721)? Alternately, the authors could have used FH2 domain of Bni1p for imaging. At the very least, the authors should explain clearly why they used different proteins for imaging and modeling.

As mentioned above (please see our response to point 1.a), we chose to use the crystal structure from formin Bni1 (PDB 1Y64) because this structure was obtained in the presence of an actin monomers, and it thus brings some insights about the formin-actin contacts. The existing structures obtained from formin mDia1 does not include actin (full length by EM: Maiti et al, 2012; crystal structure of subdomains (without FH1): Otomo et al., 2010 PLoS one). It thus seems relevant, in the context of our investigations, to use a structure where formin-actin contacts could be at least partially inferred.

Further, we superimposed the existing crystal structure of the FH2 mDia1 domain (PDB: 1V9D) with our model and reconstruction and show that the differences are minor (please see the figure in our response to point 1.a, above).

4) The open and closed states are observed from negative staining data. However, the authors can only find one of the states (open) by cryo-EM, which decreases the confidence level of the paper's conclusions. It would be useful for the authors do a little more to try to find the closed conformation by cryo-EM.

Using Cryo-EM we can already recover the most abundant open conformation.

Unfortunately, as pointed out here, the number of particles obtained was too low to enable high resolution and reveal the two observed conformations. Indeed, considering a density of ~ 5 barbed ends par micrograph, the collection of tens of thousands of images would have been necessary, which was not realistic regarding the access we have to latest generation microscopes.

5) It is unclear whether there are additional effects of using FH1-FH2-DAD protein (not FH2 only) for the imaging, as it shows long protrusion at the tip of actin barbed end. To avoid those concerns the authors could use only FH2 domain of mDia1. Also the authors have to note that they used Bni1p structure because there are no published structures of mDia1 so far.

We had indeed tried to use a construct deprived of the flexible FH1 domain but the lower purity of this construct and the presence of aggregates led to the collection of lower quality EM micrographs. As profilin was not included in our assay, FH1 domains were not involved in actin polymerization at the barbed end and thus remain very flexible and unstructured. Consistently, we did not detect any additional electronic density that could result from the FH1 domains.

We indeed point out (p5) that “We used the crystal structure from yeast Bni1p FH2 domains in interactions with an actin filament, rather than the existing one from mammalian mDia1 formin FH2 dimer in isolation (PDB 1V9D), because actin-formin contacts are described in the Bni1p structure.” Minor comments:

1) Figure 1: It would be interesting if imaging is provided for mDia1 bound to filaments which it has nucleated. Would it be possible that binding to pre-formed filaments is different to that for mDia1-nucleated filaments?

This is a good suggestion for further investigations but it extends beyond the scope of this study: as we explain, our attempts to nucleate filaments from mDia1 lead to lower quality micrographs, and the sonication of preformed filaments was our best option. However, we do not expect the translocation mechanism of FH2 to differ, as a function of the nucleation history of the filament, since the formin interacts with a filament whose elongation it has assisted over several subunits.

2) Supplementary figure 2: Numbers of things in the S2 is unclear and poorly described in both results and methods. In particular, figure S2A, the definitions of the black and gray lines (steady state actin) is not clear. Are they containing 5% pyrene actin? Is that actin in polymerization buffer or in monomer-actin buffer? Is that actin incubated with actin polymerization buffer for a certain time before measurement of fluorescent intensity? In figure S2B, how the authors calculate the monomer actin concentration? The authors should provide the information in either results or methods part.

We apologize for the lack of information. Since this is a standard assay, we have now added more details in the Methods section (rather than in the Results section).

All curves shown in figure S2 were obtained with 5% pyrene actin. The gray curve shows the pyrene fluorescence intensity baseline from 1 µM G-actin monomers, obtained in G-buffer. The black curve is the fluorescence intensity at steady-state of 1 µM actin in polymerizing conditions, (after 1 hour of incubation at room temperature, at 5 µM, the sample was diluted without sonication and left for another hour before measuring the fluorescence intensity).

The monomeric actin concentrations shown in figure S2B are derived from the intensity level of pyrene at any time point during the experiment, using the simple equations we now present in the Methods section.

3) Supplementary figure 2 C: The figure and legend are missing in the manuscript. Furthermore, the authors describe that they used Gc-globulin to sequester monomeric actin in solution. Is gc-globulin widely used for actin monomer sequestration?

Thank you for noticing the missing panel which is now back in place. Indeed, Gc globulin is known to sequester G-actin (Van Baelen, H., R. Bouillon, and P. DeMoor. 1980. “Vitamin D binding protein (Gc-globulin) binds actin”. J. Biol. Chem. 255:2270-2272). This is why we have attempted to use it. We could see a slight effect but we did not want to increase the noise within our images with additional proteins that would have made the analysis more complicated.

CROSS-CONSULTATION COMMENTS Reviewer #1 mentions that the authors identify formin densities bound along the actin filament for the first time. I agree that the imaging of the mDia1 along the actin filament using electron microscopy is novel, but the concept of formin binding has already been found and studied well with other formins (PMID 16556604, PMID 24915113) and even mDia1 has poor binding activity compared to other formins. It was really nice of the authors to show the mDia1 side filament binding, but I don't think it is a striking finding.

I have no comment for Reviewer #2.

Reviewer #3 (Significance (Required)):

If the EM refinements and 3D rendering techniques are conducted rigorously (which this reviewer is unable to judge), the data support an existing theory of how FH2 domains interact with the actin barbed end. Overall, the data will be of interest in formin field. However, as written the paper confirms an existing model, and does not represent new insight. Impact would be raised by providing insights from these findings that impact formin function or disease.

We have answered this concern above. The existing models were speculative and not based on direct observations. They relied on data obtained in non-physiological conditions.

Here, we directly observe two distinct conformations in our structural data, and clearly validate one model over the other. This provides a major advancement in our understanding of formin interaction with actin filaments. In addition, we uncovered an unexpected behavior of formin mDia1, which can readily be found along the core of the filament without the aid of additional proteins, and we propose a mechanism based on our data to account for this observation.

Another main point is that the observation of FH2 domains bound along an actin filament, while interesting, is not novel. Others have found this for other formins, but those papers are not referenced here.

The direct binding of formins to the sides of actin filaments is thought to be specific to some particular formins (we now cite additional references in our manuscript, to discuss this point). Formin mDia1, which is a ubiquitous and widely studied mammalian formin (perhaps the most studied), has only been described to diffuse along actin filaments when a capping protein dislodges it from the barbed end (Bombardier et al. Nat Com 2015). Here, we show that formin mDia1 can be found encircling the core of actin filaments, in the absence of any capping protein. This behavior is novel and unexpected. It should open new avenues for research on formin mDia1, as well as on other formins.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript, Julien et al. use negative stain electron microscopy and cryo-EM to show two conformations of the FH2 domain for the formin mDia1 bound to the barbed end of an actin filament. These conformations support the "stair-stepping" model of FH2 domain movement with an elongating actin filament, as previously postulated by Otomo et al. (reference 1). The two states observe correspond to the "open" (~79%) and closed (~21%). The authors also show the conformational variability of the open state suggesting flexibility in this state. Finally, the authors observe FH2 domains encircling the actin filament at a distance from the barbed end, and suggest that the FH2 can diffuse from the barbed end down the filament.

Major comments:

1. Novel insights into formin function derived from this structure would raise impact. Issues that could be addressed include the following. Simply adding some lines to the discussion would not really add impact, but additional experimental/modeling work would.
   • a. Whether this model really holds true for all FH2 domains.
   • b. Whether the % time spent in the open and closed states might dictate the vastly different elongation rates mediated by different formins. For example, mDia1 is considered one of the 'faster' elongators (equivalent to actin alone in the absence of profilin), while fission yeast Cdc12 essentially caps filaments in the absence of profilin.
   • c. Whether the % time spent in the open and closed states varies if filaments are actively elongating in the presence or absence of profilin.
   • d. How this model impacts the interactions of formins with other proteins at the barbed end. For example, capping proteins.
   • e. Do these results relate to formin function in disease?
2. The observation that formin FH2 domains can bind filament sides has been made several times. In particular, a structural model of the FH2 domain of the INF2 formin along the side of an actin filament (Gurel et al 2014, PMID 24915113). This publication also references other papers showing other formins binding to filament sides. There are two points to this comment:
   • a. The model in Gurel et al is that the FH2 domain does not slide down the filament from the barbed end. Rather, the FH2 dimer has an appreciable dissociation rate, enabling it to encircle the filament without having to slide. This FH2 dissociation has been observed for another formin that has been shown to bind filament sides, FMNL1 (called FRL1 in the listed publication), in Harris et al 2006 (PMID 16556604). The authors must explain their reasoning for thinking that mDia1's FH2 can slide down the filament from the barbed end. One possibility is to make observations of this FH2 population in filaments that were not sonicated. What is the average distance of FH2s from the barbed end?
   • b. Interestingly, in some of the works studying formin binding to filament sides, mDia1 was shown to be rather poor in this property. It would be useful to get an idea of what % of the observed FH2s are in the filament core, as opposed to at the barbed end.
   • c. The authors must reference the past works showing FH2 binding to filament sides, particularly the structural work. At present, no mention of prior work on FH2 side binding is mentioned.
3. My major technical concern in this manuscript is that the authors use the FH1-FH2-DAD domain of mDia1 for the imaging, but use FH2 structure of Bni1p for 3D characterization (Otomo et al.). Even though Bni1p has been used for functional and structural analysis, mDia1 and Bni1p FH2 domains share low sequence homology. In addition, mDia1 only partially complements loss of Bni1 function in vivo (Moseley et al., 2004 PMID 14657240). Can the authors use the partial structural information of the mDia1 FH2 from Shimada et al 2004 (PDB 1V9D, PMID 14992721)? Alternately, the authors could have used FH2 domain of Bni1p for imaging. At the very least, the authors should explain clearly why they used different proteins for imaging and modeling.
4. The open and closed states are observed from negative staining data. However, the authors can only find one of the states (open) by cryo-EM, which decreases the confidence level of the paper's conclusions. It would be useful for the authors do a little more to try to find the closed conformation by cryo-EM.
5. It is unclear whether there are additional effects of using FH1-FH2-DAD protein (not FH2 only) for the imaging, as it shows long protrusion at the tip of actin barbed end. To avoid those concerns the authors could use only FH2 domain of mDia1. Also the authors have to note that they used Bni1p structure because there are no published structures of mDia1 so far.

Minor comments:

1. Figure 1: It would be interesting if imaging is provided for mDia1 bound to filaments which it has nucleated. Would it be possible that binding to pre-formed filaments is different to that for mDia1-nucleated filaments?
2. Supplementary figure 2: Numbers of things in the S2 is unclear and poorly described in both results and methods. In particular, figure S2A, the definitions of the black and gray lines (steady state actin) is not clear. Are they containing 5% pyrene actin? Is that actin in polymerization buffer or in monomer-actin buffer? Is that actin incubated with actin polymerization buffer for a certain time before measurement of fluorescent intensity? In figure S2B, how the authors calculate the monomer actin concentration? The authors should provide the information in either results or methods part.
3. Supplementary figure 2 C: The figure and legend are missing in the manuscript. Furthermore, the authors describe that they used Gc-globulin to sequester monomeric actin in solution. Is gc-globulin widely used for actin monomer sequestration?

Referees cross-commenting

Reviewer #1 mentions that the authors identify formin densities bound along the actin filament for the first time. I agree that the imaging of the mDia1 along the actin filament using electron microscopy is novel, but the concept of formin binding has already been found and studied well with other formins (PMID 16556604, PMID 24915113) and even mDia1 has poor binding activity compared to other formins. It was really nice of the authors to show the mDia1 side filament binding, but I don't think it is a striking finding.

I have no comment for Reviewer #2.

Significance

If the EM refinements and 3D rendering techniques are conducted rigorously (which this reviewer is unable to judge), the data support an existing theory of how FH2 domains interact with the actin barbed end. Overall, the data will be of interest in formin field. However, as written the paper confirms an existing model, and does not represent new insight. Impact would be raised by providing insights from these findings that impact formin function or disease.

Another main point is that the observation of FH2 domains bound along an actin filament, while interesting, is not novel. Others have found this for other formins, but those papers are not referenced here.

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Referee #2

Evidence, reproducibility and clarity

Maufront et al. have used EM to study the conformation of mDia1 at the barbed end and the core of actin filaments to explain the molecular mechanism of the FH2 dimer processivity at these sites. Based on modelled structural data they tried to describe how the conformational changes in FH2 dimer lead to its partial dissociation, and then association with filaments during the process of translocation coupled to subunit addition at actin filaments barbed ends. This supports a previous study (Otomo et al. 2005, Nature), in which using X-ray crystallography structural data were used to propose a stair-stepping model for Bni1p translocation at the barbed ends during actin polymerization. The model for mDia1 binding to core filaments is also given. Moreover, using EM structure and the previously reported structures of actin (PDB: 5OOE), and actin with formin FH2 dimer (PDB: 1Y64), authors explained the dynamic nature of FH2 dimer at barbed ends of the filaments using the flapping model. But due to the low resolution of their structures ~ 26-29A0, the finer details of actin and the FH2 dimer structure at barbed ends could not be resolved, leaving open questions about the orientation of actin helical twist at this end during elongation.

The authors tried several conditions to get high density barbed-end filaments, but that did not collect adequate number of particles, resulting in low number of particles selected for structure modelling purposes. However, to attain more physiologically relevant structure they used cryo-EM, but were successful in capturing only the open conformation structure of FH2 dimer (at low resolution). Thus, due to low resolution of structures the key findings have not added much to what we already know about the mechanism of FH2 dimer translocation during actin polymerization, except that their studies support the stair-stepping model (Otomo et al. 2005, Nature) and not that of "stepping second" model ( Paul and Pollard. 2008, Curr. Bio.). Thus, this manuscript does not merit publication in this journal.

Major comments:

1. Present study does not provide any new insight about the conformation of the actin dimer at the barbed ends of actin filaments when FH2 domains of formin are bound. This study appears to be more like an extension of previous research (Otomo et al. 2005, Nature), in which the authors used X-ray crystallography data to propose a model for actin filaments elongation by formin bound at the barbed ends.
2. The low resolution of structures is a major concern.
3. Given the low resolution of data, how can the authors decide on the number (4) of classes of FH2 domain (in open state) and present them as "continuum of conformations". They stated "details featured in class 4 do not appear as sharp as in class 2". What was the basis of deciding on the sharpness level?
4. The authors showed 30Å structure of FH2 domain encircling actin filaments towards their pointed ends, but said nothing about the kind of decoration it could be, a "daisy-chain" or "concentric circle"? Also, they did not mention anything about the orientation of actin helical twist and specific sites of binding. These information would provide new in-depth understanding of how formins binds while diffusing along the filaments.
5. The author stated - "The leading FH2 domain likely provides a first docking intermediate for actin monomers that would help their orientation relative to the barbed end, resulting in a higher actin monomer on-rate". This statement was made on the basis of observing 79% times FH2 in the open state in their data set. This seems like an overstatement because they don't have any direct structural data to support such claim.
6. In the Discussion they mentioned "the FH2 dimer would then be "lagging" behind the elongating barbed end if actin twisting back to 180{degree sign} occurs before the addition of actin monomer and this explains the diffusing along the actin filaments". Did authors encounter filaments with two formins bounds to them in their negative stain images? What is their view on this? In current data, they showed structure in which only one FH2 dimer is bound to the pointed ends of actin filaments. Have they tried increasing the concentration of formins to obtain structures with more than one formin is bound towards the pointed ends of actin filaments?
7. To increase the density of short filaments for sample preparation, the authors used additional actin binding proteins "shown in supplementary Figure 2.C". There is no supplementary Figure 2.C. Moreover, it would be nice if the concentrations of these proteins are mentioned in the text.

Minor comments:

1. Figure 1 legend needs editing. E is missing in the legend.
2. There is no supplementary Figure 2.C.
3. It is recommended that the authors report the number of particle used during 2D and RELION 3D classifications in the figures. This would help in better understanding of the probability of the conformations mentioned in the text.

Significance

This is the first direct study showing the two (open and closed) conformations of mDia1 FH2 domain at the barbed ends of actin filaments using EM and cryoEM. The study supports the proposed molecular mechanism of FH2 processivity at the barbed ends during filaments elongation using stair-stepping model reported earlier (Otomo et al. 2005, Nature). For the first time, FH2 has been shown to fluctuate between various angles with respect to static actin filaments, and on this basis they propose a flapping model (Fig 5). They explained the whole mechanism using structural proof, but the low resolution of data raises a question about their quality sufficiency to propose this mechanism. The overall novelty of this manuscripts is insufficient for the publication in this journal.

Audience having understanding of the actin and actin binding proteins will be interested in this study. Additionally, researcher from the field of structural biology (EM and CryoEM) will be interested. I have been working in the field of actin and actin binding proteins for past 4 years. Over 10 years' experience in protein biochemistry, structural biology and molecular biology.

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Referee #1

Evidence, reproducibility and clarity

This study presents a first structural insight on formin mDia bound to actin filaments in physiological conditions. Based mainly negative stain EM, the authors use 2D and 3D class averaging to describe two main configuration of the formin at the filament barbed end. The two configurations support the previously proposed stair-stepping model, which was based on crystal structures, with an open state where the formin binds two actin monomers and a closed state where three monomers are bound. Because the majority of the structures fall in the first, open state, this supports the existence of this intermediate. The authors also show that the orientation of the free FH2 in this open state is somewhat flexible, as several sub-classes with different angles can be distinguished. Finally, they identify, for the first time, formin densities bound along the length of the filament.

The data is well presented and I don't have any major issue. The only point is that the information that all the initial structural data comes from negative stain EM comes should be put upfront. One gets the feeling that cryoEM is used throughout until one reads the section on cryoEM. Given that the methodology is now also established for cryoEM, it is regrettable that data was not collected with a 300kV microscope, which may have revealed more details of the conformations, but I understand microscope time is hard to come by, and the authors did a remarkable job from negative-stain EM.

The finding of formin densities binding along the length of the actin filament is very interesting. Besides the previous cited finding, it also reminds of the observations made in yeast where Bni1 (in S. cerevisiae; PMID 17344480) and For3 (in S. pombe; PMID 16782006) where shown to exhibit retrograde movement with polymerizing actin cables in vivo. This would be interesting to consider in the discussion.

Significance

This study extends our understanding of the mechanism of formin-mediated actin assembly, by providing a first structural observation in physiological conditions. While confirmatory of previously proposed model, but also excludes an alternative model, and offers novel observations of flexibility and binding along the actin filament length. It will be of great interest to researchers on the actin cytoskeleton.

My expertise is in the actin cytoskeleton and formins, but I am no expert in EM structural analysis.

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Reply to the reviewers

In this section we list all the comments done by the three referees and our corresponding action.

Regarding Reviewer #1:

1. On "mechanical control": The authors show changes in circadian power fraction with changes in YAP and with cytoskeletal inhibitors, but there are no properly-controlled experiments that directly perturb mechanics. The authors show a correlation between YAP nuclear/cytoplasmic ratio and circadian power, but YAP N/C alone is not a readout of mechanotrasndcution, per se. The authors have shown two different experiments where cells are cultured on a stiff (30kPa) substrate and soft substrate (300Pa), but they do not shown a direct comparison of YAP nuclear localization and circadian power under these two conditions in the same experiment. Direct, controlled perturbation of mechanical cues is necessary to support the title's use of the phrase "mechanical control."

We agree with the referee that further mechanical perturbations could strengthen our conclusions. In our original manuscript we directly controlled the mechanical environment by culturing cells on substrates of 300Pa and 30kPa in stiffness. These differences in stiffness were not sufficient to drive changes in circadian power fraction and YAP localisation, as depicted in Fig. 3C (we note that the direct comparison requested by the referee is shown in that figure). We hypothesise that this negative result is due to a very low “rigidity threshold” or to secretion of extracellular matrix that stiffens the initially soft substrate. In any case, we plan to strengthen the “mechanical control” message of our paper with one or more of the below experiments:

A) We will measure circadian power fraction and YAP localisation in even extremer stiffness/adhesion conditions, using 300 Pa and 30 kPa polyacrylamide gels with a different fibronectin coating protocol, as described in Elósegui-Artola et al., 2017. This allows a much finer control of the concentration of fibronectin coated, so we can reach low enough levels to compromise the cell adhesion to the substrate and cross down the threshold that would lead to cytosolic localisation of YAP. We will perform this experiment in presence of the FUD peptide, which inhibits matrix deposition (Tomasini-Johansson et al., 2001; this peptide has already been tested in our lab).

B) We will use the approach described in Fig. 2E to compare the circadian power fraction in cells spread in stadium-shaped islands of 2400 um2 and 1200 um2. Oakes et al., 2014 already showed that traction forces exerted by 3T3 fibroblasts depend on the size of the spread area of the cells, so we expect differences in mechanotransduction that should affect YAP localisation and, if our hypothesis is correct, the RevVNP circadian oscillations.

C) We will abolish the physical connection between the actin cytoskeleton and the nucleus by disrupting the LINC complex via the overexpression of a dominant negative (DN) nesprin-1 KASH domain (Lombardi et al., 2011). The plasmid designed for the inducible overexpression of the DN KASH domain, originally tested in NIH3T3 cells (Mayer et al., 2019), is available in our lab and has been used to prove that uncoupling cytoskeleton and nucleus leads to nuclear YAP decrease in single cells (Kechagia at al., 2022). We will aim to increase the circadian power fraction in low density cells upon the overexpression of the DN KASH domain.

Elosegui-Artola A, Andreu I, Beedle AEM, Lezamiz A, Uroz M, Kosmalska AJ, Oria R, Kechagia JZ, Rico-Lastres P, Le Roux AL, et al (2017) Force Triggers YAP Nuclear Entry by Regulating Transport across Nuclear Pores. Cell 171: 1397-1410.e14

Kechagia Z, Sáez P, Gómez-González M, Zamarbide M, Andreu I, Koorman T, Beedle AEM, Derksen PWB, Trepat X, Arroyo M, et al (2022) The laminin-keratin link shields the nucleus from mechanical deformation and signalling Cell Biology

Lombardi ML, Jaalouk DE, Shanahan CM, Burke B, Roux KJ & Lammerding J (2011) The Interaction between Nesprins and Sun Proteins at the Nuclear Envelope Is Critical for Force Transmission between the Nucleus and Cytoskeleton*. Journal of Biological Chemistry 286: 26743–26753

Mayer CR, Arsenovic PT, Bathula K, Denis KB & Conway DE (2019) Characterization of 3D Printed Stretching Devices for Imaging Force Transmission in Live-Cells. Cel Mol Bioeng 12: 289–300

Oakes PW, Banerjee S, Marchetti MC & Gardel ML (2014) Geometry regulates traction stresses in adherent cells. Biophysical Journal 107: 825–833

Tomasini-Johansson BR, Kaufman NR, Ensenberger MG, Ozeri V, Hanski E & Mosher DF (2001) A 49-Residue Peptide from Adhesin F1 of Streptococcus pyogenes Inhibits Fibronectin Matrix Assembly*. Journal of Biological Chemistry 276: 23430–23439

2. On "via YAP/TAZ": In addition to above, it is necessary to show that the changes in Circadian power fraction induced by mechanical cues in fact require YAP/TAZ signaling. Thus, an experiment comparing soft (300Pa) substrate with Stiff (30kPa) substrate in the presence or absence of YAP/TAZ is necessary to state that YAP and TAZ are the mechanistic mediators of mechanical cues on the clock.

We are currently generating via CRISPR-KO and shRNA silencing a YAP1/TAZ double mutant. We plan to use this cell line in those conditions where YAP is prominently nuclear (low density in stiff substrates) with the purpose of rescuing the RevVNP circadian power fraction.

1. While the TEAD-binding domain mutant experiment is elegant, to claim that TEAD is the transcriptional mediator, it must be demonstrated that this mutant indeed fails to induce TEAD-mediated transcription. This could be simply executed by demonstrating that the CCD mutant expresses reduced CTGF and Cyr61 (for example), compared to the 5SA, under these conditions. Further, endogenous YAP is still active and available to bind to TEAD in this system, which should be discussed.

We plan to carry out quantitative real-time PCR of CTGF and Cyr61 in all the YAP mutants and the control. Regarding the presence of endogenous YAP, we will clarify in the text that a) the overexpression of the different YAP mutants was done in high-density conditions, where endogenous YAP is significantly less localised in the nucleus, and that b) the levels of the exogenous YAP are much higher (we already have western blots showing this).

1. In Figure 3a: The cell perimeter needs to be shown either by actin staining or by brightfield images. The manually marking of cell boundaries is insufficient, specifically because the drugs used in this experiment affect the cytoskeleton. It would be very helpful to see this via actin staining or in the least with brightfield images.

The cell perimeter was drawn based on the cytosolic YAP immunostaining, whose levels are high enough to infer the cell shape (higher resolution images can be attached if necessary). As stated in the manuscript, the YAP nuclear-to-cytosolic ratio is calculated using two adjacent areas of identical size, one inside the nucleus and the other one just outside (see Materials and Methods/Immunostainings), so the exact cell shape is irrelevant for this particular quantification.

Regarding Reviewer #2:

Effects on the circadian clock

1. The authors use the fluorescent reporter created by Nagoshi from sections of the Rev-erbα gene. This reporter is widely used to estimate relative circadian timing in individual cells but it does not provide direct information on the circadian clock activity. In other words, while Reverb rhythmic expression is driven by the clock, it is not known whether less-rhythmic or non-rhythmic expression or change in expression level of Rev-erbα is affecting the core clock. For example, it has been shown that Rev-erbα knock-down cells are rhythmic as long as Rev-erb-beta is present. Thus, one major shortcoming of the current version of the manuscript is the missing dissection between Rev-erbα rhythmicity/expression and the circadian clock. More concretely, it remains unclear whether the change in Rev-erbα expression is a direct effect or caused by a defect clock. Since the authors presume a direct effect of YAP/TAP on Rev-erb expression, the former is likely. If that is the case, the data could be interpreted as that (missing) mechanic stimuli can lead to nuclear YAP/TAZ, which rises the level of Rev-erbα (and maybe interfere with its rhythmic accumulation). Beyond Rev-erbα expression, there may or may not be an effect on the circadian clock (core clock, CCGs). With the current version we do not know since the authors do not look beyond Rev-erbα expression. Thus, the claims on circadian clock or circadian rhythms in their cells is not studied in this version of the manuscript. The current version is still very interesting and provides insights into the Rev-erbα modulation, but additional work would be needed to show links with the core clock machinery. For this the authors could show influence (or at least correlation) of the YAP/TAZ/REVERBA phenotype on the oscillations of core clock genes or clock-controlled genes. Either through the use of alternative (ideally constitutive) reporters (e.g. PER2, BMAL1, fluorescent or LUC), or/and by analyzing RNA/Protein of core clock genes or output genes. This would not be necessary for all experiments, but at least for some were its possible (e.g. experiments with drugs perturbations). Otherwise, any claim like "YAP/TAZ perturbs the circadian clock ..." or "the circadian clock deregulation in nuclear YAP-enriched cells" is potentially flawed and has to be removed/reformulated.

We agree with the reviewer. In order to understand if the core clock is affected, beyond REV-ERBA, by YAP/TAZ expression and localisation, we plan to perform the two experimental approaches explained below. For both of them we will use high-density cells with and without YAP-5SA overexpression since the other conditions (drugs, micropatterned cells, low density) may not render enough cells for analytical approaches that are not based on fluorescent microscopy (real-time qPCR or luminescence recordings). Also, the potential results obtained with YAP-5SA overexpression will be more informative regarding causality YAP-circadian clock than those using the other conditions described in the manuscript.

1. We will use NIH3T3 bmal1::luc cells (already generated in our lab with the pABpuro-BluF plasmid; https://www.addgene.org/46824/) and an adapted microscopy-based system to track bioluminescence. We will need to give our cells a synchronisation shock since the single-cell signal with this reporter is too low and noisy to perform single-cell tracking.
2. We will check during 48 hours, every 4 hours, the mRNA levels of Bmal1, Clock, Cry1, Per2, Yap1 and Rev-erbα via quantitative real-time PCR. As in A), we will need to synchronise our cells prior RNA collection. In case the expression of the other components of the clock are not affected by YAP-5SA overexpression, we will modify the message of our manuscript to emphasize the role of REV-ERBA. As the referee mentions (and we thank them for that comment), finding that the modulation of Rev-erbα is mechano-sensitive and dependent on YAP/TAZ signalling would be still very relevant, given the role of this factor in metabolism, inflammation, mitochondrial activity, or Alzheimer’s disease, as discussed in lines 231-235 in the manuscript.

1. The authors aim to discard the possibility of paracrine signals by showing no increase in circadian power fraction of cells growing in low density with conditioned medium (Figure 2D). A paracrine signal coming from an oscillatory system is likely to oscillate and in that case, I do not see how growing cells in constant conditional medium can discard the effects of an oscillatory paracrine signal. I believe the elegant experiment shown in Figure 2E more precisely address this issue.

The reviewer is right in the sense that paracrine coupling of circadian oscillators would require a circadian paracrine signal, like shown in Finger et al., 2021, and that we provide sufficient experimental evidence of a mechanics- rather than paracrine-driven control of the RevVNP circadian oscillations. Specifically, by using micropatterning (Fig. 2E) and gap closure (Fig. 2A) we show that cells under the same paracrine medium are able to display acute differences in RevVNP expression. The experiment with conditioned medium, which is a traditional technique used in some papers in the field like in Noguchi et al., 2013, was performed to rule out the possibility that secreted factors, even if not circadian, could ultimately impact the low-density cells’ circadian clock. We will rephrase the manuscript to stress out this reasoning.

Finger AM, Jäschke S, del Olmo M, Hurwitz R, Granada AE, Herzel H & Kramer A (2021) Intercellular coupling between peripheral circadian oscillators by TGF-β signaling. Science Advances 7

Noguchi T, Wang LL & Welsh DK (2013) Fibroblast PER2 circadian rhythmicity depends on cell density. Journal of Biological Rhythms 28: 183–192

Data analysis methodology:

1. Single-cell circadian recordings like the ones analyzed here are characterized by noisy amplitude and non-sinusoidal waveforms with fluctuating period (Bieler et al., 2014; Feillet et al., 2014). The authors interpolate, smooth, detrend and normalize their data; operations that are known to introduce spectral artifacts that can mislead the interpretation of the power spectrum. Moreover, the time-series pre-processing operations described by the authors in the methods sections is incomplete and the authors should more explicitly describe all their operations with exact methods applied, filter parameters and time-windows sizes (if applicable). To validate their pre-processing steps the authors could provide their time-series analysis pipeline code and/or provide a few examples of raw versus pre-processed data together with their respective spectrums before and after pre-processing. In addition, the authors could provide their raw trace signal data together with the corresponding post-processed signal data as plain text files.

In our response to the reviewers, we will address this point exactly as requested by the reviewer. We will rewrite our methods section to explain better our analysis pipeline, clarifying that we do not apply detrending, that we resort rarely to interpolation of missing points, and stating the specifics of the standard low-pass filter we apply. We will then strengthen Supplementary Figure 1 with more examples of raw-data and processed data, and will provide raw trace signal data and the corresponding processed data to illustrate our approach.

1. The authors rely on Fourier analysis and a reasonable self-made definition of circadian strength named as "circadian power fraction". Using a stationary-based method for noisy non-stationary data can lead to inaccurate spectrum power estimations. As the current version of the manuscript does not provide any alternative/complementary analysis method nor we have any available raw signal data it is unclear if their analysis appropriately represents the circadian power. The authors could consider implementing complementary data-analysis strategies to validate their conclusions. Fortunately, there are multiple suitable data analysis strategies already available that are exactly designed for this kind of data (eg. (Price et al., 2008; Leise et al., 2012; Leise, 2013; Bieler et al., 2014; Mönke et al., 2020). This time-series analysis methods is a crucial step as all main results on this manuscript rely on the authors self-made definition of circadian power. This is particularly important as there is no standardized method in the circadian field to estimate circadian rhythmicity and/or circadian power of single-cell traces.

We will take this point into consideration by running a complementary analysis of our data with one of the methods recommended by the reviewer. Our choice is pyBOAT, as presented in Mönke et al. (2020), because on first inspection its implementation of the wavelet method appears to be the most suitable for our dataset type. If we find that our time-series are too short for these methods we will use the RAIN algorithm (Thaben and Westermark, 2014) instead.

Mönke G, Sorgenfrei FA, Schmal C & Granada AE (2020) Optimal time frequency analysis for biological data - pyBOAT Systems Biology

Thaben PF & Westermark PO (2014) Detecting Rhythms in Time Series with RAIN. J Biol Rhythms 29: 391–400

1. The authors mainly show circadian power fraction and analyze rhythmicity scores/powers. Is there the a chance that a rise in the basal expression level of Rev-erbα is reducing the rhythmicity score? Or to phrase it otherwise, the absolute amplitude may remain the same, but the relative amplitude may be reduced? Would that affect the FT analysis power scored? To clarify this the authors could provide an analysis of the relative amplitude in addition to the circadian intensity (as in Fig.1C).

Our analysis pipeline subtracts the mean signal from each cell’s intensity-time trace, and then divides each trace by its standard deviation. This procedure eliminates any bias due to basal expression of Rev-erbα. We will address this point by clarifying the methods section and providing examples in Supplementary Figure 1 of raw data with high-basal levels and low basal levels, showing their pre- and post-processed spectra.

Minor points by text-line:

YAP and TAZ should be introduced to the reader during introduction. by set a of proteins. Here the authors probably meant that cells were not reset nor entrained during the experiment. "..expression depends on..". This is a correlation, not proof of causation is shown until this point. This is an overstatement. Using the term "provoked" suggests a causal relationship not shown. Similarly last sentence "This result established.... is caused..". Again, this is an overstatement as only correlation is shown. According to their description the authors are not using any image-preprocessing steps, eg background subtraction or other filters. Is this correct? It is not clear what image metric for the single-cell signals are the authors using, eg. integrated nuclear intensity or mean/median nuclear intensity. I am not familiar with TrackMate but it might be possible to export and share with the readers the image-analysis pipeline used which would clarify any questions about image processing and signal extraction.

We thank the reviewer for pointing out all these minor points. We will address each one of them to make the paper clearer.

Regarding Reviewer #3:

The authors state in lines 163-165: 'This striking anticorrelation reveals that the robustness of the Rev-erbα circadian expression depends on the nucleocytoplasmic transport of YAP and its mechanosensitive regulation'. Although interesting, the data in figure 3 to which this statement refers is, as the authors identify, correlative, rather than causative. I would strongly suggest altering this statement to better reflect the data.

We will modify the text to eliminate this overstatement.

It looks to me as though all experiments were carried out in the same clonal reporter 3T3 line. To avoid possible issues with founder effects, I would ask that the authors repeat the initial experiment in figure 1B, and the associated analysis as in 1C-E with a different clonal 3T3 line. Hopefully this will not be very arduous, as the methods suggest that multiple clonal 3T3 reporter lines were made initially. With time to defrost, plate, record and analyse the data, I would hope that this would not take more than six weeks maximum.

We will perform the experiments regarding the cell density effect on the RevVNP oscillations (Fig. 1) in another clonal 3T3 line as the reviewer suggests. We have already initiated the experimental repeats with the alternative clone.

I would note that the custom software used for analysis does not appear to be generally available. I would assume that the authors would make this available upon request.

We will extend the explanation of our method as suggested by Reviewer #2 and make the code available to the community.

Experiments appear to have been adequately replicated in terms of n. However, the robustness of these findings would be supported though use of a different clonal reporter line, as discussed above.

We will solve this problem as stated above.

Statistical analysis is generally appropriate. I would suggest including statistical analysis in figures 3B and S4B to demonstrate that the pharmacological treatments are indeed having a statistically significant effect on the MAL and YAP nuclear/cytoplasmic ratio.

We will perform the corresponding statistical analysis on those data.

For Figure 4, it is not stated which statistical tests have been used, with only P values given in table S1. Please state which test has been used.

We will specify the statistical test used in the figure legend.

Furthermore, it would be valuable to see if it is possible to perform statistical analysis looking at the populations should in Figure 4A, to either support or refute the statement made in Line 189-90 that 'we overexpressed 5SA-S94A-YAP, a mutant version of YAP unable to interact with TEAD and observed that the cells recovered, to a large extent, both the RevVNP circadian power fraction and the REV-ERBα basal levels displayed by the wild-type high-density population'

The p-values corresponding to that dataset are represented in Table S1, but we will move them to the figure legend so the extent of the differences between the YAP mutants and the control becomes more noticeable. This applies too to the next comment of the reviewer.

Additionally, it is a little unclear to me why exact p values are reported in table S1. It seems that they might be better placed in the relevant figure legend.

Minor comments:

Although the authors took good care to try to ensure that there was minimal phase synchrony between cells, it would be good to see some analysis to confirm that these efforts were successful. This is of particular concern, given that many things that commonly happen during cell handling, such as temperature change and media change, even with conditioned media, can act to synchronise cells. Hopefully, this information should be available from your existing analysis.

All our experiments, except for the gap closure ones (which imply an unavoidable medium shock after the removal of the gasket where the cells are cultured to achieve high density) are carried out in a similar way (see Materials and Methods). This approach does not involve the typical shock of serum, dexamethasone, or other hormones, because we want to avoid biochemical signalling that could mask the “pure” effect of mechanics on the pathways that affect the circadian clock. In any case, a certain level of synchrony should not affect the analysis we perform, since this is single cell-based and does not consider the phase but the strength of its circadian frequency. But as requested by the reviewer we will analyze the phase signal and report the results if relevant to the project.

It would be informative to see both phase and period analysis for the data shown in figure 2C. Do cells at the edge show differences in relative synchrony following the removal of the PDMS barrier and Rev-erba induction? Is there a period difference between cells at the edge and those that remain confluent?

We agree with the referee that the “shock” received by the cells at the edge should work as a reset of their circadian phase and we have tried to analyse this effect. However, there are technical limitations that make this analysis difficult, mainly the short duration of the experiment and the fact that these cells transition very fast, upon gap closure, from a non-circadian to a circadian behaviour. We will attempt to better report this interesting effect by using the WAVECLOCK (Price et al., 2008) or the pyBOAT method (Mönke et al., 2020), suggested by Reviewer #2, which are designed to analyse non-stationary data.

Mönke G, Sorgenfrei FA, Schmal C & Granada AE (2020) Optimal time frequency analysis for biological data - pyBOAT Systems Biology

Price TS, Baggs JE, Curtis AM, Fitzgerald GA & Hogenesch JB (2008) WAVECLOCK: wavelet analysis of circadian oscillation. Bioinformatics 24: 2794–2795

Figure 2B - the text states that those cells far from the edge oscillate robustly thoughout the experiment, but this is not easy to see from this kymograph due to the dynamic range. Is there another way of presenting this that might make it easier to confirm?

We will calculate the circadian power fraction of the “bulk” cells as we do for the other conditions described in the manuscript. We can also show examples of individual traces if the average shown in Fig. 2C or the kymograph in Fig. 2B are not clear enough.

Figure 1D-E - the text provides periodicity for the high-density cells, but not the low density ones. Could you provide periodicity for both populations - do they differ?

We will represent in more detail the results of the frequency analysis on the low-density cells so the diversity of periods (frequencies) at this condition gets more evident.

Figure S3 - it is interesting to note the difference in population rhythmicity between the bulk and edge data here, which is not seen so clearly in cells without thymidine. Could the authors comment on this?

We agree with the referee that there is an obvious difference regarding RevVNP expression (mainly on the edge cells but also in the bulk) between the experiments with and without thymidine. We hypothesise this is due to the pronounced decrease in cell divisions in the presence of thymidine, which considerably slows down the gap closure and impacts the density of the entire cell population. We will comment this effect in the manuscript.

Line 148 - it is unclear here what is meant by 'the onset of circadian oscillations'. Could you rephrase this for clarity?

We will change that sentence.

Line 173 - a few words to highlight that Lats is a kinase and the function of YAP phosphorylation by Lats would aid clarity here. Similarly, explanation of the functional difference between the protein with 4 Serine to alanine mutations and 5 mutations and why both of these mutants were used would be helpful.

We will clarify this point following the reviewer’s suggestion.

Line 174 - for accuracy, this should perhaps read 'fibroblast circadian clock', as this work is only in 3T3 cells, and therefore may not apply more generally.

We will implement this change.

Line 202 - could you expand to explain the existing limitations of studying cell signalling cascades in synchronised cells? This is not clear to me. Thanks.

We will discuss the signalling effects caused by 50% serum shocks and other traditional ways to synchronise the cells as requested by the reviewer.

Figures 1D and 4B - the choice of colour range used in these kymographs is skewed towards the warmer colours, making it quite hard to discern differences between the groups. I would suggest using the cooler colour range for a greater proportion of the data set, to make rhythmicity, or lack of it, clearer to see.

We will invest further efforts to finding the optimal colour map and range for our datasets.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, the authors employ the NIH 3T3 fibroblast cell line to study the effect of cell density and the associated mechanical cues on cellular circadian rhythmicity. For this, they generate a Rev-erbα:VENUS line and, combined with constitutive nuclear mCherry expression, are able to track Rev-erbα: expression in single cells within populations of differing densities. Using overexpression of the transcriptional co-regulator YAP and specific mutants thereof, they suggest a role for YAP and its associated transcription factor family, TEAD, in the regulation of Rev-erbα expression under conditions of differing cell density.

Major comments:

• Are the key conclusions convincing? Yes, the major conclusions are supported by the data shown.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The authors state in lines 163-165: 'This striking anticorrelation reveals that the robustness of the Rev-erbα circadian expression depends on the nucleocytoplasmic transport of YAP and its mechanosensitive regulation'. Although interesting, the data in figure 3 to which this statement refers is, as the authors identify, correlative, rather than causative. I would strongly suggest altering this statement to better reflect the data.

• 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.

It looks to me as though all experiments were carried out in the same clonal reporter 3T3 line. To avoid possible issues with founder effects, I would ask that the authors repeat the initial experiment in figure 1B, and the associated analysis as in 1C-E with a different clonal 3T3 line. Hopefully this will not be very arduous, as the methods suggest that multiple clonal 3T3 reporter lines were made initially. With time to defrost, plate, record and analyse the data, I would hope that this would not take more than six weeks maximum.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes. I would note that the custom software used for analysis does not appear to be generally available. I would assume that the authors would make this available upon request.

• Are the experiments adequately replicated and statistical analysis adequate?

Experiments appear to have been adequately replicated in terms of n. However, the robustness of these findings would be supported though use of a different clonal reporter line, as discussed above.

Statistical analysis is generally appropriate. I would suggest including statistical analysis in figures 3B and S4B to demonstrate that the pharmacological treatments are indeed having a statistically significant effect on the MAL and YAP nuclear/cytoplasmic ratio.

For Figure 4, it is not stated which statistical tests have been used, with only P values given in table S1. Please state which test has been used.

Furthermore, it would be valuable to see if it is possible to perform statistical analysis looking at the populations should in Figure 4A, to either support or refute the statement made in Line 189-90 that 'we overexpressed 5SA-S94A-YAP, a mutant version of YAP unable to interact with TEAD and observed that the cells recovered, to a large extent, both the RevVNP circadian power fraction and the REV-ERBα basal levels displayed by the wild-type high-density population'

Additionally, it is a little unclear to me why exact p values are reported in table S1. It seems that they might be better placed in the relevant figure legend.

Minor comments:

• Specific experimental issues that are easily addressable. Although the authors took good care to try to ensure that there was minimal phase synchrony between cells, it would be good to see some analysis to confirm that these efforts were successful. This is of particular concern, given that many things that commonly happen during cell handling, such as temperature change and media change, even with conditioned media, can act to synchronise cells. Hopefully, this information should be available from your existing analysis.

It would be informative to see both phase and period analysis for the data shown in figure 2C. Do cells at the edge show differences in relative synchrony following the removal of the PDMS barrier and Rev-erba induction? Is there a period difference between cells at the edge and those that remain confluent?

• Are prior studies referenced appropriately?

To the best of my knowledge, yes.

• Are the text and figures clear and accurate?

Figure 2B - the text states that those cells far from the edge oscillate robustly thoughout the experiment, but this is not easy to see from this kymograph due to the dynamic range. Is there another way of presenting this that might make it easier to confirm?

Figure 1D-E - the text provides periodicity for the high-density cells, but not the low density ones. Could you provide periodicity for both populations - do they differ?

Figure S3 - it is interesting to note the difference in population rhythmicity between the bulk and edge data here, which is not seen so clearly in cells without thymidine. Could the authors comment on this?

Line 148 - it is unclear here what is meant by 'the onset of circadian oscillations'. Could you rephrase this for clarity?

Line 173 - a few words to highlight that Lats is a kinase and the function of YAP phosphorylation by Lats would aid clarity here. Similarly, explanation of the functional difference between the protein with 4 Serine to alanine mutations and 5 mutations and why both of these mutants were used would be helpful.

Line 174 - for accuracy, this should perhaps read 'fibroblast circadian clock', as this work is only in 3T3 cells, and therefore may not apply more generally.

Line 202 - could you expand to explain the existing limitations of studying cell signalling cascades in synchronised cells? This is not clear to me. Thanks.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Figures 1D and 4B - the choice of colour range used in these kymographs is skewed towards the warmer colours, making it quite hard to discern differences between the groups. I would suggest using the cooler colour range for a greater proportion of the data set, to make rhythmicity, or lack of it, clearer to see.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This work provides a potential mechanism for the modulation of cellular rhythmicity under conditions of varying cell density, a currently relatively understudied area to which the contribution made here will be valuable. However, the work is limited by its use of only one cell type (NIH 3T3) and one reporter (Rev-erb:VENUS), which makes the work difficult to generalise in the context of all cell types and environments that exist in a mammalian context.

• Place the work in the context of the existing literature (provide references, where appropriate).

Previous work has identified YAP activity as a mechanism of signalling growth substrate stiffness (Halder et al. 2012, Panciera et al. 2017). It has also been speculated, but not demonstrated, that YAP might influence circadian rhythmicity (Streuli and Meng, 2019). This work provides some initial evidence to support this speculation.

• State what audience might be interested in and influenced by the reported findings.

This work would be of genera; interest to those working on mammalian cellular circadian rhythmicity. Additionally, given YAP's status as an oncogene, this work would also be relevant to those considering circadian disruption in cancer.

• 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.

Mammalian circadian cell biology and biochemistry.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Abenza et al. investigate an important question of how the physical environment affects the properties of the individual circadian clocks. The authors utilize a set of clever experiments, pharmacological manipulations and data analysis techniques to unveil a potential role of YAP/TAZ in the circadian clock.

Major comments:

Effects on the circadian clock

1. The authors use the fluorescent reporter created by Nagoshi from sections of the Rev-erbα gene. This reporter is widely used to estimate relative circadian timing in individual cells but it does not provide direct information on the circadian clock activity. In other words, while Reverb rhythmic expression is driven by the clock, it is not known whether less-rhythmic or non-rhythmic expression or change in expression level of Rev-erbα is affecting the core clock. For example, it has been shown that Rev-erbα knock-down cells are rhythmic as long as Rev-erb-beta is present. Thus, one major shortcoming of the current version of the manuscript is the missing dissection between Rev-erbα rhythmicity/expression and the circadian clock. More concretely, it remains unclear whether the change in Rev-erbα expression is a direct effect or caused by a defect clock. Since the authors presume a direct effect of YAP/TAP on Rev-erb expression, the former is likely. If that is the case, the data could be interpreted as that (missing) mechanic stimuli can lead to nuclear YAP/TAZ, which rises the level of Rev-erbα (and maybe interfere with its rhythmic accumulation). Beyond Rev-erbα expression, there may or may not be an effect on the circadian clock (core clock, CCGs). With the current version we do not know since the authors do not look beyond Rev-erbα expression. Thus, the claims on circadian clock or circadian rhythms in their cells is not studied in this version of the manuscript. The current version is still very interesting and provides insights into the Rev-erbα modulation, but additional work would be needed to show links with the core clock machinery. For this the authors could show influence (or at least correlation) of the YAP/TAZ/REVERBA phenotype on the oscillations of core clock genes or clock-controlled genes. Either through the use of alternative (ideally constitutive) reporters (e.g. PER2, BMAL1, fluorescent or LUC), or/and by analyzing RNA/Protein of core clock genes or output genes. This would not be necessary for all experiments, but at least for some were its possible (e.g. experiments with drugs perturbations). Otherwise, any claim like "YAP/TAZ perturbs the circadian clock ..." or "the circadian clock deregulation in nuclear YAP-enriched cells" is potentially flawed and has to be removed/reformulated.

2. The authors aim to discard the possibility of paracrine signals by showing no increase in circadian power fraction of cells growing in low density with conditioned medium (Figure 2D). A paracrine signal coming from an oscillatory system is likely to oscillate and in that case, I do not see how growing cells in constant conditional medium can discard the effects of an oscillatory paracrine signal. I believe the elegant experiment shown in Figure 2E more precisely address this issue.

Data analysis methodology:

1. Single-cell circadian recordings like the ones analyzed here are characterized by noisy amplitude and non-sinusoidal waveforms with fluctuating period (Bieler et al., 2014; Feillet et al., 2014). The authors interpolate, smooth, detrend and normalize their data; operations that are known to introduce spectral artifacts that can mislead the interpretation of the power spectrum. Moreover, the time-series pre-processing operations described by the authors in the methods sections is incomplete and the authors should more explicitly describe all their operations with exact methods applied, filter parameters and time-windows sizes (if applicable). To validate their pre-processing steps the authors could provide their time-series analysis pipeline code and/or provide a few examples of raw versus pre-processed data together with their respective spectrums before and after pre-processing. In addition, the authors could provide their raw trace signal data together with the corresponding post-processed signal data as plain text files.

2. The authors rely on Fourier analysis and a reasonable self-made definition of circadian strength named as "circadian power fraction". Using a stationary-based method for noisy non-stationary data can lead to inaccurate spectrum power estimations. As the current version of the manuscript does not provide any alternative/complementary analysis method nor we have any available raw signal data it is unclear if their analysis appropriately represents the circadian power. The authors could consider implementing complementary data-analysis strategies to validate their conclusions. Fortunately, there are multiple suitable data analysis strategies already available that are exactly designed for this kind of data (eg. (Price et al., 2008; Leise et al., 2012; Leise, 2013; Bieler et al., 2014; Mönke et al., 2020). This time-series analysis methods is a crucial step as all main results on this manuscript rely on the authors self-made definition of circadian power. This is particularly important as there is no standardized method in the circadian field to estimate circadian rhythmicity and/or circadian power of single-cell traces.

3. The authors mainly show circadian power fraction and analyze rhythmicity scores/powers. Is there the a chance that a rise in the basal expression level of Rev-erbα is reducing the rhythmicity score? Or to phrase it otherwise, the absolute amplitude may remain the same, but the relative amplitude may be reduced? Would that affect the FT analysis power scored? To clarify this the authors could provide an analysis of the relative amplitude in addition to the circadian intensity (as in Fig.1C).

Minor points by text-line:

1. YAP and TAZ should be introduced to the reader during introduction.
2. by set a of proteins.
3. Here the authors probably meant that cells were not reset nor entrained during the experiment.
4. "..expression depends on..". This is a correlation, not proof of causation is shown until this point. This is an overstatement.
5. Using the term "provoked" suggests a causal relationship not shown.
6. Similarly last sentence "This result established.... is caused..". Again, this is an overstatement as only correlation is shown.
7. According to their description the authors are not using any image-preprocessing steps, eg background subtraction or other filters. Is this correct?
8. It is not clear what image metric for the single-cell signals are the authors using, eg. integrated nuclear intensity or mean/median nuclear intensity. I am not familiar with TrackMate but it might be possible to export and share with the readers the image-analysis pipeline used which would clarify any questions about image processing and signal extraction.

References:

1. Bieler, J, Cannavo, R, Gustafson, K, Gobet, C, Gatfield, D, and Naef, F (2014). Robust synchronization of coupled circadian and cell cycle oscillators in single mammalian cells. Mol Syst Biol 10, 739.

2. Leise, TL (2013). Wavelet analysis of circadian and ultradian behavioral rhythms. J Circadian Rhythms 11, 5.

3. Leise, TL, Wang, CW, Gitis, PJ, and Welsh, DK (2012). Persistent Cell-Autonomous Circadian Oscillations in Fibroblasts Revealed by Six-Week Single-Cell Imaging of PER2::LUC Bioluminescence. PLoS One 7, 1-10.

4. Mönke, G, Sorgenfrei, F, Schmal, C, and Granada, A (2020). Optimal time frequency analysis for biological data - pyBOAT. BioRxiv 179, 985-986.

5. Price, TS, Baggs, JE, Curtis, AM, FitzGerald, GA, and Hogenesch, JB (2008). WAVECLOCK: wavelet analysis of circadian oscillation. Bioinformatics 24, 2794-2795.

Significance

I believe this manuscript is of high significant both for the circadian as well as the mechanobiology fields. Readers from single-cell signalling studies will also be very interested in this work.

To my knowledge the discussed link has not been studied before at single cell level, which as the authors show can provide multiple new insights.

I do work with similar single-cell signals, have broad expertise in microscopy, image analysis methods, time series analysis, and the circadian clock mechanisms but very little experience in mechanobiology.

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Referee #1

Evidence, reproducibility and clarity

Here Abenza & Rossetti et al. show that in 3T3 fibroblasts, the circadian clock depends on cell density, correlates with YAP activity, and further demonstrate that circadian power fraction is suppressed by genetic YAP activation (5SA), but is rescued by expression of 5SA YAP without the tead-binding domain. This is a striking study on an important question; however, the data do not directly support the conclusions and the title of the paper. These conclusions/title should be altered, or supported with additional experiments, as detailed below:

Major Critiques:

1. On "mechanical control": The authors show changes in circadian power fraction with changes in YAP and with cytoskeletal inhibitors, but there are no properly-controlled experiments that directly perturb mechanics. The authors show a correlation between YAP nuclear/cytoplasmic ratio and circadian power, but YAP N/C alone is not a readout of mechanotrasndcution, per se. The authors have shown two different experiments where cells are cultured on a stiff (30kPa) substrate and soft substrate (300Pa), but they do not shown a direct comparison of YAP nuclear localization and circadian power under these two conditions in the same experiment. Direct, controlled perturbation of mechanical cues is necessary to support the title's use of the phrase "mechanical control."

2. On "via YAP/TAZ": In addition to above, it is necessary to show that the changes in Circadian power fraction induced by mechanical cues in fact require YAP/TAZ signaling. Thus, an experiment comparing soft (300Pa) substrate with Stiff (30kPa) substrate in the presence or absence of YAP/TAZ is necessary to state that YAP and TAZ are the mechanistic mediators of mechanical cues on the clock.

3. While the TEAD-binding domain mutant experiment is elegant, to claim that TEAD is the transcriptional mediator, it must be demonstrated that this mutant indeed fails to induce TEAD-mediated transcription. This could be simply executed by demonstrating that the CCD mutant expresses reduced CTGF and Cyr61 (for example), compared to the 5SA, under these conditions. Further, endogenous YAP is still active and available to bind to TEAD in this system, which should be discussed.

4. In Figure 3a: The cell perimeter needs to be shown either by actin staining or by brightfield images. The manually marking of cell boundaries is insufficient, specifically because the drugs used in this experiment affect the cytoskeleton. It would be very helpful to see this via actin staining or in the least with brightfield images.

Significance

This is an exciting paper that potentially links mechanotransduction to the circadian clock. While my group is not focused on circadian rhythms, and I don't have the background to comment on the measurements or robustness of circadian power, the idea is striking and significant.

I strongly recommend inclusion of loss-of-function approaches (either genetic or pharmacologic) in addition to the gain-of-function methods employed here to support the necessity of YAP/TAZ signaling. Also, appropriately controlled experiments to show true mechanical effects on the circadian clock are necessary.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): ____ *A significant criticism of the paper is an assumption that readers will be familiar with all of the findings in the author's previous 2016 paper and the PGL-1 papers by Aoki et al. Minimal context is given for each approach. *

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

*Some conclusions are not well supported and require further analysis, proper controls, and more extensive descriptions of the experiments performed. *

We have addressed the reviewer’s concerns as detailed below.

Most importantly, the central conclusion and title of the paper is that composition can buffer the dynamics of individual proteins within liquid-like condensates. In other words, in vitro condensation assays often do not recapitulate LLPS behavior in vivo. That said, the findings in this study would be significantly strengthened and complemented by observing endogenously tagged PGL-3 and PGL-3 mutants in living worms, considering the efficiency of using CRISPR in C. elegans to insert tags and make precise mutations.

The original manuscript already contained data where we microinjected wild-type PGL-3 and mutant PGL-3 proteins (recombinantly purified) into adult C. elegans gonads to assay how the P granule phase supports diffusion of these proteins.

In the revised version, we now include additional data which shows “dynamics buffering” in transgenic worms generated using CRISPR/Cas9 technology. Briefly, we used CRISPR/Cas9 to generate transgenic C. elegans which expresses PGL-3-mEGFP or PGL-3(D425-452)-mEGFP from the native pgl-3 locus. In vitro, wild-type PGL-3-mEGFP protein generates liquid-like condensates. On the other hand, the recombinantly purified PGL-3(D425-452)-mEGFP protein generates condensates that are non-dynamic. In contrast to these observations in vitro, both wild-type PGL-3-mEGFP and PGL-3(D425-452)-mEGFP show similar dynamics (half-time of FRAP recovery) within P granules in vivo.

*To improve readability, the introduction to P granules should be expanded, and include the reasons for looking at the nematode-specific PGL-3 protein among all the other known P granule proteins. A recap of previous findings on PGL-3 phase separation, in vivo and in vitro, is warranted, starting with the significant results of Saha et al 2016. Setting up the investigative questions in the context of recent work on PGL-1 (Aoki, et al) is also necessary. *

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

The physiological concentration of PGL-3 should be more transparent, including why some experiments in this study are done at physiological concentrations while others are not. Describing why salt concentrations, crowding agents, and protein abundance are similar or different for each experiment is necessary and relevant. For example, after showing in Figure 1 that PGL-3 protein phase separates, the paragraph starting on line 161 says that it was previously shown that PGL-3 doesn't phase separate at physiological concentrations without RNA. One has to go back to Figure 1 to realize it was done differently than Figure 2 and Saha 2016.

The concentrations of PGL-3 protein and use of crowding agents (if any) have already been specified within figures or figure legends. Salt concentrations used are specified within figure legends or materials and methods section.

We have added the following paragraph to the materials and methods section of the revised manuscript.

“Saha et al. 2016 showed that at physiological concentrations (approx. 1 mM), the PGL-3 protein is unable to phase separate into condensates. At these concentrations, mRNA promotes phase separation of PGL-3. To assay for mRNA-dependence of condensate assembly, it is therefore essential to use physiological concentrations of the PGL-3 protein or mutants (e.g. Figure 2). However, these condensates are generally too small to assay rate of internal rearrangement of PGL-3 molecules within condensates using fluorescence recovery after photobleaching experiments. Therefore, to generate large condensates for measuring internal rearrangement of PGL-3 or mutant molecules, we primarily used higher concentrations of these proteins where binding to RNA is not essential for phase separation. However, to mimic the in vivo P granule phase as closely as possible, we generally added constituent proteins in proportion to their in vivo abundance estimated in Saha et al. 2016.”

The added paragraph in the Introduction section of the revised manuscript may be helpful to the readers. * *

*Statements in the same paragraph like "in contrast to full-length PGL-3, mRNA does not support phase separation..." should be qualified by stating the concentration observed, with or without salts or other crowding agents. Similarly, line 230 "suggests that interactions involving the disordered C-terminal region of PGL-3 are not essential for the fast dynamics" and should be qualified with "at non-physiological concentrations and with XX crowding agents or salt concentration." It would be more consistent if physiological concentrations were consistent from figure to figure, as extra variables weaken some of the stated conclusions. *

We thank the reviewer for this suggestion. However, we feel the statements (without full experimental details within main text) help convey the conceptual essence of the findings better. Of course, all these statements contain reference to figures or prior publications which provide relevant details about experimental conditions.

*The 2010 review reference stating that there are 40 P granule enriched proteins is outdated. More recent reviews put the number much higher. This is relevant because the approach to put PGL-3 in a more physiological environment by including just PGL-1, GLH-1 and mRNA with the condensate assays, out of ~100 P granule enriched proteins, may not be sufficient to conclude "that the influence of complex composition on dynamics is modest" (line 223), or imply that the multicomponent nature of the P granule is reconstituted by adding these components (line 355). *

We revised the text to indicate that P granules contain approx. 70 proteins and added appropriate references.

• *

Based on current information of constitutive P granule components (PGL-1, PGL-3, GLH-1, GLH-2, GLH-3, GLH-4, DEPS-1, MIP-1 and mRNA), (Kawasaki et al, 1998, 2004; Spike et al, 2008a, 2008b; Price et al, 2021; Cipriani et al, 2021; Phillips & Updike, 2022) we reconstituted P granule-like phase in vitro with mRNA, PGL- and GLH- proteins that likely constitute the most abundant components within P granules in vivo (based on concentration estimates in Saha et al. 2016).

We do appreciate the reviewer’s comment that more components can be added to our in vitro reconstitution in addition to the limited set of components used in our study. However, we feel it is interesting to observe that a limited set of components can support dynamics buffering (the main message of the paper). Further, the complementary in vivo experiments show that the P granule phase can also support dynamics buffering.

*Figure 1C needs to include PGL-3(370-693) in the analysis. Figure 1E is also incomplete without a comparison of FRAP recovery between PGL-3(1-452) and full PGL-3 as the control.

*

Fig. 1c already includes data with PGL-3 (370-693) [top row, central panel]. FRAP recovery data with full-length PGL-3 is already available in Supplementary Fig. 2c, g.

*Figure 4C is missing an essential control where PGL-3 and S1 FRAP is performed without PGL-1, GLH-1, and mRNA. *

In the revised version, we have added Supplementary Fig. 5f, where FRAP recovery of the following condensates are plotted together: 1) PGL-3 alone, 2) S1 alone, 3) PGL-3 + PGL-1, GLH-1 and mRNA, 4) S1 + PGL-1, GLH-1 and mRNA.

*It would also help show sup Fig4A in the main figure to show concentration dependence. *

We revised Fig. 4 to address the reviewer’s suggestion.

Consider adding subtitles to supplementary figures.

We considered the suggestion but felt it may not be essential.

*M&M should include an explanation for statistical analysis *

We added a paragraph describing statistical analysis within the Materials and Methods section.

*CROSS-CONSULTATION COMMENTS I am also in agreement with the comments and critiques of reviewers 2 and 3.

* Reviewer #1 (Significance (Required)): The paper by Saha and colleagues investigate the in vitro liquid-liquid phase separation propensity of a P granule protein PGL-3 and its structural domains. The findings largely replicate and support the phase-separation properties of a paralogous protein called PGL-1, as recently described by Aoki et al. 2021. Furthermore, they show that the dynamics demonstrated by recombinant PGL-3 may be maintained or buffered by the complex composition of P granules.

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

*Jelenic et al. describe the effect of partner proteins on the FRAP dynamics of recombinant PGL-3 protein and variants in in vitro condensates and C elegans p-granules. The study shows that the N terminal a-helical dimerization domains is required for condensate formation and modulate of it alters aggregation and the FRAP dynamics of its condensates. Interestingly, a construct including the entire IDR region (370-693) by itself does not phase separate on its own at these conditions. The K126E K129E mutant (known previously to disrupt dimerization) and the deletion mutant abrogate llps. A mutant construct that shuffles the sequence in the region 423-453 called S1 here reduces the helicity and the condensate FRAP dynamics but recovered in the presence of a few P granule components. Also, the reduced dynamics of partially unfolded PGL-3 condensates are also rescued by the p-granule components to a certain degree of the unfolded PGL3 concentrations. This threshold concentration for recovering the condensate dynamics is further reduced in the helix reducing S1 mutant, which is also dependent on the number and the nature of P granule components.

Overall, the study aims to probe how "composition can buffer protein dynamics within liquid-like condensates" - yet several underlying aspects of the study do not fully support that conclusion. The introduction does not sufficiently introduce the known structural information of the two dimerization domains in C elegans PGL proteins for which structures are known. The region is discussed as "alpha helical" but really there are two evolutionarily conserved independently folding dimerization domains (referring to the mutants as "reduced alpha helicity" is not helpful - these are mutations that destabilize a folded domain).*

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

*Additionally, the abstract and introduction ignore the aspects of aggregation (touched on in discussion) - this is likely what the disruption to the helical region in residue 450 region is doing (the helix is not on the dimer interface based on homology / sequence identity to the crystal structure of PGL-1 central dimerization domain. *

We think elucidating the molecular mechanism of apparent aggregation of PGL-3 (D425-452) could be an interesting direction for future investigation. Here, we focused our analysis predominantly on the mutant S1 since it generates liquid-like condensates with ~20- fold slower dynamics (compared to wild-type) in contrast to non-dynamic condensates/aggregates. Therefore, influence of other P granule components on the dynamics of PGL-3 in liquid-like condensates is easier to address using the mutant S1 rather than PGL-3 (D425-452). We didn’t find evidence that S1 aggregates as we did not detect aggregates of S1 molecules using fluorescence confocal microscopy and the slow dynamics in condensates of S1 does not change significantly over 24 h (Supplementary Fig. 3f).

However, in the revised version, we now include additional in vivo data with C. elegans expressing the aggregation-prone PGL-3 (D425-452)-mEGFP. Briefly, we used CRISPR/Cas9 to generate transgenic C. elegans which expresses PGL-3-mEGFP or PGL-3(D425-452)-mEGFP from the native pgl-3 locus. In vitro, wild-type PGL-3-mEGFP protein generates liquid-like condensates. On the other hand, the recombinantly purified PGL-3(D425-452)-mEGFP protein generates condensates that are non-dynamic. In contrast to these observations in vitro, both wild-type PGL-3-mEGFP and PGL-3(D425-452)-mEGFP show similar dynamics (half-time of FRAP recovery) within P granules in vivo.

Finally, the "dynamics buffering" is not really clearly established and could also be explained as small concentrations of aggregated proteins act like clients while increasing the concentration results in aggregation and "cross linking" in the entire droplet - and this concentration is never achieved in the in worm experiments so it is not clear. In other words, the change in FRAP dynamics not observed in worms is perhaps not surprising if small amount of recombinant proteins are incorporated into the granules. *

*

Data with the S1 mutant establishes that dynamics buffering can be observed in condensates with different sets of additives both in vitro (Fig. 5a, b) and in vivo (Fig. 4a, b). Further, data with condensates of S1 containing the additives PGL-3 (K126E K129E) or S1 (K126E K129E) demonstrate that dynamics (half-time of FRAP recovery) within S1 condensates, and in turn “dynamics buffering” depend on inter-molecular interactions. With respect to the hypothesis proposed by the reviewer, we did not detect aggregates within S1 condensates using confocal fluorescence microscopy.

In contrast to S1 condensates, condensates containing partially unfolded PGL-3-mEGFP together with PGL-1, GLH-1 and mRNA showed spatial inhomogeneities in fluorescence signal throughout the condensate (Fig. 4g). We have not tested if areas with higher fluorescence signal represent aggregates. It is a possibility that the partially unfolded PGL-3-mEGFP fluorescence signal becomes more homogeneous if higher concentrations of additives (PGL-1, GLH-1 and mRNA) are used. However, the presented data demonstrate the significant effect of the P granule components (PGL-1, GLH-1 and mRNA) on the FRAP recovery rate of partially unfolded PGL-3-mEGFP in condensates (compare figures Fig. 3e and Fig. 4g).

However, consistent with dynamics buffering, the P granule phase in vivo supports wild-type dynamics of different PGL-3 constructs over a range of concentrations - PGL-3(D425-452)-mEGFP at physiological concentration (CRISPR transgenic strain, Fig. 4e) or at higher concentrations (microinjected S1 and partially unfolded PGL-3-mEGFP, Fig. 4b).

• *

*It is also not clear what the mechanism of the changes is - is the protein driven to fold more properly (despite S1 disruption of its conserved sequence) inside the condensate? Does it still self interact and act as a dimerization domain? Does this change disrupt interactions? *

We agree with the reviewer that identifying the precise structural changes of the S1 protein within the condensate vs. dilute phase could be an interesting direction for future investigation. However, we have already discussed the issues raised by the reviewer in the original manuscript.

“Our data is consistent with the model that other regions of S1 molecules cooperate with residues 425-452 (shuffled) to generate stronger inter-molecular interactions. For instance, addition of the mutant S1 (K126E K129E) enhances dynamics of S1 within condensates in contrast to maintaining the slower dynamics observed within condensates of S1 alone. This suggests that the interactions disrupted by the mutations K126E and K129E also contribute to slow S1 dynamics. One possibility is that interactions involving the residues K126 and K129 favor S1 conformations that enhance 425-452 (shuffled)-dependent interactions. Indeed, the mutations K126E K129E have been reported to interfere with interactions among N-termini of PGL-3 molecules (Aoki et al, 2021). While two self-association domains within the α-helical N-terminus of PGL-3 have been mapped (Aoki et al, 2021, 2016), structural insights into those associations are limited. However, PGL-3 shares significant sequence similarity with another protein PGL-1. Crystal structures are available for fragments of the PGL-1 protein that show the two self-association domains at the N-terminus are predominantly α-helical and globular in nature (Aoki et al, 2016, 2021). Therefore, one possibility is that shuffling the sequence 425-452 of PGL-3 or heat-induced unfolding of PGL-3 exposes hydrophobic residues that become available to participate in inter-molecular interactions.”

What is the real mechanism by which PGL-3 phase separates if not via the disordered domains? *

*

We agree with the reviewer that elucidating the detailed mechanism of phase separation of PGL-3 is an interesting direction for future investigation. However, we feel this is not required to support the main message of this manuscript.

Throughout the manuscript, the term "dynamics" is used to indicate FRAP, but it would be better to define what is meant (diffusion of PGL-3 in condensates) instead of using dynamics a term that could mean many things. Secondly, FRAP cannot directly measure liquidity etc (see recent critiques by McSwiggen elife 2019, etc) so it is better to be cautious in the claims. Finally, discussing "dyanmics buffering" adds more terminology where it is not needed - perhaps say "changes to diffusion of PGL-3 in condensates".

We feel it is useful to introduce a term that describes our observation. To our knowledge, our observation is novel and therefore requires a new term to describe it.

However, we do appreciate the concern raised by the reviewer. We used a more generic term “dynamics buffering” in contrast to the more specific “diffusion buffering” since we did not directly estimate diffusion behavior at the ‘single-molecule’ level. However, we already described what we mean by “dynamics buffering” in the text as follows.

“We used condensates of similar size for our analysis (average ± 1 SD of diameter of condensates are 6.4 ± 1.7 mm (Fig. 5a) and 5.9 ± 0.4 mm (Fig. 5b)). Therefore, dynamics buffering here is likely to represent similar diffusion rates of S1 within condensates.”

• *

*The "N-terminus" is not 65% of the protein. One could define this as the N-terminal domain, but again there are two clear folded domains in the first 65% of the protein and this needs to be described better. *

We revised the text to replace the terms “N-terminus” and “N-terminal domain” to “N-terminal fragment”.

*The description of "stickers" and the references to tau and hnRNPA1 are confusing as this is a predominantly ordered domain while those are IDRs. *

• *

We feel this is important as it aids discussing our work in the context of current literature describing the mechanisms of macromolecular phase separation.

The suggestion in the discussion that "P granule components support dynamics by participating in intermolecular interactions wth PGL-3-mEGFP molecules" is not well supported because no interaction assays are performed and no mutaitons are made that disrupt these interactions to test this.

Indeed, we have not conducted interaction assays or mutational analysis to directly test this. However, our detailed analysis with the S1 mutant supports this suggestion.

While partially unfolded PGL-3-mEGFP molecules lose 30% of a-helicity, the a-helicity of the S1 mutant is reduced by 15% compared to wild-type PGL-3. Data with S1 and partially unfolded PGL-3-mEGFP molecules show that loss of a-helicity correlates with slower diffusion of protein molecules within condensates. Using the mutants PGL-3 (K126E K129E) and S1 (K126E K129E), we show that diffusion rate of S1 molecules within condensates depend on inter-molecular interactions, and presence of other P granule components support faster diffusion rate of S1 molecules within condensates. Therefore, we feel it is safe to speculate that intermolecular interactions with P granule components can support dynamics of a “more unfolded” (compared to S1) version of PGL-3 molecule. * *

*More detailed analysis of some of the claims: Claim 1: An a-helical region mediates the phase separation of PGL-3, and the C-terminal disordered region by itself does not phase separate. The N-terminal dimerization is essential for LLPS. The C-terminal IDR interactions with mRNA facilitate the LLPS. Comments: The authors show sufficient experimental data using microscopy and FRAP on truncated constructs with the N-terminal and C-terminal regions - but see above regarding how these are described - a proper domain structure with the folded domains shown and the RGG motifs highlighted should be added and integrated throughout the discussion. *

In the revised version of the manuscript, we described the predicted PGL-3 domains within a paragraph in the introduction: “The interactions that support phase separation of the PGL-3 protein remains unclear. Structural studies on the orthologous PGL-1 protein revealed two dimerization domains. This raises the possibility that PGL-3 also contains similar dimerization domains, and phase separation depends on interactions involving these domains.”

Our Fig. 1a already includes the schematic representation of PGL-3 with predicted N-terminal and Central Dimerization domains and RGG repeats.

*They show that the N-terminus is necessary and adequate for LLPS, and the C-terminus by itself does not phase separate. But, how does the N-terminal domains phase separate? This is not explained - what are the interactions? *

• *

Also, a di-mutant (K126E K129E) that is known, and also authors use SEC-MALS to show their N-terminal construct is consistent with the published results. Disrupting the n-terminal dimerization prevents phase separation, suggesting the importance of these residues in the N-terminus for self-assembly and LLPS. The Microscopy data backs the claim that the mRNA-mediated LLPS is facilitated by binding with C-terminus. However, the m-RNA binding to IDR is not sufficient for LLPS. Yet, the authors do not explain how higher salt prevents phase separation - again the mechanism of phase separation is unclear. Is it multivalent interaction of the two dimerization domains? A basic model (that is tested) would be important.

We agree with the reviewer that elucidating the detailed mechanism of phase separation of PGL-3 is an interesting direction for future investigation. However, we feel this is not required to support the main message of this manuscript.

However, our manuscript already provides some relevant insights as follows.

“To investigate the underlying mechanism further, we began by testing if the N-terminal α-helical region of PGL-3 can self-associate. Our analysis using size exclusion chromatography followed by multi-angle light scattering (SEC-MALS) showed that this PGL-3 fragment 1-452 forms a dimer (Supplementary Fig. 2f). Mutation of two residues (K126E K129E) have been shown to interfere with interactions among the N-termini of PGL-3 molecules (Aoki et al, 2021). We mutated these two residues within the full-length PGL-3 protein (K126E K129E) (Fig. 1a) and found that this mutant PGL-3 (K126E K129E) protein cannot phase separate even at high protein concentrations up to ~130 µM (Fig. 1b, c). Addition of mRNA does not trigger phase separation of this protein at physiological concentrations either (Fig. 2a, b). Taken together, our data is consistent with a model where association among folded N-termini of PGL-3 molecules is essential for phase separation.”

A likely possibility is that phase separation of PGL-3 depends on electrostatic inter-molecular interactions among the folded N-terminal fragment of PGL-3 molecules. Therefore, high salt prevents phase separation.

Are the tags removed to ensure that phase separation is not caused by tags or remaining linker regions? Is the protein purified to be without nucleic acid contamination or other purity metrics?

Most of the experiments were done with only 5% of total protein tagged with 6x-His-mEGFP. No additional tags were present on the constructs. For recombinant expression and purification, proteins were cloned such that it is possible to remove the 6xHis-mEGFP tag following treatment with TEV protease. Following removal of the 6xHis-mEGFP tag, the residual linker is just two amino acid residues long. We used 100% tagged-protein for our experiments only in very few cases (indicated in the figure legends).

To demonstrate purity of recombinant proteins, SDS-PAGE gels with all protein constructs used in this study are shown in Supplementary Fig. 1.

To minimize contamination of nucleic acids, we treated samples with Benzonase during the course of purification.

To assess the extent of nucleic acid contamination, the ratio of absorbance at 260 nm and 280 nm (A260/A280) was monitored. In exceptional cases with high A260/A280 values, we analyzed samples further by purifying RNA from the sample using RNA purification kit (Qiagen) and found that RNA represented 1% or less of the sample mass.* *

Claim2: The N-terminal a-helical region modulates the dynamics within condensates. The IDR region has minimal effect on the fast dynamics of PGL-3. Comments: The authors show that the full-length PGL-3 condensates have modest influence of components by comparing the FRAP half times with or without the P granule components, including mRNA. However, have the authors tried this in the presence of mRNAs for the constructs lacking the IDRs as they have several RGG domains and bind with mRNA and are likely to change the dynamics.

We thank the reviewer for this suggestion. However, this experiment is not essential to support the claim made in the context of homotypic condensates of PGL-3 : “The N-terminal a-helical region modulates the dynamics within condensates. The IDR region has minimal effect on the fast dynamics of PGL-3.”

*The authors report the importance of the N-terminal a-helical region by making a construct that lacks/disrupts a part of the helices lowers the thermal stability and significantly lowers the dynamics of the condensates. Also unfolding of helices is shown to reduce the dynamics. One primary concern is whether these "rescued" protein dynamics imply protein functionality. *

An assay of “functionality” e.g. an enzymatic activity of the PGL-3 protein is not available.

However, we compared the fecundity of C. elegans worms expressing from the native pgl-3 locus, PGL-3-mEGFP or the mutant protein PGL-3(D425-452)-mEGFP, to assay the functionality of P granules in these strains. We found that worms of both genotypes produced similar number of offspring (Fig. 4d). This suggests that deletion of residues 425-452 of PGL-3 does not result in significant loss of function of P granules.

Are these semi denatured proteins refolded in the presence of P-granule components?

We feel that identifying the precise structural changes of the semi-denatured PGL-3 proteins within the condensate vs. dilute phase could be an interesting direction for future investigation.

Finally, it is not clear why the authors chose to disrupt folding of the central dimerization domain?

The manuscript included a paragraph to describe the rationale.

“This suggests that interactions involving the disordered C-terminal region of PGL-3 are not essential for the fast dynamics within condensates. Therefore, we addressed the role of the N-terminal α-helical region (1-452) in driving dynamics. In order to avoid engineering mutations that result in significant misfolding of PGL-3 and concomitant loss of its ability to phase separate, we focused our mutational analysis close to the junction of the folded N-terminus and the disordered C-terminus of PGL-3. Surprisingly, we found that a full-length PGL-3 construct (D425-452) that lacks only 27 residues phase separates into condensates that are non-dynamic (Fig. 3a, c). Sequence analysis of the PGL-3 protein predicts that this region 425-452 spans two α-helices (one complete helix and fraction of a second helix) (Supplementary Fig. 3d). We generated a PGL-3 construct (hereafter called ‘S1’) (Fig. 3a) in which the sequence in the region, 425-452, is shuffled while keeping the overall amino acid composition unchanged. We found that S1 phase separates into condensates that are 20- fold less dynamic than with wild-type PGL-3 (Fig. 3d, Supplementary Fig. 3c).”

Saying that "reduced alpha-helicity of PGL-3 correlates with slower dynamics in condensates" may be factual in these assays but "correlation" should be expanded upon to include mechanism and to me it seems that the statement should read "aggregation of PGL-3 causes slower dynamics in condensates" (both the partially destabilized mutant and the fully unfolded WT show similar effects perhaps to different degrees).

We feel that identifying the precise structural changes of the semi-denatured PGL-3 proteins within the condensate vs. dilute phase could be an interesting direction for future investigation.

We did not use the term "aggregation" since we did not detect aggregates of S1 molecules using fluorescence confocal microscopy.

*CROSS-CONSULTATION COMMENTS I agree with the other reviewer's comments and critiques, I have concerns about the biological relevance and also the biophysical mechanisms. Reflecting on the other reviewers' comments, the papers could provide more depth in one or both of these areas to come to firm conclusions that are either revealing about PGL biology or elucidate a (possible) general biophysical mechanism. *

In the revised version, we now include additional data which shows “dynamics buffering” in transgenic worms generated using CRISPR/Cas9 technology. Briefly, we used CRISPR/Cas9 to generate transgenic C. elegans which expresses PGL-3-mEGFP or PGL-3(D425-452)-mEGFP from the native pgl-3 locus. In vitro, wild-type PGL-3-mEGFP protein generates liquid-like condensates. On the other hand, the recombinantly purified PGL-3(D425-452)-mEGFP protein generates condensates that are non-dynamic. In contrast to these observations in vitro, both wild-type PGL-3-mEGFP and PGL-3(D425-452)-mEGFP show similar dynamics (half-time of FRAP recovery) within P granules in vivo.

Reviewer #2 (Significance (Required)): *Hence, although the authors shows how inclusion of other components can alter the one protein component phase separation, this is done with entirely artificial means of destabilizing the fold of one of the domains which likely leads to aggregation. So the true impact of the work is hard to understand because the mutations impact on the basic biophysical properties of the domain (stability, interaction) are not completely characterized and the reason for disrupting this folding is not clear. *

A major impact of our work is elucidation of a novel “dynamics buffering” property within biomolecular condensates in vitro. Our in vivo data is consistent with this finding.

• *

We have chosen two orthogonal ways of perturbing the PGL-3 protein (i.e. mutations and temperature-dependent unfolding) to assay the effect on diffusion rate against different levels of perturbation (e.g. 30% loss of a-helicity in heat-denatured PGL-3-mEGFP vs. 15% loss of a-helicity in the S1 mutant, compared to wild-type PGL-3). Studying the phase separation behavior of these “artificially-generated” constructs provided the understanding that dynamics of PGL-3 in condensates depends on inter-molecular interactions, and slower dynamics generally correlate with stronger inter-molecular interactions. Further, interactions among two or more P granule components can buffer against large change in dynamics / aggregation within the P granule phase. These insights may lay the groundwork for addressing how more “natural” modifications (e.g., post-translational modifications, high local concentration of “sticky” molecules) may influence dynamics within biomolecular condensates in vivo.

Based on current knowledge of P granule composition, chaperone proteins (e.g. heat-shock family proteins) do not show abundant concentration within P granules. However, it is unclear if chaperone proteins are completely excluded from the P granule phase. Therefore, we speculate that weak interactions among two or more non-chaperone proteins contribute significantly to “dynamics buffering” within the P granule phase in vivo.

In the discussion section of the manuscript, we had speculated that “dynamics buffering” may potentially explain observations reported in the nucleolus: “Similarly, interactions among components could be a potential mechanism of storage of misfolding-prone proteins in non-aggregated state within the liquid-like nucleolus under stress in vivo (Frottin et al, 2019).”

Our finding is also relevant in the context of synthetic biology with applications that require steady diffusion rate of macromolecules during biochemical reactions within biomolecular condensates.

• *

My field of expertise is protein phase separation and protein structure. * *

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

Summary: P granules are liquid condensates found in the developing germlines and embryos of C. elegans. Prior work by the authors and others have established P granules as a tractable model to investigate the basic biophysical properties of liquid condensates. Much of the prior published work focused on specific P granule scaffold proteins, PGL-1 and PGL-3. How attributes of these PGL proteins and the effect of other P granule components affect condensate properties is not fully understood. Here, Jelenic, et al. probe the biophysical properties of PGL-3. Using recombinant protein, they show that an N-terminal, alpha-helical region of PGL-3 is sufficient for liquid condensate formation and that N-terminal assembly is required for this formation. Creation of a scrambled alpha-helical region in PGL-3 and heat treatment affects PGL-3 fluidity. This fluidity can be "rescued" in vivo and in vitro with the inclusion of other P granule factors, including wildtype PGL-3, PGL-1, GLH-1 and mRNA. The authors note an inverse correlation between fluidity and mutant PGL-3 fluorescent intensity. They propose a model that heterotypic compositions of condensates can buffer their fluidity against components with stronger multivalent interactions. *

MAJOR: 1. PGL-3 is a fantastic model to study the biophysical properties of a liquid condensate. But as the authors address in their discussion, the S1 mutant will likely affect the central domain folding, at its minimum causing exposure of a hydrophobic surface not typically exposed in biology. These helices are found at the terminal portion of the domain determined in the crystal structure and as depicted in the authors' Figure 1A. While the cause of S1's enhanced molecular interactions does not affect the in vitro work presented in this manuscript, it does affect how the conclusions connect to the biological nature of P granules and liquid condensates more generally. *

We have chosen two orthogonal ways of perturbing the PGL-3 protein (i.e. mutations and temperature-dependent unfolding) to assay the effect on diffusion rate against different levels of perturbation (e.g. 30% loss of a-helicity in heat-denatured PGL-3-mEGFP vs. 15% loss of a-helicity in the S1 mutant, compared to wild-type PGL-3). Studying the phase separation behavior of these “artificial” constructs provided the understanding that dynamics of PGL-3 in condensates depends on inter-molecular interactions, and slower dynamics generally correlate with stronger inter-molecular interactions. Further, interactions among two or more P granule components can buffer against large change in dynamics / aggregation within the P granule phase. These insights may lay the groundwork for addressing how more “natural” modifications (e.g., post-translational modifications, high local concentration of “sticky” molecules) may influence dynamics within biomolecular condensates in vivo.

Based on current knowledge of P granule composition, chaperone proteins (e.g. heat-shock family proteins) do not show abundant concentration within P granules. However, it is unclear if chaperone proteins are completely excluded from the P granule phase. Therefore, we speculate that weak interactions among two or more non-chaperone proteins contribute significantly to “dynamics buffering” within the P granule phase in vivo.

In the discussion section of the manuscript, we had speculated that “dynamics buffering” may potentially explain observations reported in the nucleolus: “Similarly, interactions among components could be a potential mechanism of storage of misfolding-prone proteins in non-aggregated state within the liquid-like nucleolus under stress in vivo (Frottin et al, 2019).”

Our finding is also relevant in the context of synthetic biology with applications that require steady diffusion rate of macromolecules during biochemical reactions within biomolecular condensates.

• Recombinant PGL-3 experiments added PGL-1, GLH-1 and mRNA simultaneously and measured fluidity. It will be interesting to know which components contribute to fluidity and whether fluidity enhancement of each component is dependent on one another. Addition experiments with each component should be included and/or at least discussed in the main text. *

Our data with S1-mEGFP or PGL-3-mEGFP (pre-heated at 50°C) proteins microinjected into C. elegans gonads, and the transgenic strain expressing PGL-3(D425-452)-mEGFP from the pgl-3 locus showed that the P granule phase can support fast dynamics of these mutant PGL-3 constructs. Since P granules have a complex composition, one possibility is that fast dynamics of these constructs is supported by interactions involving many P granule components. We found that using only a limited set of P granule components (PGL-1, GLH-1 and mRNA) can buffer dynamics of S1 in condensates in vitro.

In absence of a systematic analysis investigating the individual role of approx. 70 P granule proteins in buffering S1 dynamics in condensates in vitro, we have claimed in the text that dynamics-buffering of S1 in condensates is supported by interactions among two or more components. However, we do appreciate the reviewer’s comment and feel it would be interesting to investigate the contribution of individual P granule components towards fluidity in future studies. We have discussed this in the ‘Discussion’ section of the manuscript.

• The biological relevance of PGL-1, GLH-1, and mRNA were not discussed in the main text. How these factors contribute to P granule assembly and function should be mentioned in the Introduction or Results. *

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

*MINOR: 1. Line 20, "most non-membrane-bound compartments...have complex composition": Are there examples of condensates that do not have complex composition? *

Not all non-membrane-bound compartments may have been characterized. To accommodate this possibility, we refrained from making a more general statement, but stated “most non-membrane-bound compartments…”.

• Lines 40-43, RNA interactions driving LLPS: Please include citations from the Parker Lab (e.g. Van Treeck and Parker, Cell. 2018 doi: 10.1016/j.cell.2018.07.023) *

We added the reference suggested by the reviewer.

• *

• Line 60, condensates contain hundreds of different proteins and RNA: Please cite at least a few examples of condensates with their components identified. *

We added some references following suggestion by the reviewer.

• Lines 82-84, PGL-3 drives assembly: Please cite Kawasaki, et al. Genetics 2004 for the discovery of PGL-3. *

We added the reference suggested by the reviewer.

• Lines 88-89, PGL-3 N-terminal fragment predominantly alpha-helical: The PGL domain structures should be cited here as supporting evidence that these regions are composed primarily of alpha helices (Aoki, et al 2016, 2021) *

• *

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

• Lines 158-159, driving forces for phase separation: This statement should be removed or expanded. The authors point regarding the protein concentrations is not clear here but clarified in the Discussion (Lines 691-693). Recommend removing due to its speculative nature. *

We retained the speculative comment in the results section. We feel that this prepares the readers for the discussion later in the manuscript.

• Lines 210: Add commas before and after "PGL-1 and GLH-1"*

We addressed the reviewer’s suggestion.

• Lines 218-219: add "and" instead of comma between PGL-1 and GLH-1 *

We addressed the reviewer’s suggestion.

• Lines 238-239, alpha-helices: The PGL CDD structure should also be referenced here (Aoki, et al 2016). *

To address this concern, we have added a paragraph in the Introduction section of the revised manuscript.

• Lines 680-682, MEG proteins: Please cite accordingly. *

We added the reference suggested by the reviewer.

• Lines 694-695, heterotypic interactions: Please cite Saha, et al. 2016. *

We added the reference suggested by the reviewer.

• Figure 1: Add space between 1 and mM DTT *

We addressed the reviewer’s suggestion.

• Figure 2b: Please provide statistics between condensate numbers. *

We provide statistics between condensate numbers in Fig. 2b.

• Figure 4A: The region of the germline imaged and analyzed should be mentioned in the caption or the main text. *

We revised the Figure legend of Fig. 4a to address this issue.

• Figure 4B,C: Please include statistics between the FRAP curves. *

We have included statistics comparing FRAP curves in Supplementary Fig. 4a-c.

• Figure 4D: It will be helpful to compare this curve to Figure S4A in the same graph. Please also include graph statistics. *

We have revised Fig. 4 to address the reviewer’s suggestion.

• Figure 5: The data points are difficult to resolve. Recommend use of color.*

We considered the suggestion, but felt it works better in the original form.

• Figure 6: This is a very general model that does not highlight the extensive experimental work performed by the authors. Recommend incorporating PGL-3, mutants and P granule factors into this model. *

We thank the reviewer for appreciating our extensive work. However, we retained the original Fig. 6 for the sake of simplicity.

• Methods, Line 939, C. elegans section: What worms were used? TH623? Please describe the genotype. *

We have included a table listing the strains used in the study and their genotype. * CROSS-CONSULTATION COMMENTS While my review was arguably the more favorable of the three, I agree with the other reviewers' comments and evaluation, particularly with Reviewer #1. As written in my review, my primary concern was the biological relevance of the work.*

Reviewer #3 (Significance (Required)):

Overall, the in vitro work presented investigating the biophysical properties of this minimal P granule system was thorough and well-analyzed, and the manuscript was clearly written. Additional citations and statistics will improve the manuscript and the strength of the conclusions, respectively. The biological relevance of this study to P granule form and function in vivo, and to condensates in vivo, is debatable. This work will interest those who study condensate biology, the biophysics of protein-protein and protein-RNA interactions, and RNA biochemists more generally.

A major impact of our work is elucidation of a novel “dynamics buffering” property within biomolecular condensates in vitro. Our in vivo data is consistent with this finding.

We have chosen two orthogonal ways of perturbing the PGL-3 protein (i.e. mutations and temperature-dependent unfolding) to assay the effect on diffusion rate against different levels of perturbation (e.g. 30% loss of a-helicity in heat-denatured PGL-3-mEGFP vs. 15% loss of a-helicity in the S1 mutant, compared to wild-type PGL-3). Studying the phase separation behavior of these “artificially-generated” constructs provided the understanding that dynamics of PGL-3 in condensates depends on inter-molecular interactions, and slower dynamics generally correlate with stronger inter-molecular interactions. Further, interactions among two or more P granule components can buffer against large change in dynamics / aggregation within the P granule phase. These insights may lay the groundwork for addressing how more “natural” modifications (e.g., post-translational modifications, high local concentration of “sticky” molecules) may influence dynamics within biomolecular condensates in vivo.

• *

Based on current knowledge of P granule composition, chaperone proteins (e.g. heat-shock family proteins) do not show abundant concentration within P granules. However, it is unclear if chaperone proteins are completely excluded from the P granule phase. Therefore, we speculate that weak interactions among two or more non-chaperone proteins contribute significantly to “dynamics buffering” within the P granule phase in vivo.

In the discussion section of the manuscript, we had speculated that “dynamics buffering” may potentially explain observations reported in the nucleolus: “Similarly, interactions among components could be a potential mechanism of storage of misfolding-prone proteins in non-aggregated state within the liquid-like nucleolus under stress in vivo (Frottin et al, 2019).”

Our finding is also relevant in the context of synthetic biology with applications that require steady diffusion rate of macromolecules during biochemical reactions within biomolecular condensates.

*I have expertise in P granules, protein/RNA biochemistry, condensate assembly, and C. elegans. *

References

Aoki ST, Kershner AM, Bingman CA, Wickens M & Kimble J (2016) PGL germ granule assembly protein is a base-specific, single-stranded RNase. Proceedings of the National Academy of Sciences of the United States of America

Aoki ST, Lynch TR, Crittenden SL, Bingman CA, Wickens M & Kimble J (2021) C. elegans germ granules require both assembly and localized regulators for mRNA repression. Nat Commun 12: 996

Cipriani PG, Bay O, Zinno J, Gutwein M, Gan HH, Mayya VK, Chung G, Chen J-X, Fahs H, Guan Y, et al (2021) Novel LOTUS-domain proteins are organizational hubs that recruit C. elegans Vasa to germ granules. Elife 10: e60833

Frottin F, Schueder F, Tiwary S, Gupta R, Körner R, Schlichthaerle T, Cox J, Jungmann R, Hartl FU & Hipp MS (2019) The nucleolus functions as a phase-separated protein quality control compartment. Science 365: 342–347

Kawasaki I, Amiri A, Fan Y, Meyer N, Dunkelbarger S, Motohashi T, Karashima T, Bossinger O & Strome S (2004) The PGL family proteins associate with germ granules and function redundantly in Caenorhabditis elegans germline development. Genetics 167: 645–661

Kawasaki I, Shim YH, Kirchner J, Kaminker J, Wood WB & Strome S (1998) PGL-1, a predicted RNA-binding component of germ granules, is essential for fertility in C. elegans. Cell 94: 635–645

Phillips CM & Updike DL (2022) Germ granules and gene regulation in the Caenorhabditis elegans germline. Genetics 220: iyab195

Price IF, Hertz HL, Pastore B, Wagner J & Tang W (2021) Proximity labeling identifies LOTUS domain proteins that promote the formation of perinuclear germ granules in C. elegans. Elife 10: e72276

Saha S, Weber CA, Nousch M, Adame-Arana O, Hoege C, Hein MY, Osborne Nishimura E, Mahamid J, Jahnel M, Jawerth L, et al (2016) Polar Positioning of Phase-Separated Liquid Compartments in Cells Regulated by an mRNA Competition Mechanism. Cell 166: 1572-1584.e16

Spike C, Meyer N, Racen E, Orsborn A, Kirchner J, Kuznicki K, Yee C, Bennett K & Strome S (2008a) Genetic analysis of the Caenorhabditis elegans GLH family of P-granule proteins. Genetics 178: 1973–1987

Spike CA, Bader J, Reinke V & Strome S (2008b) DEPS-1 promotes P-granule assembly and RNA interference in C. elegans germ cells. Development (Cambridge, England) 135: 983–993

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Referee #3

Evidence, reproducibility and clarity

Summary:

P granules are liquid condensates found in the developing germlines and embryos of C. elegans. Prior work by the authors and others have established P granules as a tractable model to investigate the basic biophysical properties of liquid condensates. Much of the prior published work focused on specific P granule scaffold proteins, PGL-1 and PGL-3. How attributes of these PGL proteins and the effect of other P granule components affect condensate properties is not fully understood. Here, Jelenic, et al. probe the biophysical properties of PGL-3. Using recombinant protein, they show that an N-terminal, alpha-helical region of PGL-3 is sufficient for liquid condensate formation and that N-terminal assembly is required for this formation. Creation of a scrambled alpha-helical region in PGL-3 and heat treatment affects PGL-3 fluidity. This fluidity can be "rescued" in vivo and in vitro with the inclusion of other P granule factors, including wildtype PGL-3, PGL-1, GLH-1 and mRNA. The authors note an inverse correlation between fluidity and mutant PGL-3 fluorescent intensity. They propose a model that heterotypic compositions of condensates can buffer their fluidity against components with stronger multivalent interactions.

MAJOR:

1. PGL-3 is a fantastic model to study the biophysical properties of a liquid condensate. But as the authors address in their discussion, the S1 mutant will likely affect the central domain folding, at its minimum causing exposure of a hydrophobic surface not typically exposed in biology. These helices are found at the terminal portion of the domain determined in the crystal structure and as depicted in the authors' Figure 1A. While the cause of S1's enhanced molecular interactions does not affect the in vitro work presented in this manuscript, it does affect how the conclusions connect to the biological nature of P granules and liquid condensates more generally.
2. Recombinant PGL-3 experiments added PGL-1, GLH-1 and mRNA simultaneously and measured fluidity. It will be interesting to know which components contribute to fluidity and whether fluidity enhancement of each component is dependent on one another. Addition experiments with each component should be included and/or at least discussed in the main text.
3. The biological relevance of PGL-1, GLH-1, and mRNA were not discussed in the main text. How these factors contribute to P granule assembly and function should be mentioned in the Introduction or Results.

MINOR:

1. Line 20, "most non-membrane-bound compartments...have complex composition": Are there examples of condensates that do not have complex composition?
2. Lines 40-43, RNA interactions driving LLPS: Please include citations from the Parker Lab (e.g. Van Treeck and Parker, Cell. 2018 doi: 10.1016/j.cell.2018.07.023)
3. Line 60, condensates contain hundreds of different proteins and RNA: Please cite at least a few examples of condensates with their components identified.
4. Lines 82-84, PGL-3 drives assembly: Please cite Kawasaki, et al. Genetics 2004 for the discovery of PGL-3.
5. Lines 88-89, PGL-3 N-terminal fragment predominantly alpha-helical: The PGL domain structures should be cited here as supporting evidence that these regions are composed primarily of alpha helices (Aoki, et al 2016, 2021)
6. Lines 158-159, driving forces for phase separation: This statement should be removed or expanded. The authors point regarding the protein concentrations is not clear here but clarified in the Discussion (Lines 691-693). Recommend removing due to its speculative nature.
7. Lines 210: Add commas before and after "PGL-1 and GLH-1"
8. Lines 218-219: add "and" instead of comma between PGL-1 and GLH-1
9. Lines 238-239, alpha-helices: The PGL CDD structure should also be referenced here (Aoki, et al 2016).
10. Lines 680-682, MEG proteins: Please cite accordingly.
11. Lines 694-695, heterotypic interactions: Please cite Saha, et al. 2016.
12. Figure 1: Add space between 1 and mM DTT
13. Figure 2b: Please provide statistics between condensate numbers.
14. Figure 4A: The region of the germline imaged and analyzed should be mentioned in the caption or the main text.
15. Figure 4B,C: Please include statistics between the FRAP curves.
16. Figure 4D: It will be helpful to compare this curve to Figure S4A in the same graph. Please also include graph statistics.
17. Figure 5: The data points are difficult to resolve. Recommend use of color.
18. Figure 6: This is a very general model that does not highlight the extensive experimental work performed by the authors. Recommend incorporating PGL-3, mutants and P granule factors into this model.
19. Methods, Line 939, C. elegans section: What worms were used? TH623? Please describe the genotype.

CROSS-CONSULTATION COMMENTS

While my review was arguably the more favorable of the three, I agree with the other reviewers' comments and evaluation, particularly with Reviewer #1. As written in my review, my primary concern was the biological relevance of the work.

Significance

Overall, the in vitro work presented investigating the biophysical properties of this minimal P granule system was thorough and well-analyzed, and the manuscript was clearly written. Additional citations and statistics will improve the manuscript and the strength of the conclusions, respectively. The biological relevance of this study to P granule form and function in vivo, and to condensates in vivo, is debatable. This work will interest those who study condensate biology, the biophysics of protein-protein and protein-RNA interactions, and RNA biochemists more generally.

I have expertise in P granules, protein/RNA biochemistry, condensate assembly, and C. elegans.

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Referee #2

Evidence, reproducibility and clarity

Jelenic et al. describe the effect of partner proteins on the FRAP dynamics of recombinant PGL-3 protein and variants in in vitro condensates and C elegans p-granules. The study shows that the N terminal a-helical dimerization domains is required for condensate formation and modulate of it alters aggregation and the FRAP dynamics of its condensates. Interestingly, a construct including the entire IDR region (370-693) by itself does not phase separate on its own at these conditions. The K126E K129E mutant (known previously to disrupt dimerization) and the deletion mutant abrogate llps. A mutant construct that shuffles the sequence in the region 423-453 called S1 here reduces the helicity and the condensate FRAP dynamics but recovered in the presence of a few P granule components. Also, the reduced dynamics of partially unfolded PGL-3 condensates are also rescued by the p-granule components to a certain degree of the unfolded PGL3 concentrations. This threshold concentration for recovering the condensate dynamics is further reduced in the helix reducing S1 mutant, which is also dependent on the number and the nature of P granule components.

• Overall, the study aims to probe how "composition can buffer protein dynamics within liquid-like condensates" - yet several underlying aspects of the study do not fully support that conclusion. The introduction does not sufficiently introduce the known structural information of the two dimerization domains in C elegans PGL proteins for which structures are known. The region is discussed as "alpha helical" but really there are two evolutionarily conserved independently folding dimerization domains (referring to the mutants as "reduced alpha helicity" is not helpful - these are mutations that destabilize a folded domain). Additionally, the abstract and introduction ignore the aspects of aggregation (touched on in discussion) - this is likely what the disruption to the helical region in residue 450 region is doing (the helix is not on the dimer interface based on homology / sequence identity to the crystal structure of PGL-1 central dimerization domain. Finally, the "dynamics buffering" is not really clearly established and could also be explained as small concentrations of aggregated proteins act like clients while increasing the concentration results in aggregation and "cross linking" in the entire droplet - and this concentration is never achieved in the in worm experiments so it is not clear. In other words, the change in FRAP dynamics not observed in worms is perhaps not surprising if small amount of recombinant proteins are incorporated into the granules. It is also not clear what the mechanism of the changes is - is the protein driven to fold more properly (despite S1 disruption of its conserved sequence) inside the condensate? Does it still self interact and act as a dimerization domain? Does this change disrupt interactions? What is the real mechanism by which PGL-3 phase separates if not via the disordered domains?

• Throughout the manuscript, the term "dynamics" is used to indicate FRAP, but it would be better to define what is meant (diffusion of PGL-3 in condensates) instead of using dynamics a term that could mean many things. Secondly, FRAP cannot directly measure liquidity etc (see recent critiques by McSwiggen elife 2019, etc) so it is better to be cautious in the claims. Finally, discussing "dyanmics buffering" adds more terminology where it is not needed - perhaps say "changes to diffusion of PGL-3 in condensates".

• The "N-terminus" is not 65% of the protein. One could define this as the N-terminal domain, but again there are two clear folded domains in the first 65% of the protein and this needs to be described better.

• The description of "stickers" and the references to tau and hnRNPA1 are confusing as this is a predominantly ordered domain while those are IDRs.

• The suggestion in the discussion that "P granule components support dynamics by participating in intermolecular interactions wth PGL-3-mEGFP molecules" is not well supported because no interaction assays are performed and no mutaitons are made that disrupt these interactions to test this.

More detailed analysis of some of the claims:

Claim 1:

An a-helical region mediates the phase separation of PGL-3, and the C-terminal disordered region by itself does not phase separate. The N-terminal dimerization is essential for LLPS. The C-terminal IDR interactions with mRNA facilitate the LLPS.

Comments:

The authors show sufficient experimental data using microscopy and FRAP on truncated constructs with the N-terminal and C-terminal regions - but see above regarding how these are described - a proper domain structure with the folded domains shown and the RGG motifs highlighted should be added and integrated throughout the discussion. They show that the N-terminus is necessary and adequate for LLPS, and the C-terminus by itself does not phase separate. But, how does the N-terminal domains phase separate? This is not explained - what are the interactions? Are the tags removed to ensure that phase separation is not caused by tags or remaining linker regions? Is the protein purified to be without nucleic acid contamination or other purity metrics? Also, a di-mutant (K126E K129E) that is known, and also authors use SEC-MALS to show their N-terminal construct is consistent with the published results. Disrupting the n-terminal dimerization prevents phase separation, suggesting the importance of these residues in the N-terminus for self-assembly and LLPS. The Microscopy data backs the claim that the mRNA-mediated LLPS is facilitated by binding with C-terminus. However, the m-RNA binding to IDR is not sufficient for LLPS. Yet, the authors do not explain how higher salt prevents phase separation - again the mechanism of phase separation is unclear. Is it multivalent interaction of the two dimerization domains? A basic model (that is tested) would be important.

Claim 2:

The N-terminal a-helical region modulates the dynamics within condensates. The IDR region has minimal effect on the fast dynamics of PGL-3.

Comments:

The authors show that the full-length PGL-3 condensates have modest influence of components by comparing the FRAP half times with or without the P granule components, including mRNA. However, have the authors tried this in the presence of mRNAs for the constructs lacking the IDRs as they have several RGG domains and bind with mRNA and are likely to change the dynamics. The authors report the importance of the N-terminal a-helical region by making a construct that lacks/disrupts a part of the helices lowers the thermal stability and significantly lowers the dynamics of the condensates. Also unfolding of helices is shown to reduce the dynamics. One primary concern is whether these "rescued" protein dynamics imply protein functionality. Are these semi denatured proteins refolded in the presence of P-granule components? Finally, it is not clear why the authors chose to disrupt folding of the central dimerization domain?

Saying that "reduced alpha-helicity of PGL-3 correlates with slower dynamics in condensates" may be factual in these assays but "correlation" should be expanded upon to include mechanism and to me it seems that the statement should read "aggregation of PGL-3 causes slower dynamics in condensates" (both the partially destabilized mutant and the fully unfolded WT show similar effects perhaps to different degrees).

CROSS-CONSULTATION COMMENTS

I agree with the other reviewer's comments and critiques, I have concerns about the biological relevance and also the biophysical mechanisms. Reflecting on the other reviewers' comments, the papers could provide more depth in one or both of these areas to come to firm conclusions that are either revealing about PGL biology or elucidate a (possible) general biophysical mechanism.

Significance

Hence, although the authors shows how inclusion of other components can alter the one protein component phase separation, this is done with entirely artificial means of destabilizing the fold of one of the domains which likely leads to aggregation. So the true impact of the work is hard to understand because the mutations impact on the basic biophysical properties of the domain (stability, interaction) are not completely characterized and the reason for disrupting this folding is not clear.

My field of expertise is protein phase separation and protein structure.

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Referee #1

Evidence, reproducibility and clarity

• A significant criticism of the paper is an assumption that readers will be familiar with all of the findings in the author's previous 2016 paper and the PGL-1 papers by Aoki et al. Minimal context is given for each approach. Some conclusions are not well supported and require further analysis, proper controls, and more extensive descriptions of the experiments performed. Most importantly, the central conclusion and title of the paper is that composition can buffer the dynamics of individual proteins within liquid-like condensates. In other words, in vitro condensation assays often do not recapitulate LLPS behavior in vivo. That said, the findings in this study would be significantly strengthened and complemented by observing endogenously tagged PGL-3 and PGL-3 mutants in living worms, considering the efficiency of using CRISPR in C. elegans to insert tags and make precise mutations.

• To improve readability, the introduction to P granules should be expanded, and include the reasons for looking at the nematode-specific PGL-3 protein among all the other known P granule proteins. A recap of previous findings on PGL-3 phase separation, in vivo and in vitro, is warranted, starting with the significant results of Saha et al 2016. Setting up the investigative questions in the context of recent work on PGL-1 (Aoki, et al) is also necessary.

• The physiological concentration of PGL-3 should be more transparent, including why some experiments in this study are done at physiological concentrations while others are not. Describing why salt concentrations, crowding agents, and protein abundance are similar or different for each experiment is necessary and relevant. For example, after showing in Figure 1 that PGL-3 protein phase separates, the paragraph starting on line 161 says that it was previously shown that PGL-3 doesn't phase separate at physiological concentrations without RNA. One has to go back to Figure 1 to realize it was done differently than Figure 2 and Saha 2016. Statements in the same paragraph like "in contrast to full-length PGL-3, mRNA does not support phase separation..." should be qualified by stating the concentration observed, with or without salts or other crowding agents. Similarly, line 230 "suggests that interactions involving the disordered C-terminal region of PGL-3 are not essential for the fast dynamics" and should be qualified with "at non-physiological concentrations and with XX crowding agents or salt concentration." It would be more consistent if physiological concentrations were consistent from figure to figure, as extra variables weaken some of the stated conclusions.

• The 2010 review reference stating that there are 40 P granule enriched proteins is outdated. More recent reviews put the number much higher. This is relevant because the approach to put PGL-3 in a more physiological environment by including just PGL-1, GLH-1 and mRNA with the condensate assays, out of ~100 P granule enriched proteins, may not be sufficient to conclude "that the influence of complex composition on dynamics is modest" (line 223), or imply that the multicomponent nature of the P granule is reconstituted by adding these components (line 355).

• Figure 1C needs to include PGL-3(370-693) in the analysis. Figure 1E is also incomplete without a comparison of FRAP recovery between PGL-3(1-452) and full PGL-3 as the control.

• Figure 4C is missing an essential control where PGL-3 and S1 FRAP is performed without PGL-1, GLH-1, and mRNA. It would also help show sup Fig4A in the main figure to show concentration dependence.

• Consider adding subtitles to supplementary figures.

• M&M should include an explanation for statistical analysis

CROSS-CONSULTATION COMMENTS

I am also in agreement with the comments and critiques of reviewers 2 and 3.

Significance

The paper by Saha and colleagues investigate the in vitro liquid-liquid phase separation propensity of a P granule protein PGL-3 and its structural domains. The findings largely replicate and support the phase-separation properties of a paralogous protein called PGL-1, as recently described by Aoki et al. 2021. Furthermore, they show that the dynamics demonstrated by recombinant PGL-3 may be maintained or buffered by the complex composition of P granules.

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Reply to the reviewers

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

The authors have assembled an enormous amount of statistical data on the genomes and phylogeny of Arctic algae, including the genomes of four new species that they sequenced for this study. Their main finding is that horizontal gene transfer has led to convergent evolution in distantly related microalgae.

**Major comments**

Reviewer #1__: The purpose of the study is not clearly stated in the abstract or the introduction. The authors say (line 93) "Defining the genetic adaptations underpinning these small algal species is crucial as a baseline to understand their response to anthropogenic global change (Notz & Stroeve,2016)." Is this their goal? Or are they just quoting another study? The authors state (line 103) "We extend by sequencing the genomes of four distantly related microalgae...". This is not really a question or a hypothesis. I am sure the authors can provide a more compelling reason to embark on such a labor-intensive study.__

Reply: We agree that the aim was lost in the details and the Introduction is now focused towards the original goal of the study, which was to investigate convergent evolution in a biogeographically isolated ocean. Additional references on the formation and history of the Arctic Basin have been added to the Introduction to provide context. “An ocean has been present at the pole since the beginning of the Cretaceous. Shaped by tectonic processes (Nikishin et al., 2021) the Arctic Ocean has been a relatively closed basin since the Masstrichtian at the end of the late Cretaceous epoch (ca. 70 million years before present), with episodic sea-ice cover since that time (Niezgodzki et al., 2019). This long history suggests limited gene flow from the global ocean over vast time scales and Arctic marine species including microalgae could well have unique adaptations to cold arctic conditions.” Line 78-83.

And following this we provide a clear hypothesis “The potential for lineages of ancient Arctic origin and the episodic input of outside species led us to our hypothesis that Arctic microalgae convergently evolved traits or adaptations aiding survival in an ice-influenced ocean. Line 112-117.

We also discuss both the adaptive and distinct physical environment of the Arctic, and its topographical separation from other ocean regions as dispersal limitation would enhance the Arctic-specific genomic signatures. We now cite the recent paper by Sommeria-Kline et al. (2020), which puts eukaryotic plankton biogeography into a global context (Line 72)

Reveiwer #1__: The most prominent shared trait that the authors found are genes for ice-binding proteins. However, in view of their importance, little information is given about their different types and possible functions.__

Reply: We appreciate the comment and have added information on relevant ice binding proteins found in the Arctic Algae. In addition, we discuss how the functional and secretory diversity of IBP would enhance the survivability of pelagic taxa. Lines 534 to 564.

Although ice binding proteins from multicellular animals and plants are outside the scope of this study, there is a recent review; Bar Doley, Braslavsky and Davies 2016 Annual review of Biochemisty 85: 515-542.

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Reviewer #1__: The HGT of ice-binding proteins is a major focus of this study, but little is said about what previous studies have said about this. What are the previous studies, what are their findings and how do the present findings contribute to this?__

Reply: We agree that this aspect should have been more visible. We incorporated new data to characterize IBPs drawn from MMETSP transcriptomes, and environmental Tara Ocean metagenomes, as well as our Arctic strains. We note that as we take a PFAM-based approach, the IBPs treated are DUF3494/PF11999 domain, which are type 1 IBPs / algal IBPs (Raymond and Remia 2019). As an example of novelty, we identify the position of IBPs from dinoflagellates, within a larger Arctic Clade that included CCMP2293, CCMP2436 and CCMP2097 and Arctic TARA IBP, rendering this a pan-algal IBD clade.

In addition, we were able to resolve the position of anomalous F. cylindrus IBP that fell between two Arctic associated clades (A and B, in our Fig 4). This finding is consistent with F. cylindrus originating in the Arctic as previously suggested and subsequently invading the Southern Ocean.

The recurrent acquisition of multiple diverse IBP isoforms in individual species through HGT events has not been previously reported, and the extent of isoforms in the Arctic was surprising. See for example multiple different IBP forms with separate origins in Pavlovales CCMP2436 (Fig 4). The previous studies are referred to in the context of the phylogeny of the IBD within the results section: Lines 322- 413, and Lines 534-585.

Reviewer #1: Figure 5 on HGT of ice-binding proteins is difficult to follow. It would be clearer if each panel could be described separately, clearly stating its main finding. I doubt that a reader could look at this figure and explain to a colleague what it shows.

Reply: We have revised rearranged the figure (now Fig 4) with Arctic A, B, C and D clearly indicated as well as the two Antarctic dominated clades. The upper schematic includes the deepest phylogeny of algal IBDs to date, incorporating all of UniRef, MMETSP and TARA Oceans. The fasta files underlying the tree and the nexus file used are provided the S1 Data Folder, which is an excel folder with information on the analysis of the data. The callout and order of the clades has been revised to facilitate interpretation of the phylogenies more clearly. The entire section has been completely rewritten.

Reviewer #1: This is also a problem with many of the other figures. For each figure, what is the question being asked and what is its take-home message?

Reply: We agree that the message was lost and have now focused on our original question in our accepted proposal to JGI. “Is there a convergence among arctic microalgae at the genomic level?”. We found some genome properties were common among the Arctic isolates (more unknown PFAMS and several expanded PFAMs). The importance of ice binding proteins in Arctic Isolates and the widespread inter-algal HGT of this important protein among the Arctic strains. The IBP biogeography and phylogeny strongly indicate that the Arctic microalga have acquired IBP locally and that the Antarctic strains have acquired additional isoforms independently from Antarctic bacteria and fungi (Lines 565-585).

Reviewer ____#1____: ____The paper has more data than a reader can absorb. It could be strengthened by reducing the number of figures, simplifying them if possible, and more clearly stating the value of the remaining figures.

Reply. As suggested, we have refocused the paper, removing more speculative statistics based analysis and associated figures. The main conclusions are supported by the 5 main figures. We are now present 5 main figures and 11 supplementary figures (previously 23 downloadable supplementary figures and 40 on-line only figures supporting the support figures). We agree with the reviewer, and we feel the revised version is a more transparent synthesis. Briefly the Figures illustrate the following points. Fig. 1. The multigene tree of available algal genomes and transcriptomes provides a clear framework for judging the divergence of subsequent individual gene and PFAMs phylogenies. Fig. 2 (originally Fig. 3). Indicates the convergence of PFAM domains in the Arctic strains, in contrast to strains from elsewhere. Fig. 3 (originally Figure 4) shows Arctic specific expansions and contraction of PFAM domains, again demonstrating convergent evolution in the Arctic. The figure identifies specific PFAMs that contribute to the within-Arctic convergence. This figure is based on statistical methods independent of Fig 2. Figure 4 is the most extensive IBP phylogeny to date and has been discussed above. Figure 5, which was supplementary in our non-peer reviewed version, shows the biogeographic distribution of IBP, and can be compared to the distributions of the 18S rRNA genes from the four Arctic algae provided as supplementary (S6 Fig.)

**Minor comments**Reviewer #1

1. The figure citations are confusing. E.g., what does "Fig.1- Figure supplement 1" refer to? Does this refer to 1 or 2 figures? Apparently, it refers only to Fig. S1, so many readers will be confused when they look at Fig. 1.

Reply: We apologize for the confusing format; the manuscript had been formatted for the online journal eLife. Our revision follows the more traditional style of PLoS Biology and other Review Commons journals.

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Multiple citations should be in order of publication date, not alphabetical order.

Reply ; We agree that date of publications is quite standard and recognizes priority of publication. Several on line journals no longer follow this rule and citation order will follow the specific style used by our accepting journal.

Reviewer #1 (Significance (Required)): It is well known that useful genes tend to be shared among microorganisms. The present study strengthens previous studies in showing that gene transfer is an important process in polar regions.

Reply: We thank the reviewer for recognizing the importance of our study.

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

This manuscript is the result of a large international collaborative effort, including the US Department of Energy Joint Genome Institute. Its focus is comparative genomics of eukaryotic Arctic algae. The primary data described in the ms are four new genome and transcriptome sequences from diverse Arctic algae, represented by a cryptomonad, a haptophyte, a chrysophyte, and a pelagophyte.

The authors compare these new data to previously published genomic/transcriptomic data from eukaryotic algae with the goal of understanding genome evolution in the Artic. The results of the paper are a series large-scale comparative genomic bioinformatics analyses, including the associated statistical analyses. The key findings center on statistically significant features of Arctic genomes, features that stand out as compared to the genomes of algae that are not primarily found in the Arctic. Together, these findings allow the authors to make various hypotheses and suggestions about genetic adaptations to polar environments.

By far the most significant finding is that the genomes of Arctic algae are enriched in genes encoding proteins with an ice-binding domain, paralleling findings from Antarctic algae. These genes appear to have spread among Arctic algal genomes via horizontal gene transfer, which raises a series of interesting questions. In my opinion, the major conclusions of this paper are supported by the data. Listed below are a few comments that may improve the ms:

Reviewer #2.

1) In today's post-genomics era, everyone seems to be sequencing nuclear genomes. Often what distinguishes high-impact and low-impact genome papers is the number of genomes presented and the quality of the genome assembly. I may have missed it, but reading the main text, the figures/tables, and the supplementary data I was not able to get a sense of the quality of the four genome assemblies from which the main findings are based. I was eventually able to find this information from PhycoCosm (note: some of the links to this site are not working in the ms). My quick scan of the PhycoCosm summary info for the four genomes indicates that the assemblies are highly fragmented, likely because they are based on short-read Illumina sequencing rather than a combination of short and long reads. I think it is important to briefly discuss (and or present) the quality of the assemblies in the ms and to highlight the potential limitations/drawbacks of employing highly fragmented assemblies when carrying out large-scale comparative genomics.

Reply: We agree and the data concerning the genome quality assemblies has been moved to the main text Table 1. The comparison with other paired related strains is provided in an excel folder designated S2 Data Folder.

Reviewer #2.

2) Horizontal gene transfer is undeniably a major driving force in evolution, and one that has shaped genomic architecture across the Tree of Life. I believe the data presented here support a role for HGT in the genome of evolution of Arctic algae, particularly with respect to genes encoding proteins with an ice-binding domain. However, we can all think of numerous instances when authors of genome papers were too quick to point to HGT. Thus, I would urge more caution and balance when presenting the HGT data, including some discussion about factors that could incorrectly lead researchers to conclude a significant role for HGT, such as contamination, gene duplication, mis-assemblies, etc. I'm not suggesting that you change the main conclusions, but just tone down the language in places (e.g., "we reveal remarkable convergence in the coding content ... ").

Reply: We understand the reviewers concerns and now more clearly outline the pipeline we have used to identify HGTs. This included: filtering each genome to remove all possible contaminant sequences first, considering both contig co-presence of vertical- and horizontally-derived genes, and reciprocal and independent annotations of gene sequences in both genome sequences and MMETSP transcriptomes. Retained genes were subjected to simultaneous BLAST analysis and manually curated phylogenies using decontaminated reference datasets. The most parsimonious explanation for our final IBP domain microbial algal clusters (Fig 4) is HGT. On the side of caution, we removed the entire section that identified potential arctic HGT based primarily on a less targeted broad statistical analysis. The focus is now on 3 genes that have clearly identifiable utility in the Arctic, were found to be enriched in Arctic genomes via a separate analysis and had homologs in the Tara Ocean Polar circle data. In addition, we describe more clearly the role of expansion and enrichment of PFAMs and the high proportion genes without an identifiable PFAMs in the Arctic strains as evidence for Arctic convergence separate from potential HGT.

Reviewer #2.

3) The downside of studying protists (as compared to multicellular animals, for instance) is that most are not widely known by the scientific community and even fewer scientists can picture what they actually look like (e.g., Pavlovales sp. CCMP2436). A few more details about the four Arctic algae that make up the focus of this paper might be helpful for the casual reader. My sense is that if at the next departmental meeting I asked my colleagues what a pelagophyte was most would look at me with a blank stare. Moreover, am I right to assume that all four algae are psychrotolerant rather than psychrophilic (Supplement Fig. 1 makes me think otherwise). It might be good to point out the difference in the text.

Reply: High resolution images of each strain are available on the JGI home page for each alga, given the multiple figures we feel photos would not add information.

Reviewer #2

4) I don't think Supp. Table 1 (the Pan-algal dataset) got uploaded correctly during the manuscript submission stage. The first link I click on gives me Supp. Table 2.

Reply: We apologize for this, the format was incorrect for the file designation and there were lost links. We now more actually refer to these as Data Folders as they are excel folders containing multiple sheets, All supplementary links will be verified again on final submission.

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Reviewer #2 (Significance (Required)):

By far the most significant finding from this paper is that the genomes of Arctic algae are enriched in genes encoding proteins with an ice-binding domain, paralleling findings from Antarctic algae. These genes appear to have spread among Arctic algal genomes via horizontal gene transfer, which raises a series of interesting questions. This is not the first paper to present these types of ideas, but it is arguably the broadest analysis yet, at least with respect to eukaryotic algae. This work will be of great interest to polar scientists, phycologists, protistologists, and the genomics community. I am genome scientist studying protists, including algae.

Reply. We thank the reviewer for their insightful comments.

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

**Summary:**

This manuscript is focused on Arctic microalgae, an important yet understudied community in permanently cold ecosystems. By sequencing the genomes of four phylogenetically diverse and uncharacterized polar algae, the authors seek to elucidate genomic features and protein families that are similar in polar species (and differ from their relatives from temperate environments) This work used high-throughput genomic sequencing and computational analysis to demonstrate significant horizontal gene transfer (HGT) in several gene families, including ice-binding proteins. The authors suggest that this HGT is an effector of environmental adaptation to Arctic environments.

**Major comments and experiment suggestions:**

The authors conclude that HGT between arctic species is a driver of polar adaptation. The authors strongly support the claim that HGT is present more frequently in the polar algae examined here. Whether this is adaptive should be further explored though. For instance, ice-binding domains were one PFAM group found at significantly higher frequencies in the polar species - but are all of these species associated with ice? What would be the benefit of IBDs in an alga that is found in the open ocean. Similar with the other domains (Lns 333-335), its not clear whether these are truly adaptive features. ____This is more speculative.

Reply: We agree that detail was lacking and have considerably expanded our introduction on the character of the Arctic Ocean and have stated the goals and underlying hypothesis. Briefly, all surface water organisms that live in the Arctic encounter ice during the year as the ocean freezes in winter, and surface waters reman around negative 1.7 °C for much of the year. This information has been added to the introduction. We have also expanded the discussion on the multiple effects of different IBPs that would be ecologically beneficial for plankton as well as ice-algae and cite relevant experimental studies and reviews.

Reviewer #3) ____HGT was a major conclusion of this study, putting this in a wider perspective would strengthen the conclusion, especially in the context of HGT from prokaryotes. Are there insights on whether IBDs are present in Arctic prokaryotes?

Reply: This is a good question, and we now point out that there were 91 Arctic bacterial and archaeal IBP sequences in our comparative dataset. In contrast to the Antarctic clades, none were closely related to the Arctic strain IBPs (Fig 4). Line 336.

Reviewer #3) ____The data obtained from the genomic works supports the conclusions stronger that ones from transcriptomes, where what genes/domains are present would depend largely on the sampling conditions. This should be emphasized.

Reply: The main rational for using transcriptomes was that more of these are available and enabled us to detect convergences and HGT across a broader taxonomic range than would be possible with genome-only data, where we had access to a total of only 21 microalgal genomes. In general transcriptome studies are aimed at identifying responses under different conditions and rely on comparative expression data, usually 2-fold differences in up or down expression under different growth conditions, see for example Freyria et al. 2022 (Communications Biology). Unlike a transcriptome expression study, our data mining detected any (constitutive or regulated) expression in these unicellular haploid cells, we would have detected genes used under any condition that an algal happened to be growing. IBD was not detected in any of the temperate genomes, and only detected in transcriptomes of Arctic and Arctic-Boreal groups. However, we agree that there may be some limitation of transcriptomes only studies and mention this. Lines 522-528.

Reviewer #3) ____An experiment to determine whether the species are cold extremophiles (psychrophiles) would be useful here to strongly support the data in Figure 1. The authors state that their species can not survive >6C but this is based on experiments done on older studies. Considering the cultures have been maintained as a continuous culture for decades, confirming that they still have psychrophilic characteristic would be useful. This is a straightforward and low cost experiment that requires simply measuring growth rates at several temperatures to define the optimal and confirm that the cells are not viable above 6C.

Reply: These are interesting points, and the broad “background” statements in the original manuscript would require a separate study,and have been deleted. Temperature tolerance experiments are not so simple for cold adapted algae with slow growth rates. Such experiments require specialized incubators to maintain low temperatures. Temperature experiments have been carried out on the cultures in the context of other studies, see for example, Daugberg et al. 2018, J. Phycol. But this is not within the scope of the present study.

We now restrict our conclusions to the specific question of convergence among Arctic strains. We apologize for the misunderstanding on the history of the cultures. They have not been in “continuous culture” but are cryopreserved. We now simply indicate that they grow below 6 °C, which is sufficient to assume that they are likely cryophiles, our experience is that they do not grow well or at all at higher temperatures, our efforts have been to maintain the cultures that are otherwise easily lost. We now make no claims about optimality or limits. Here we simply examined genomes and available transcriptomes that were generated from algae growing at 4-6 °C.

Reviewer #3) ____**Minor comments:**

Defining the species used here as psychrophiles would put the study in context better. The authors relate their finding to Antarctic species (HGT, ice-binding domains, large genomes) all of which are confirmed psychrophiles.

Reply: The temperature definition of psychrophiles is surprisingly high (optimal growth below 15 °C) and this definition of psychrophiles is now given in the introduction. The point is really that there are few isolates from cold surface waters that have been well studied. We now add. “A handful of polar algal genomes have been extensively studied, with 4 of these from around Antarctica and classified as psychrophiles (not being able to grow above 15 °C (Feller & Gerday, 2003)”. Lines 103-107.

Reviewer #3) ____A short rationale on why these species at all would be useful - are they representative of their classes? Do they have psychrophilic characteristics that might make them useful models in the future? Are they widely used now?

Reply: We appreciate the point as the definition of utility in discovery-based science is an open dialog.

We agree that the study requires context and have added our rational for selecting the species for genome sequencing to the introduction. “To address questions on genetic adaptations to this ice-influenced environment, we sequenced 4 phylogenetically divergent microalgae, from 4 algal classes belonging to 3 algal phyla: Cryptophyceae (Cryptophyta), Pavlovophyceae (Haptophyta), Chrysophyceae and Pelagophyceae (both in the Ochrophyta) isolated from the ca. 77 °N, where surface ice flow persists through June (Mei et al., 2002). The four isolates were selected as representatives of different water and ice conditions and phylogeny from available strains collected in April and June 1998 during the North Water Polynya study”.

Reviewer #3) ____Starting algal cultures were maintained in a continuous culture since 1998 and under continuous light since at least 2015, have the authors confirmed that these algae retain their physiological features even after this long time? The accumulation of mutations is a possibility here.

Reply: We apologize for the misunderstanding of the timeline; the history of the cultures was not given in the manuscript and the inferred history is not quite correct. The 2015 date was the year of publication for the MMETSP data. Our continuous light statement is a record of our standard culture conditions. We now elaborate on the material used in the current study. The cultures were deposited in the Bigelow culture collection (now NCMA) in 2002 and cryopreserved once they had been verified and given a culture designation. We obtained fresh cultures in 2005 and these were used for the MMETSP project. We obtained fresh cultures again in 2011, specifically for the JGI genome project. These algae do not grow fast and most of the DNA was sent to JGI in 2012 for most of the isolates. This history is rather long and not relevant, since one would speculate that over the years the algae would tend to lose the ice associated functionality, e.g. they were not frozen in seawater every year for 4 to 6 months or subject to sudden freshwater exposure, when ice melts. We would encourage other researchers to order the cultures and run experiments. We note that many of the 40 or so algae isolated from the same campaign have been used by others for specific studies and at least 8 are in the MMETSP data set. The presence of 18S rRNA and phylogenetic position of the IBP sequences compared to Tara Arctic circle data confirms long-term Arctic presence of each species and the IBP domains in the Arctic without marked changes over the last 20 years.

Reviewer #3) ____Ln381 - The culture collection IDs for each sequenced species should be included here

Reply: we have added the culture IDs throughout.

Reviewer #3) ____Ln. 389 - Algal cells are harvested and used for nucleic acid extraction, the nucleic acids themselves are not harvested

Reply: we agree and corrected the wording

Reviewer #3 (Significance (Required)):

This study is well places in the current state of research on polar alga and represents a significant and very valuable addition to the current knowledge pool. Algae in general are lagging behind other groups of photosynthetic organisms in the number of sequenced and analyzed genomes, despite algae being one of the main primary producers globally. This is even more strongly felt in polar research, where only 4 species have been sequenced, most of which are restricted to Antarctica. There is a true gap in our knowledge when it comes to Arctic species, and this study fills this gap. As the authors correctly state, we need more knowledge on polar environments and the primary producers that support these important ecosystems in light of current climate change trends.

Reply: we appreciate the succinct summary of our study and thank the reviewer for insights and suggestions that have improved the manuscript.

Reviewer field of expertise: Polar algae, stress responses, plant and algal energetics, cell signalling

Reply: We appreciate the incites and perspective steming from the reviewer's expertise.

Relevant key references cited in the reply:

Daugbjerg N, Norlin A, Lovejoy C. Baffinella frigidus gen. et sp. nov. (Baffinellaceae fam. nov., Cryptophyceae) from Baffin Bay: Morphology, pigment profile, phylogeny, and growth rate response to three abiotic factors. Journal of Phycology. 2018;54(5):665-80

Feller, G. and Gerday, C. (2003) Psychrophilic enzymes: Hot topics in cold adaptation. Nat Rev Microbiol, 1, 200-208.

Freyria NJ, Kuo A, Chovatia M, Johnson J, Lipzen A, Barry KW, et al. Salinity tolerance mechanisms of an Arctic Pelagophyte using comparative transcriptomic and gene expression analysis. Communications Biology. 2022;5(1). doi: 10.1038/s42003-022-03461-2

Mei, Z. P., Legendre, L., Gratton, Y., Tremblay, J. E., Leblanc, B., Mundy, C. J., Klein, B., Gosselin, M., Larouche, P., Papakyriakou, T. N., Lovejoy, C. and Von Quillfeldt, C. H. (2002) Physical control of spring-summer phytoplankton dynamics in the North Water, April-July 1998. Deep-Sea Research Part Ii-Topical Studies in Oceanography, 49, 4959-4982.

Niezgodzki, I., Tyszka, J., Knorr, G. and Lohmann, G. (2019) Was the Arctic Ocean ice free during the latest Cretaceous? The role of CO2 and gateway configurations. Global and Planetary Change, 177, 201-212.

Nikishin, A. M., Petrov, E. I., Cloetingh, S., Freiman, S. I., Malyshev, N. A., Morozov, A. F., Posamentier, H. W., Verzhbitsky, V. E., Zhukov, N. N. and Startseva, K. (2021) Arctic Ocean Mega Project: Paper 3-Mesozoic to Cenozoic geological evolution. Earth-Science Reviews, 217.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript is focused on Arctic microalgae, an important yet understudied community in permanently cold ecosystems. By sequencing the genomes of four phylogenetically diverse and uncharacterized polar algae, the authors seek to elucidate genomic features and protein families that are similar in polar species (and differ from their relatives from temperate environments) This work used high-throughput genomic sequencing and computational analysis to demonstrate significant horizontal gene transfer (HGT) in several gene families, including ice-binding proteins. The authors suggest that this HGT is an effector of environmental adaptation to Arctic environments.

Major comments and experiment suggestions:

• The authors conclude that HGT between arctic species is a driver of polar adaptation. The authors strongly support the claim that HGT is present more frequently in the polar algae examined here. Whether this is adaptive should be further explored though. For instance, ice-binding domains were one PFAM group found at significantly higher frequencies in the polar species - but are all of these species associated with ice? What would be the benefit of IBDs in an alga that is found in the open ocean. Similar with the other domains (Lns 333-335), its not clear whether these are truly adaptive features. This is more speculative.
• HGT was a major conclusion of this study, putting this in a wider perspective would strengthen the conclusion, especially in the context of HGT from prokaryotes. Are there insights on whether IBDs are present in Arctic prokaryotes?
• The data obtained from the genomic works supports the conclusions stronger that ones from transcriptomes, where what genes/domains are present would depend largely on the sampling conditions. This should be emphasized.
• An experiment to determine whether the species are cold extremophiles (psychrophiles) would be useful here to strongly support the data in Figure 1. The authors state that their species can not survive >6C but this is based on experiments done on older studies. Considering the cultures have been maintained as a continuous culture for decades, confirming that they still have psychrophilic characteristic would be useful. This is a straightforward and low cost experiment that requires simply measuring growth rates at several temperatures to define the optimal and confirm that the cells are not viable above 6C.

Minor comments:

• Defining the species used here as psychrophiles would put the study in context better. The authors relate their finding to Antarctic species (HGT, ice-binding domains, large genomes) all of which are confirmed psychrophiles.
• A short rationale on why these species at all would be useful - are they representative of their classes? Do they have psychrophilic characteristics that might make them useful models in the future? Are they widely used now?
• Starting algal cultures were maintained in a continuous culture since 1998 and under continuous light since at least 2015, have the authors confirmed that these algae retain their physiological features even after this long time? The accumulation of mutations is a possibility here.
• Ln381 - The culture collection IDs for each sequenced species should be included here
• Ln. 389 - Algal cells are harvested and used for nucleic acid extraction, the nucleic acids themselves are not harvested

Significance

This study is well places in the current state of research on polar alga and represents a significant and very valuable addition to the current knowledge pool. Algae in general are lagging behind other groups of photosynthetic organisms in the number of sequenced and analyzed genomes, despite algae being one of the main primary producers globally. This is even more strongly felt in polar research, where only 4 species have been sequenced, most of which are restricted to Antarctica. There is a true gap in our knowledge when it comes to Arctic species, and this study fills this gap. As the authors correctly state, we need more knowledge on polar environments and the primary producers that support these important ecosystems in light of current climate change trends.

Review field of expertise: Polar algae, stress responses, plant and algal energetics, cell signalling

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Referee #2

Evidence, reproducibility and clarity

This manuscript is the result of a large international collaborative effort, including the US Department of Energy Joint Genome Institute. Its focus is comparative genomics of eukaryotic Arctic algae. The primary data described in the ms are four new genome and transcriptome sequences from diverse Arctic algae, represented by a cryptomonad, a haptophyte, a chrysophyte, and a pelagophyte.

The authors compare these new data to previously published genomic/transcriptomic data from eukaryotic algae with the goal of understanding genome evolution in the Artic. The results of the paper are a series large-scale comparative genomic bioinformatics analyses, including the associated statistical analyses. The key findings center on statistically significant features of Arctic genomes, features that stand out as compared to the genomes of algae that are not primarily found in the Arctic. Together, these findings allow the authors to make various hypotheses and suggestions about genetic adaptations to polar environments.

By far the most significant finding is that the genomes of Arctic algae are enriched in genes encoding proteins with an ice-binding domain, paralleling findings from Antarctic algae. These genes appear to have spread among Arctic algal genomes via horizontal gene transfer, which raises a series of interesting questions. In my opinion, the major conclusions of this paper are supported by the data. Listed below are a few comments that may improve the ms:

1) In today's post-genomics era, everyone seems to be sequencing nuclear genomes. Often what distinguishes high-impact and low-impact genome papers is the number of genomes presented and the quality of the genome assembly. I may have missed it, but reading the main text, the figures/tables, and the supplementary data I was not able to get a sense of the quality of the four genome assemblies from which the main findings are based. I was eventually able to find this information from PhycoCosm (note: some of the links to this site are not working in the ms). My quick scan of the PhycoCosm summary info for the four genomes indicates that the assemblies are highly fragmented, likely because they are based on short-read Illumina sequencing rather than a combination of short and long reads. I think it is important to briefly discuss (and or present) the quality of the assemblies in the ms and to highlight the potential limitations/drawbacks of employing highly fragmented assemblies when carrying out large-scale comparative genomics.

2) Horizontal gene transfer is undeniably a major driving force in evolution, and one that has shaped genomic architecture across the Tree of Life. I believe the data presented here support a role for HGT in the genome of evolution of Arctic algae, particularly with respect to genes encoding proteins with an ice-binding domain. However, we can all think of numerous instances when authors of genome papers were too quick to point to HGT. Thus, I would urge more caution and balance when presenting the HGT data, including some discussion about factors that could incorrectly lead researchers to conclude a significant role for HGT, such as contamination, gene duplication, mis-assemblies, etc. I'm not suggesting that you change the main conclusions, but just tone down the language in places (e.g., "we reveal remarkable convergence in the coding content ... ").

3) The downside of studying protists (as compared to multicellular animals, for instance) is that most are not widely known by the scientific community and even fewer scientists can picture what they actually look like (e.g., Pavlovales sp. CCMP2436). A few more details about the four Arctic algae that make up the focus of this paper might be helpful for the casual reader. My sense is that if at the next departmental meeting I asked my colleagues what a pelagophyte was most would look at me with a blank stare. Moreover, am I right to assume that all four algae are psychrotolerant rather than psychrophilic (Supplement Fig. 1 makes me think otherwise). It might be good to point out the difference in the text.

4) I don't think Supp. Table 1 (the Pan-algal dataset) got uploaded correctly during the manuscript submission stage. The first link I click on gives me Supp. Table 2.

Significance

By far the most significant finding from this paper is that the genomes of Arctic algae are enriched in genes encoding proteins with an ice-binding domain, paralleling findings from Antarctic algae. These genes appear to have spread among Arctic algal genomes via horizontal gene transfer, which raises a series of interesting questions. This is not the first paper to present these types of ideas, but it is arguably the broadest analysis yet, at least with respect to eukaryotic algae. This work will be of great interest to polar scientists, phycologists, protistologists, and the genomics community. I am genome scientist studying protists, including algae.

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Referee #1

Evidence, reproducibility and clarity

The authors have assembled an enormous amount of statistical data on the genomes and phylogeny of Arctic algae, including the genomes of four new species that they sequenced for this study. Their main finding is that horizontal gene transfer has led to convergent evolution in distantly related microalgae.

Major comments

1. The purpose of the study is not clearly stated in the abstract or the introduction. The authors say (line 93) "Defining the genetic adaptations underpinning these small algal species is crucial as a baseline to understand their response to anthropogenic global change (Notz & Stroeve,2016)." Is this their goal? Or are they just quoting another study? The authors state (line 103) "We extend <previous findings> by sequencing the genomes of four distantly related microalgae...". This is not really a question or a hypothesis. I am sure the authors can provide a more compelling reason to embark on such a labor-intensive study.
2. The most prominent shared trait that the authors found are genes for ice-binding proteins. However, in view of their importance, little information is given about their different types and possible functions.
3. The HGT of ice-binding proteins is a major focus of this study, but little is said about what previous studies have said about this. What are the previous studies, what are their findings and how do the present findings contribute to this?
4. Figure 5 on HGT of ice-binding proteins is difficult to follow. It would be clearer if each panel could be described separately, clearly stating its main finding. I doubt that a reader could look at this figure and explain to a colleague what it shows.
5. This is also a problem with many of the other figures. For each figure, what is the question being asked and what is its take-home message?
6. The paper has more data than a reader can absorb. It could be strengthened by reducing the number of figures, simplifying them if possible, and more clearly stating the value of the remaining figures.

Minor comments

1. The figure citations are confusing. E.g., what does "Fig.1- Figure supplement 1" refer to? Does this refer to 1 or 2 figures? Apparently, it refers only to Fig. S1, so many readers will be confused when they look at Fig. 1.
2. Multiple citations should be in order of publication date, not alphabetical order.

Significance

It is well known that useful genes tend to be shared among microorganisms. The present study strengthens previous studies in showing that gene transfer is an important process in polar regions.

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Reply to the reviewers

We are very grateful about the thorough reading and deep understanding of the work that these 4 reviewers have provided. Although it is evident that they still request an improved profiling of some aspects, it is very encouraging that all four think the work is very interesting, original, insightful and adds a new layer of knowledge to the regulation of DNA damage sensing and repair. It is also very rewarding that the four reviewers estimate that this work will sew connections between different fields and interest a broad readership. This is why we have designed here a very deep revision, tailored to satisfy all the raised concerns except one, and this just for technical reasons.

Please find below the original reviewers’ comments and our answers to them preceded by the symbol “>”:

Reviewer #1 (Evidence, reproducibility and clarity (Required)): Ovejero et al. report an increase in lipid droplet (LD) abundance after long (from 120' on) exposure of budding yeast cells to DNA damaging agents zeocin and camptothecin (CPT). Next, they analyze DNA damage signaling in yeast mutants that impair triacylglycerol (TAGs) or sterol (STEs) esterification. They observe a slight anticipation in Rad53/CHK2 phosphorylation (indicative of DDR signaling) in yeast stem mutants, as well as in yeast cells or human cells lines pre-treated with oleate upon zeocin treatment. Yeast stem mutants are sensitive to zeocin and captothecin, but only confer sensitivity to hydroxyurea upon combination with tagD mutations. Authors relate these phenotypes to a somewhat decreases DSB resection in yeh2D mutants (expected to have reduced steryl esters pools) and RPA-foci in steD yeast cells. Next, a reduction in single strand annealing recombination repair events upon zeocin treatment is reported using a genetic reporter in steD mutants and oleate-treated cells. From these data they conclude that inability to process sterols in response to DSBs leads to an exacerbated DDR and prevents DNA repair. Next, it is shown that Flag-tagged Tel1 distinctly interacts with mono-phosphate phosphoinositides, including PI(4)P. An interaction in vivo is also inferred through Proximity Ligation Assays (PLA) using anti-PI(4)P and anti-ATM antibodies in human cell lines, which was moderately downregulated upon treatment with MMS or zeocin. Over-expression of the Osh4/OSBP1 transporter, which consumes PI(4)P, increased the number of Tel1 (nuclear) foci upon zeocin treatment. Conversely Sac1 ablation, in which accumulation of PI(4)P is expected, abrogated nuclear Tel1 foci formation and reduced telomere length (a phenotype related to lack of Tel1 function). From these results authors conclude that Tel1 availability in the nucleus is influenced by PI(4)P availability. Lastly, treatment with an OSBP1 inhibitor led to a cell line and damaging agent -variable reduction of ATM phosphorylation and a mostly non-significant reduction of DNA resection, measured by native BrdU detection, in response to CPT treatment. Overall, authors conclude that i) biding of Tel1/ATM to PI(4)P modulates its functional availability in the nucleus, and that ii) DNA damage elicits the esterification and storage of sterols toward LDs, which contributes to tritate Tel1/ATM away from the nucleus dampening the DDR and affecting long-range resection.

Major comments: While the conclusion that Tel1/ATM binds PI(4)P and this interaction modulates Tel1/ATM functional availability at the nucleus is convincing, the conclusion that DSBs elicit a change in the metabolism of this lipid to "control" Tel1/ATM function is not demonstrated. The notion that sterol processing occurs in response to DSBs is not sufficiently supported by the data presented, as the increase in LD numbers is observed much after activation of the DDR (Rad53 phosphorylation) in Zeozin-treated yeast cells.

We are afraid that we have not been clear enough in explaining the kinetics giving rise to our model. As indicated by the reviewer, our work shows, through kinetic studies, that the storage of sterols within LD occurs at later stages than the activation of the DDR by Tel1 and Rad53 phosphorylation. Tel1 foci decline is necessary for subsequent engagement of downstream DNA long-range resection. Since we propose that sterol storage within LD is a means to attenuate Tel1 engagement at DSBs, it is thus logical (and thus compatible with the data we show) that LD number increase occurs simultaneously with Tel1 foci decrease, at late stages of the reactionWe will include this explanation and graph in the revised version of the work.

In addition, evidence is not provided on the mechanisms by which PI(4)P metabolism would be controlled, which would be expected to be DDR-independent as they are placed upstream of this signaling pathway in the author's model.

The key mechanism through which, in the end, PI(4)P metabolism will be controlled, is the esterification of sterols within LD. Given that, as clarified above, LD formation in response to DSBs occurs “late” (i.e., after 120 min), it is not excluded that the DDR itself can instruct, through phosphorylation of some effector(s), LD formation. In other words, by ordering LD formation, the DDR would be launching a self-limiting mechanism. In support, we now know, although we do not show in this work, that eliminating key DDR proteins prevents the formation of LD in response to DNA damage. Because of this, we have undertaken an educated-guess approach and chosen critical or rate-limiting enzymes in LD biology either possessing an S/T-Q cluster domain (predicted to be a phosphorylation substrate for the DNA Damage Response kinases (1), and/or retrieved in phospho-proteomic screens as specific DDR targets (2,3). This adds up to 28 proteins in S. cerevisiae and 45 proteins in Homo sapiens. Importantly, the emergent candidates fall into two identical categories in both organisms. To provide initial support for their pertinence, we have generated a point mutant in the putative S/T-Q cluster of one of the yeast candidates. Of high relevance, we find that the concerned mutant is impaired in correctly triggering LD formation in response to DNA damage, and we have now obtained a specific funding to pursue this characterization that, as such, constitutes a different work from the one presented in this manuscript. We hope that the reviewer is now convinced yet that she/he agrees in keeping this information for subsequent manuscript(s).

The damaging agents used have been suggested to alter the redox metabolism and even lipid peroxidation (Kitanovic 2009, Mizumoto 1993, Krol 2015, Todorova 2015, Ren 2019, Singh 2014). Hence it is possible that PI(4)P changes are not due to DSBs, but an indirect though relevant effect. In absence of direct evidence supporting an active regulation of PI(4)P dynamics in response to DNA breaks, this conclusion remains speculative and this should be noted in the manuscript.

We fully agree with the reviewer that the used genotoxins are triggering a myriad of effects which could elicit the same phenomenon by indirect means. Yet, we want to stress that the use of camptothecin, which elicits a very robust LD formation phenotype (Figure 1C), is very likely specific, as it is proven as a potent and direct trapper of Top1 onto DNA after having cleaved it. Nevertheless, we propose in the next paragraph two specific experiments to dismiss this problem, please see immediately below.

Authors conclude that LD is specific to DSB induction. This seems an overstatement as they just reported LD increases in response to two agents that also induce other kinds of DNA damage. To also strengthen the link between DSBs and PI(4)P modulation of Tel1 function, authors should analyze LD numbers, Rad53 phosphorylation and Tel1 nuclear re-localization in response to HO-induced DNA breaks (e.g., using the system employed in Figure 3C).

We humbly think that enzymatically-induced DNA breaks will both activate Rad53 phosphorylation and Tel1 nuclear concentration, as this has already been established, thus requiring no further exploration. Yet, it is very important to assess the reviewer’s suggestion concerning whether enzymatically-induced DNA breaks also trigger the formation of LD. To this end, we will perform two complementary studies in which, instead of using HO, which cuts only a few times in the genome, we will:

1. a) exploit the naturally DSB-accumulating mutant rad3-102, which we previously characterized in the past (4), and which we already exploit in this work for recombination analyses (Figure S4A), to evaluate whether it endogenously harbors more LD in comparison with the WT.
2. b) we have recently created a tool in which gRNAs targeted to different subsets of transposons in the genome can drive Cas9 to create DSB in a dose-dependent manner ((9), under revision in Genetics). We will use this system to monitor the LD formation in response to Cas9-triggered cuts. In addition, on figure 5A, significant differences in GFP-Tel1 foci abundance between WT and steD or yeh2D cells are only observed after 210', way after the slight effect on Rad53 phosphorylation is observed. This is at odds with the conclusion that Tel1 association to STEs modulates DDR signaling.

We are afraid that we have not been clear enough in explaining the kinetics giving rise to our model. As indicated by the reviewer, our work shows, through kinetic studies, that the storage of sterols within LD occurs at later stages than the activation of the DDR by Tel1 and Rad53 phosphorylation. Tel1 foci decline is necessary for subsequent engagement of downstream DNA long-range resection. Since we propose that sterol storage within LD is a means to attenuate Tel1 engagement at DSBs, it is thus logical (and thus compatible with the data we show) that LD number increase occurs simultaneously with Tel1 foci decrease, at late stages of the reactionWe will include this explanation and graph in the revised version of the work.

Minor comments:

Figure S1D and E, experiments should be carried out to include time points in which LD accumulation and cell cycle arrest are observed upon zeocin treatment (i.e., up to 210' as in Figure 1A)

We will provide cytometry profiles of cells at 210 min. These data exist already in our laboratory.

How do authors explain increased single strand annealing recombination frequencies in steD and oleate-treated wild type cells (Figure 4A). Should it not be expected that increased STEs also impair recombination induced by endogenous damage?

Only ste∆ (and not +oleate) indeed manifests an increase in basal recombination frequencies, likely arising from endogenous damage. Although the increase is observed, it is not significant. We agree anyway with the reviewer that, was the experiment to be repeated more times, the increase may be found significantly different. We do not have any honest proposal to explain this.

Data presented in figure 4B and 4C are not fully convincing. Performing time course experiments might help concluding if the differences observed represent a relevant defect in DSB processing.

We will perform a Pulsed Field Gel Electrophoresis (PFGE) kinetcis in response to zeocin with or without oleate pre-loading to reinforce the conclusion.

Is Figure 5B referring to Flag-tagged Tel1 or GFP-tagged Tel1 as stated in the figure legend?

There is a misunderstanding here, as the mentioned Figure 5B corresponds to P-ATM immunofluorescences in human cells, not to any tagged Tel1 experiment.

Treatment with the ATM inhibitor AZD0156 increased PI(4)P-ATM PLA signals. From these authors conclude that "association of ATM and PI(4)P inversely correlated with the need for ATM within the nucleus. Do they imply that treatment with ATM-inhibitors reduces the requirement for ATM function in the nucleus? The interpretation of this result should be further elaborated to sustain this conclusion.

We may have conveyed a wrong notion at this point. We do not imply at all that ATM inhibitors reduce the need for ATM in the nucleus. Instead, we imply that, by reinforcing ATM attachment to Golgi-resident PI(4)P, ATM inhibitors end up titrating ATM away from the nucleus. We will clarify our explanation to avoid misunderstandings.

An increase of GFP-Tel1 foci upon OSH4 overexpression is described on Figure 7B. These are described as nuclear in the results, but no reference is made in the figure or legend as to how nucleus positions are addressed in these experiments. This should be clarified.

We systematically combine the tagging of a nucleoplasmic protein (mCherry-Pus1) with the detection of GFP-Tel1 foci, as to unambiguously assess the nuclear position of Tel1 foci. We will include this explanation and the corresponding mCherry-Pus1 channel to clarify this.

Also, WT controls and quantifications should be included in the experiments shown on Figure 7C.

These experiments are quantified from the moment we did them, although we did not include such quantifications in the present version for the sake of space. We will do so in the revised version.

Reviewer #1 (Significance (Required)):

While the conclusion of lipid metabolism responding to DSBs is not convincing, the observation that Tel1/ATM function is modulated by PI(4)P biding is significant and advances the understanding on the function and regulation of this key kinase in promoting genome integrity maintenance. This is an unanticipated result which is highly novel and has implications for the modulation of Tel1/ATM function through pharmacological manipulation of lipid metabolism. This finding would be of broad interest for scientists working on the response to DNA damage and the maintenance of genome integrity. This reviewer belongs to that group and has limited expertise to evaluate the lipid metabolism genetic manipulation in the manuscript.

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

The authors show that cytoplasmic PI4P have a regulatory role on ATM response to DNA double strand breaks. The process involves a balance between exchange of PI4P between Golgi and ER in exchange of esterified sterols. The study is of interest, however provides indirect evidences to support their conclusions.

Major comments : 1). Since the major conclusion relates to PI4P association with ATM in basal conditions to keep ATM outside nucleus and known presence of PI4P, ATM in other organelles of a cell, further experiments such as cell fractionation experimental that show golgi specific interaction would support the main conclusion.

In continuation of 1st comment, since PI4P in substrate of PI4 phosphoinositol kinases, is there a competition between PI4kinases and ATM for PI4P binding should be addressed through immunoprecipitation studies.

First of all, we need to specify here that PI4kinases will phosphorylated PI4 to create PI(4)P. Thus, PI(4)P is the product, and not the substrate, of PI4kinases. We therefore do not expect any competition between such kinases and ATM.

Second, we take good note of the reviewer’s concern that the pool of PI(4)P at the Golgi may be shared, and also that it would be important to reinforce the notion of the relative subcellular localization of ATM under different treatments. To this end, we will perform the following integrative experiment:

Immunoprecipitation of PI(4)P could theoretically be done using our specific antibody, yet the IP efficiency of a lipid cannot be verified by western blot. Further, there are PI(4)P pools elsewhere in the cell that would mess up with interpretations. We therefore dismiss the use of anti-PI(4)P as a tool to perform immunoprecipitations.

Instead, to explore the impact of PI(4)P levels on ATM both at the Golgi and within the nucleus, we will split our cultures in two to either immunoprecipitate specific cytoplasmic Trans-Golgi Network-associated proteins (we will test separately TGN46 and GOLPH3); or the nuclear ATM-interacting factor MRE11 from nuclei, then blot for co-immunoprecipitated ATM. The relative co-immunoprecipitated ATM is expected to vary under different treatments to which the cells will be exposed, namely:

• untreated
• zeocin, to trigger ATM need in the nucleus
• OSBP inhibition (+/- zeocin), to stabilize PI(4)P at the Golgi
• PIK93, an inhibitor of PI4 kinases that prevents PI(4)P synthesis

2). The authors claim that the ATM retention is the main function of PI4P in Golgi. The authors should rule out the possibility that the phenotype observed on DNA damage response is not due to non availability of PI4P substrate for PI4P kinases, that have recently been shown to participate in genome integrity maintenance.

We want to explain that we do not intend to say that PI(4)P main function at the Golgi is ATM retention, as PI(4)P is a molecule binding and modulating multiple proteins, as for example the aforementioned GOLPH3. We will first revise our text to correct it, in case we have conveyed this incorrect notion, as it stems from the reviewer’s comment.

Second, the reviewer evokes the notion that PI(4)P can be the substrate of a second phosphorylation, which could give rise to PI(3,4)P or to PI(4,5)P, which could still undergo remodeling into PI(3)P, for example. Recent work by Dr Michael Sheetz’s lab demonstrated that this set of phosphoinositides serves to drive the nucleation and activation of the ATR-Chk1 branch of the DNA Damage Response upon genotoxic stress, yet was completely inert with respect to the ATM-Chk2 branch (5). To rule out the possibility, as evoked by the reviewer, that the oleate-induced DDR phenomena we describe relate to these other events, we have now explored the response of the ATR-Chk1 branch when comparing the response of zeocin-treated cells that have been pre-loaded or not with oleate. We observe that the ATR-Chk1 branch is unaltered by oleate loading. Thus, we can now propose that the PI(4)P branch exclusively modulates the ATM-Chk2 axis.

3). Does Oleate treatment influences Rad53 protein levels in addition to its phosphorylation that affect DNA damage response may be addressed.

Exponential cultures from three different WT, three different ste∆ and three different yeh2∆ strains have now been taken and pre-loaded for 2 hours with 0.05% oleate, then total levels of Rad53 (without induction of DNA damage) assessed. We can now formally say that basal levels of Rad53 protein are not altered by this incubation. We will include this control in the revised manuscript.

4). Does Yeh2 deletion reduces LDS should be checked.

We frequently use yeh2∆ cells in our studies. In particular, we have recently published work characterizing the phenotype of this strain with respect to the formation of lipid droplets in the nucleus (6). We are currently exploiting those same sets of data to quantify the total number of LD in order to satisfy the reviewer’s concern.

5). Figure 4D representation should show % of phospho reduction of initial activation and a better western blot image should be shown that show equal loading of samples.

We are currently repeating these gels and blots for the sake of clarity, as requested.

6). In immunoprecipitation experiments, kindly include isotypee IgG controls as well to rule out non-specificity.

Of course, this important control will be included every time.

Minor points: 1). Figure S1F do not show oleate treatment as presented in results section.

We will revise the accurate naming.

2). A better gel for S4B should be presented with ponceau of the same gel.

We are currently repeating this gel and associated blot for the sake of clarity, as requested.

3). Nuclear PI4Ps has also been previously reported, an explanation to the specific interaction of ATM and PI4P in the Golgi should be addressed/discussed.

We take it that the reviewer is referring here to the recent work by Fáberová et al (7) in which PI(4)P and PI(4,5)P were described as very dynamic in the nucleus, and mostly related then to mRNA transcription, splicing and export. We will reinforce the connection of our phenomenon to the Golgi-associated pool of PI(4)P thanks to the co-immunoprecipitation experiments proposed above, and will timely contextualize these in light of the paper by Fáberová and co-workers in the revised version. Thank you for reminding us of this work.

Reviewer #2 (Significance (Required)):

The current work definitely adds a layer in our understanding to ATM regulation and cross-talk between different PIKK family of kinases. ATM localisation in extra nuclear regions of a cell has been described earlier with significant impact on cell physiology such as mitochondria etc., ATM retention at golgi and limiting nuclear ATM levels is significant advance at ATM activity regulation, while signifying non canonical function of PI4P.

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

Summary:

In this manuscript, the authors propose that ATM/Tel1 signaling is regulated in a spatiotemporal manner during genotoxic stress both in yeast and mammalian cells. They show that Lipid droplets accumulate in response to genotoxic stress. As a consequence, there is a decrease of exchange of PI4P from the Golgi to ER, thus dampening ATM/Tel1 signaling by sequestering this kinase into the Golgi. The authors combined findings in yeast and mammals showing that this mechanism is conserved throughout eukaryotes. For this purpose, they use a vast number of techniques that support their proposed model.

Major comments:

The conclusions were made based on evidence combining yeast genetics, immunofluorescence, DNA end resection analysis and pharmacological interventions. The hypothesis that ATM is kept away from the nucleus by physically interacting with PI4P at the Golgi, thus allowing processive repair is bold and contributes for a better understanding of the choreography of the DDR kinases during DSB repair. However, many of the experiments in yeast and mammals show only mild phenotypes and there is no evidence that this mode of ATM dampening impact cell viability in mammals.

We agree with the reviewer that the effects associated to the reported phenomenon are indeed mild. This is a fact. We would like to remind that the metabolism of sterols is finely controlled, and at many different levels, in a very complex manner. For example, sterol increases in the cell will immediately be compensated by reduced synthesis, while synthesis inhibition will immediately promote uptake from the medium, and/or release from stores (for example, see (8)). As a natural consequence, the window of manipulation and, more importantly, the strength of the phenotypes we can uncover are small.

Therefore, I have some comments and suggestions of experiments that I think could improve the quality of the manuscript. I believe that most of these new experiments does not require much time and resources.

• Does oleate treatment in RPE-1/Huh-7 cells induce loss of viability? An experiment showing loss of viability like MT-assay or decreased cell proliferation would reinforce the importance of the mechanism proposed.

This experiment was already included in the previous version, yet it may have escaped the attention of the reviewer. We show in Figure S2E that oleate treatment restricts viability in Huh-7 cells alone, and also worsens their tolerance to zeocin. Perhaps we should reconsider moving this result to the main figures so that it does not go unnoticed.

• In yeast there is evidence that a ste delta strain show sensitivity to zeocin/CPT, but there is no experiment showing the same effect on cells lacking Yeh2. Since both strains share similar phenotypes, it would be interesting to show that increased kinetics of Rad53 signaling leads to sensitivity to genotoxins.

We have now performed this experiment, we will include the matching information for yeh2∆ cells, which agrees with the predictions.

• The conclusion that ste delta cells exposed to zeocin leads to unproductive events due to defects in DNA-end resection could be reinforced by a decrease in Rad52 foci. It has been previously shown by the group of Dr. Marcus Smolka, that inhibition of DNA-end resection decreases Rad52 foci (https://doi.org/10.1083/jcb.201607031). Since the authors were able to monitor Rad52-YFP (Figure S1A), it shouldn't consume time and resources.

The reviewer is right that this experiment should not be time- or resources-consuming. We will evaluate the accumulation of Rad52 foci in response to the concerned genotoxin in ste∆ cells.

• Since the authors propose that there is a DNA repair defect due to inhibition of long-range DNA-end resection, it would be important to monitor gamma-H2A(X) signal either in yeast or mammals.

Taking into consideration the reviewer’s suggestion, we have now performed anti-yH2AX immunofluorescence of all the implied conditions (genotoxins +/- oleate pre-load) and will quantify them to answer the concern.

• How do the authors exclude the possibility that yeast mutants or oleate treatment in yeast/mammalian cells change membrane permeability allowing an increase in genotoxin concentration?

Although this is a very reasonable criticism, we want to remind the data we present in Figure S4A in which we use the naturally DSB-bearing rad3-102 cells for recombination analyses, showing that, in the absence of any genotoxin, the same phenotype also applies. Yet, we want to reinforce the notion that LD formation in response to DSB can also occur when the breaks are not chemically, but physically, induced. To this end, and also to match a related request by Reviewer 1, we will:

1. a) exploit the naturally DSB-accumulating mutant rad3-102 (4) to evaluate whether it endogenously harbors more LD in comparison with the WT.
2. b) we have recently created a tool in which gRNAs targeted to different subsets of transposons in the genome can drive Cas9 to create DSB in a dose-dependent manner ((9), under revision in Genetics). We will use this system to monitor the LD formation in response to Cas9-triggered cuts. In addition, on figure 5A, significant differences in GFP-Tel1 foci abundance between WT and steD or yeh2D cells are only observed after 210', way after the slight effect on Rad53 phosphorylation is observed. This is at odds with the conclusion that Tel1 association to STEs modulates DDR signaling.

We are afraid that we have not been clear enough in explaining the kinetics giving rise to our model. As indicated by the reviewer, our work shows, through kinetic studies, that the storage of sterols within LD occurs at later stages than the activation of the DDR by Tel1 and Rad53 phosphorylation. Tel1 foci decline is necessary for subsequent engagement of downstream DNA long-range resection. Since we propose that sterol storage within LD is a means to attenuate Tel1 engagement at DSBs, it is thus logical (and thus compatible with the data we show) that LD number increase occurs simultaneously with Tel1 foci decrease, at late stages of the reactionWe will include this explanation and graph in the revised version of the work.

• It would be interesting to investigate genetic interactions between ste delta (or yeh2delta) and yeast mutants with DNA-end resection problems (exo1delta; sae2delta). For instance, it has been shown that Sae2 antagonizes checkpoint signaling by competing with Rad9 to DSB sites (https://doi.org/10.1073/pnas.1816539115). Also, cells lacking Sae2 show an increase in Rad53 signaling due to increased Tel1 Signaling. Therefore, an epistatic effect between these two pathways would reinforce the hypothesis of the manuscript.

we will build the double mutant sae2∆ yeh2∆ and assess the potential epistatic behavior they may display with respect to some key phenotypes (Tel1 foci formation, Rad53 phosphorylation…).

• The authors showed that Tel1-GFP does not accumulate in the nucleus in cells lacking Sac1 (Figure 7C). Tel1 is important to cope with increased DSBs in the absence of Mec1, thus avoiding genomic instability. Cells lacking both Mec1 and Tel1 show a sick phenotype with an exponential increase in gross chromosomal rearrangements and sensitivity to genotoxins. Therefore, does deletion of Mec1 (and Sml1) in sac1 delta phenocopies a mec1tel1 delta? Alternatively, does pharmacological inhibition of ATR in the presence of the OSBP1 inhibitor causes loss of viability or chromosomal aberrations?

We will delete SAC1 in mec1∆ sml1∆ and compare the fitness, through growth drop assays, with respect to the mutant tel1∆ mec1∆ sml1∆.

We will expose cells either to OSBP1 inhibitor, ATR inhibitor, or both, and assess the phosphorylation of their downstream common effector H2AX. Additionally, we will assess the effect on cell growth of the combination of ATRi and OSBP1i using synergy matrices. We will determine if the combination of both drugs synergizes or not to impair cell proliferation and reduce cell viability.

• Finally, it seems strange to me that ATR/Mec1 signaling is not mentioned throughout the entire manuscript. Does PI4P pathway affect only ATM/Tel1? In Figure 2D, an antibody against phospho-CHK1 could be used to monitor ATR signaling. In line with that, I would like to see in the discussion how these new findings are in line with evidence from a 2019 paper showing that phophoinositides PIP2 and PIP3, but not PI4P are important for ATR signaling (DOI: 10.1038/s41467-017-01805-9). They showed that a nuclear pool of PIP2 increases upon DNA damage induction and rapidly accumulates at DNA lesions. This event is important for the recruitment of ATR. Since PI4P is substrate for PIP2 synthesis and there is a nuclear pool of PI4P and PIP2, I think it is important to discuss if the results presented here are in line with these previous findings.

The reviewer evokes recent work by Dr Michael Sheetz’s lab demonstrating that a different set of phosphoinositides serves to drive the nucleation and activation of the ATR-Chk1 branch of the DNA Damage Response upon genotoxic stress, yet was completely inert with respect to the ATM-Chk2 branch (5). We have now explored, also to satisfy a similar concerned raised by Reviewer 2, the response of the ATR-Chk1 branch when comparing the response of zeocin-treated cells that have been pre-loaded or not with oleate. We observe that the ATR-Chk1 branch is unaltered by oleate loading. Thus, we can now propose that the PI(4)P branch exclusively modulates the ATM-Chk2 axis.

We will of course give the needed credit to this work and contextualize our findings accordingly.

Minor comments:

• Line 124: The correct is Figure S1E, lower panel and not Figure S1F -Lines 127-128: Figure S2A does not show zeocin treatment

Both minor mistakes will be corrected.

Reviewer #3 (Significance (Required)):

Together, these new findings, if corroborated by others, might be important to open new lines of investigation in basic and translational research regarding human diseases as explored in the discussion section. I believe this paper will attract attention not only from the DDR field but also from other areas of research such as nutrient and lipid signaling both in yeast and mammals. I hope I was able to collaborate in this review, since my main expertise is in the area of DNA damage signaling using budding yeast as an organism model.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

This is a very interesting study where Sara et al. demonstrated a link between lipid metabolism with DNA repair response (DDR). In this study, they have proposed ATM as a novel PI4P-effector. The sterol deposition into lipid droplets impacts the Golgi PI4P level due to lipid exchange machinery facilitated by OSBP1, therefore regulating the cytosolic retention of ATM due to PI4P binding. Although how lipid droplets in the cytosol sense the DNA damage and control the initiation of DDR by regulating ATM is still unclear, this study linked lipid biology/PI signaling to DNA damage repair and showed the evolutionary conservation of PI signaling and DNA repair machinery from yeast to humans. The experiments are well designed, nicely controlled, with a high quality of data presentation. With some improvements, this work could be a very interesting study attracting a broad readership.

In their model, ATM is PI4P-bound and sequestered inside the cytosol under basal conditions. Upon genotoxic stress, activation of OSBP1 removes PI4P and free PI4P-bound ATM for nuclear translocation of DNA repair. This could also be interpreted as genotoxic stress-induced PIP-kinase activity, where PI4P is processed into PIP2 or PIP3, somehow redirecting ATM into the nucleus to initiate its activation for DDR. Those aspects should be discussed and improved.

Both Reviewers 2 and 3 have somehow evoked a similar concern. More precisely, the work by Dr Michael Sheetz’s lab demonstrating that a different set of phosphoinositides serves to drive the nucleation and activation of the ATR-Chk1 branch of the DNA Damage Response upon genotoxic stress, yet was completely inert with respect to the ATM-Chk2 branch (5). We have now explored, to satisfy all reviewers’ concerns, the response of the ATR-Chk1 branch when comparing the response of zeocin-treated cells that have been pre-loaded or not with oleate. We observe that the ATR-Chk1 branch is unaltered by oleate loading. Thus, we can now propose that the PI(4)P branch exclusively modulates the ATM-Chk2 axis.

Additionally, we will of course give the needed credit to this work and contextualize our findings accordingly.

Upon stress, there is nuclear activation of p53-phosphoinositide (PI) signalosomes and PIP-kinases. Also, there is a significant PIP2 pool inside the nucleus with an involvement in DNA damage repair. Those papers and their relevance to the current study need to be discussed. If ATM is a novel PI4P-effector, there is also nuclear PI4P formation or nuclear PI4P accumulation upon stresses based on recent studies; how the ATM interacts with PIPn in the nucleus upon translocation? A know ATM substrate p53 is PIP2/PIP3 bound in the nucleus based on recent studies. Will ATM prefer to interact with other PIPn-bound proteins in the nucleus or PIPn regulate their interaction needs to be discussed.

These additional notions are in line with the previous paragraph presented by the reviewer, and our answers too. We will provide a constructive overview of all these ideas in the revised version of the manuscript.

Major points: 1. The PI4P-ATM complex is supported only by PLA and PIP strips. Need more robust biochemical characterization of the interaction: co-IP, lipid binding, and/or in vitro constitution.

We agree with the need to perform assays in which PI(4)P is embedded in a bilayer, as to confidently assess whether Tel1 can bind it in that context. We have now performed a pilot experiment in which we have confronted purified FLAG-Tel1 to liposomes harboring PI(4)P. Western blot analysis using anti-FLAG antibody shows the encouraging result that FLAG-Tel1 can be found there. As a control, we have performed the same process but in the absence of any liposomes. We observe that a residual fraction of FLAG-Tel1 can nevertheless be found in this control, most probably because the buffer used during the liposome assay makes part of FLAG-Tel1 precipitate.To avoid this type of background and to increase our trust in the results, we propose to perform the liposome assay but on a discontinuous density gradient, so that liposomes will be retrieved in the top layer (and bound FLAG-Tel1 with them, if that is the case), while any precipitated FLAG-Tel1 will be in the bottom fraction (liposome floatation assay). As a further control, we will include the same liposomes but lacking PI(4)P. We expect to be successful in the floatation assays. If we are not, we will repeat the experiment presented above to be confident that the observed increase is reproducible.

1. The use of drug inhibitors only in the final figure is problematic. KD or KO experiments should be performed to confirm that ATM and the exchanger are the relevant targets.

We have now used siRNAs against the exchanger protein, OSBP1, with a very high silencing rate success. We have next monitored the activation status of the chromatin-associated ATM target KAP1, in order to monitor the predicted decrease of ATM activity specifically inside the nucleus. Our results confirm the role of OSBP1, by KD experiments as requested by the reviewer, in attenuating ATM nuclear participation.

1. Poor quality of some WBs (e.g Fig. S1F).

We have now repeated the Western Blot to detect Rad53-P in response to 20 mM HU in WT versus ste∆cells.

1. Lack of statistical analyses for some data (e.g. Fig. 1B-E)

We had already included, in the previous version, the complete statistical analyses corresponding to Figures 1B to E and evoked here by the reviewer. They were indeed included in Figure S1C, and our brief reference to them in the text may have escaped her/his attention. We will make a clear reference to this in the revised version.

Additional clarification points:

Figure 1: No representative images were shown for quantifications in Figure 1C, D, E.

If the reviewer / editor estimates it pertinent, we can of course include them. Yet, they will be very redundant with the images displayed in Figure 1A.

Line 121: Should be Figure S1E, upper panel. Line 124: Should be Figure S1E, lower panel. Figure 2D-E, please show the quantification of the ratio of pCHK2/CHK2 with an N=3

We will correct / include the requested changes.

Figure S2B: needs quantification of NileRed staining to conclude induction in LD formation

We will quantify the LD as requested.

Figure 3C, to show the selectivity of ATM-binding toward PI4P, PLA of ATM with other PIPn species should be assessed, such as PI3P, PI4,5P2, and PI3,4,5P3.

We have provided an overview of the binding preferences of ATM with respect to the full battery of phosphoinositides in the strip-binding assay shown in Figures S5C and 6B. Other than that, we are afraid that PLA studies as the ones we develop in the current manuscript for PI(4)P are not feasible, since no reliable antibodies exist for most of the phosphoinositide species evoked by the reviewer.

Figure S6A, PI4P level could be assessed by IF staining using PI4P antibody besides using PI4P sensor.

We will use our PI(4)P antibody to monitor by immunofluorescence the behavior of this molecule in response to either MMS or zeocin, as suggested.

References

1. Cheung HC, San Lucas FA, Hicks S, Chang K, Bertuch AA, Ribes-Zamora A. An S/T-Q cluster domain census unveils new putative targets under Tel1/Mec1 control. BMC Genomics. 2012;
2. Bensimon A, Schmidt A, Ziv Y, Elkon R, Wang SY, Chen DJ, et al. ATM-dependent and -independent dynamics of the nuclear phosphoproteome after DNA damage. Sci Signal. 2010;
3. BastosdeOliveira FM, Kim D, Cussiol JR, Das J, Jeong MC, Doerfler L, et al. Phosphoproteomics Reveals Distinct Modes of Mec1/ATR Signaling during DNA Replication. Mol Cell. 2015;
4. Moriel-Carretero M, Aguilera A. A Postincision-Deficient TFIIH Causes Replication Fork Breakage and Uncovers Alternative Rad51- or Pol32-Mediated Restart Mechanisms. Mol Cell. 2010;37(5):690–701.
5. Wang YH, Hariharan A, Bastianello G, Toyama Y, Shivashankar G V., Foiani M, et al. DNA damage causes rapid accumulation of phosphoinositides for ATR signaling. Nat Commun. 2017;
6. Kumanski S, Forey R, Cazevieille C, Moriel-Carretero M. Nuclear Lipid Droplet Birth during Replicative Stress. Cells. 2022;11(1390).
7. Fáberová V, Kalasová I, Krausová A, Hozák P. Super-Resolution Localisation of Nuclear PI(4)P and Identification of Its Interacting Proteome. Cells. 2020;9(5):1–17.
8. Luo J, Yang H, Song BL. Mechanisms and regulation of cholesterol homeostasis. Nat Rev Mol Cell Biol [Internet]. 2020;21(4):225–45. Available from: http://dx.doi.org/10.1038/s41580-019-0190-7
9. Coiffard J, Santt O, Kumanski S, Pardo B, Moriel-Carretero M. A CRISPR-Cas9-based system for the dose-dependent study of 4 DNA double strand breaks sensing and repair 5 6. bioRxiv [Internet]. 2021;1–37. Available from: https://doi.org/10.1101/2021.10.21.465387.

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

Learn more at Review Commons

---

Referee #4

Evidence, reproducibility and clarity

This is a very interesting study where Sara et al. demonstrated a link between lipid metabolism with DNA repair response (DDR). In this study, they have proposed ATM as a novel PI4P-effector. The sterol deposition into lipid droplets impacts the Golgi PI4P level due to lipid exchange machinery facilitated by OSBP1, therefore regulating the cytosolic retention of ATM due to PI4P binding. Although how lipid droplets in the cytosol sense the DNA damage and control the initiation of DDR by regulating ATM is still unclear, this study linked lipid biology/PI signaling to DNA damage repair and showed the evolutionary conservation of PI signaling and DNA repair machinery from yeast to humans. The experiments are well designed, nicely controlled, with a high quality of data presentation. With some improvements, this work could be a very interesting study attracting a broad readership.

In their model, ATM is PI4P-bound and sequestered inside the cytosol under basal conditions. Upon genotoxic stress, activation of OSBP1 removes PI4P and free PI4P-bound ATM for nuclear translocation of DNA repair. This could also be interpreted as genotoxic stress-induced PIP-kinase activity, where PI4P is processed into PIP2 or PIP3, somehow redirecting ATM into the nucleus to initiate its activation for DDR. Those aspects should be discussed and improved.

Upon stress, there is nuclear activation of p53-phosphoinositide (PI) signalosomes and PIP-kinases. Also, there is a significant PIP2 pool inside the nucleus with an involvement in DNA damage repair. Those papers and their relevance to the current study need to be discussed. If ATM is a novel PI4P-effector, there is also nuclear PI4P formation or nuclear PI4P accumulation upon stresses based on recent studies; how the ATM interacts with PIPn in the nucleus upon translocation? A know ATM substrate p53 is PIP2/PIP3 bound in the nucleus based on recent studies. Will ATM prefer to interact with other PIPn-bound proteins in the nucleus or PIPn regulate their interaction needs to be discussed.

Major points:

1. The PI4P-ATM complex is supported only by PLA and PIP strips. Need more robust biochemical characterization of the interaction: co-IP, lipid binding, and/or in vitro constitution.
2. The use of drug inhibitors only in the final figure is problematic. KD or KO experiments should be performed to confirm that ATM and the exchanger are the relevant targets.
3. Poor quality of some WBs (e.g Fig. S1F).
4. Lack of statistical analyses for some data (e.g. Fig. 1B-E)

Additional clarification points:

• Figure 1: No representative images were shown for quantifications in Figure 1C, D, E.

• Line 121: Should be Figure S1E, upper panel.

• Line 124: Should be Figure S1E, lower panel.

• Figure 2D-E, please show the quantification of the ratio of pCHK2/CHK2 with an N=3

• Figure S2B: needs quantification of NileRed staining to conclude induction in LD formation.

• Figure 3C, to show the selectivity of ATM-binding toward PI4P, PLA of ATM with other PIPn species should be assessed, such as PI3P, PI4,5P2, and PI3,4,5P3.

• Figure S6A, PI4P level could be assessed by IF staining using PI4P antibody besides using PI4P sensor.

Significance

This is a very interesting study where Sara et al. demonstrated a link between lipid metabolism with DNA repair response (DDR). In this study, they have proposed ATM as a novel PI4P-effector. The sterol deposition into lipid droplets impacts the Golgi PI4P level due to lipid exchange machinery facilitated by OSBP1, therefore regulating the cytosolic retention of ATM due to PI4P binding. Although how lipid droplets in the cytosol sense the DNA damage and control the initiation of DDR by regulating ATM is still unclear, this study linked lipid biology/PI signaling to DNA damage repair and showed the evolutionary conservation of PI signaling and DNA repair machinery from yeast to humans. The experiments are well designed, nicely controlled, with a high quality of data presentation. With some improvements, this work could be a very interesting study attracting a broad readership.

In their model, ATM is PI4P-bound and sequestered inside the cytosol under basal conditions. Upon genotoxic stress, activation of OSBP1 removes PI4P and free PI4P-bound ATM for nuclear translocation of DNA repair. This could also be interpreted as genotoxic stress-induced PIP-kinase activity, where PI4P is processed into PIP2 or PIP3, somehow redirecting ATM into the nucleus to initiate its activation for DDR. Those aspects should be discussed and improved.

Upon stress, there is nuclear activation of p53-phosphoinositide (PI) signalosomes and PIP-kinases. Also, there is a significant PIP2 pool inside the nucleus with an involvement in DNA damage repair. Those papers and their relevance to the current study need to be discussed. If ATM is a novel PI4P-effector, there is also nuclear PI4P formation or nuclear PI4P accumulation upon stresses based on recent studies; how the ATM interacts with PIPn in the nucleus upon translocation? A know ATM substrate p53 is PIP2/PIP3 bound in the nucleus based on recent studies. Will ATM prefer to interact with other PIPn-bound proteins in the nucleus or PIPn regulate their interaction needs to be discussed.

Major points:

1. The PI4P-ATM complex is supported only by PLA and PIP strips. Need more robust biochemical characterization of the interaction: co-IP, lipid binding, and/or in vitro constitution.
2. The use of drug inhibitors only in the final figure is problematic. KD or KO experiments should be performed to confirm that ATM and the exchanger are the relevant targets.
3. Poor quality of some WBs (e.g Fig. S1F).
4. Lack of statistical analyses for some data (e.g. Fig. 1B-E)

Additional clarification points:

• Figure 1: No representative images were shown for quantifications in Figure 1C, D, E.

• Line 121: Should be Figure S1E, upper panel.

• Line 124: Should be Figure S1E, lower panel.

• Figure 2D-E, please show the quantification of the ratio of pCHK2/CHK2 with an N=3

• Figure S2B: needs quantification of NileRed staining to conclude induction in LD formation.

• Figure 3C, to show the selectivity of ATM-binding toward PI4P, PLA of ATM with other PIPn species should be assessed, such as PI3P, PI4,5P2, and PI3,4,5P3.

• Figure S6A, PI4P level could be assessed by IF staining using PI4P antibody besides using PI4P sensor.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors propose that ATM/Tel1 signaling is regulated in a spatiotemporal manner during genotoxic stress both in yeast and mammalian cells. They show that Lipid droplets accumulate in response to genotoxic stress. As a consequence, there is a decrease of exchange of PI4P from the Golgi to ER, thus dampening ATM/Tel1 signaling by sequestering this kinase into the Golgi. The authors combined findings in yeast and mammals showing that this mechanism is conserved throughout eukaryotes. For this purpose, they use a vast number of techniques that support their proposed model.

Major comments:

The conclusions were made based on evidence combining yeast genetics, immunofluorescence, DNA end resection analysis and pharmacological interventions. The hypothesis that ATM is kept away from the nucleus by physically interacting with PI4P at the Golgi, thus allowing processive repair is bold and contributes for a better understanding of the choreography of the DDR kinases during DSB repair. However, many of the experiments in yeast and mammals show only mild phenotypes and there is no evidence that this mode of ATM dampening impact cell viability in mammals. Therefore, I have some comments and suggestions of experiments that I think could improve the quality of the manuscript. I believe that most of these new experiments does not require much time and resources.

• Does oleate treatment in RPE-1/Huh-7 cells induce loss of viability? An experiment showing loss of viability like MT-assay or decreased cell proliferation would reinforce the importance of the mechanism proposed.
• In yeast there is evidence that a ste delta strain show sensitivity to zeocin/CPT, but there is no experiment showing the same effect on cells lacking Yeh2. Since both strains share similar phenotypes, it would be interesting to show that increased kinetics of Rad53 signaling leads to sensitivity to genotoxins.
• The conclusion that ste delta cells exposed to zeocin leads to unproductive events due to defects in DNA-end resection could be reinforced by a decrease in Rad52 foci. It has been previously shown by the group of Dr. Marcus Smolka, that inhibition of DNA-end resection decreases Rad52 foci (https://doi.org/10.1083/jcb.201607031). Since the authors were able to monitor Rad52-YFP (Figure S1A), it shouldn't consume time and resources.
• Since the authors propose that there is a DNA repair defect due to inhibition of long-range DNA-end resection, it would be important to monitor gamma-H2A(X) signal either in yeast or mammals.
• How do the authors exclude the possibility that yeast mutants or oleate treatment in yeast/mammalian cells change membrane permeability allowing an increase in genotoxin concentration?
• It would be interesting to investigate genetic interactions between ste delta (or yeh2delta) and yeast mutants with DNA-end resection problems (exo1delta; sae2delta). For instance, it has been shown that Sae2 antagonizes checkpoint signaling by competing with Rad9 to DSB sites (https://doi.org/10.1073/pnas.1816539115). Also, cells lacking Sae2 show an increase in Rad53 signaling due to increased Tel1 Signaling. Therefore, an epistatic effect between these two pathways would reinforce the hypothesis of the manuscript.
• The authors showed that Tel1-GFP does not accumulate in the nucleus in cells lacking Sac1 (Figure 7C). Tel1 is important to cope with increased DSBs in the absence of Mec1, thus avoiding genomic instability. Cells lacking both Mec1 and Tel1 show a sick phenotype with an exponential increase in gross chromosomal rearrangements and sensitivity to genotoxins. Therefore, does deletion of Mec1 (and Sml1) in sac1 delta phenocopies a mec1tel1 delta? Alternatively, does pharmacological inhibition of ATR in the presence of the OSBP1 inhibitor causes loss of viability or chromosomal aberrations?
• Finally, it seems strange to me that ATR/Mec1 signaling is not mentioned throughout the entire manuscript. Does PI4P pathway affect only ATM/Tel1? In Figure 2D, an antibody against phospho-CHK1 could be used to monitor ATR signaling. In line with that, I would like to see in the discussion how these new findings are in line with evidence from a 2019 paper showing that phophoinositides PIP2 and PIP3, but not PI4P are important for ATR signaling (DOI: 10.1038/s41467-017-01805-9). They showed that a nuclear pool of PIP2 increases upon DNA damage induction and rapidly accumulates at DNA lesions. This event is important for the recruitment of ATR. Since PI4P is substrate for PIP2 synthesis and there is a nuclear pool of PI4P and PIP2, I think it is important to discuss if the results presented here are in line with these previous findings.

Minor comments:

• Line 124: The correct is Figure S1E, lower panel and not Figure S1F
• Lines 127-128: Figure S2A does not show zeocin treatment

Significance

Together, these new findings, if corroborated by others, might be important to open new lines of investigation in basic and translational research regarding human diseases as explored in the discussion section. I believe this paper will attract attention not only from the DDR field but also from other areas of research such as nutrient and lipid signaling both in yeast and mammals. I hope I was able to collaborate in this review, since my main expertise is in the area of DNA damage signaling using budding yeast as an organism model.

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Referee #2

Evidence, reproducibility and clarity

The authors show that cytoplasmic PI4P have a regulatory role on ATM response to DNA double strand breaks. The process involves a balance between exchange of PI4P between Golgi and ER in exchange of esterified sterols. The study is of interest, however provides indirect evidences to support their conclusions.

Major comments:

1). Since the major conclusion relates to PI4P association with ATM in basal conditions to keep ATM outside nucleus and known presence of PI4P, ATM in other organelles of a cell, further experiments such as cell fractionation experimental that show golgi specific interaction would support the main conclusion.

2). In continuation of 1st comment, since PI4P in substrate of PI4 phosphoinositol kinases, is there a competition between PI4kinases and ATM for PI4P binding should be addressed through immunoprecipitation studies.

3). The authors claim that the ATM retention is the main function of PI4P in Golgi. The authors should rule out the possibility that the phenotype observed on DNA damage response is not due to non availability of PI4P substrate for PI4P kinases, that have recently been shown to participate in genome integrity maintenance.

4). Does Oleate treatment influences Rad53 protein levels in addition to its phosphorylation that affect DNA damage response may be addressed.

5). Does Yeh2 deletion reduces LDS should be checked.

6). Figure 4D representation should show % of phospho reduction of initial activation and a bettier western blot image should be shown that show equal loading of samples.

7). In ammunoprecipitation experiments, kindly include isotypee IgG controls as well to rule out non-specificity.

Minor points:

1). Figure S1F do not show oleate treatment as presented in results section.

2). A better gel for S4B should be presented with ponceau of the same gel.

3). Nuclear PI4Ps has also been previously reported, an explanation to the specific interaction of ATM and PI4P in the Golgi should be addressed/discussed.

Significance

The current work definitely adds a layer in our understanding to ATM regulation and cross-talk between different PIKK family of kinases. ATM localisation in extra nuclear regions of a cell has been described earlier with significant impact on cell physiology such as mitochondria etc., ATM retention at golgi and limiting nuclear ATM levels is significant advance at ATM activity regulation, while signifying non canonical function of PI4P.

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Referee #1

Evidence, reproducibility and clarity

Ovejero et al. report an increase in lipid droplet (LD) abundance after long (from 120' on) exposure of budding yeast cells to DNA damaging agents zeocin and camptothecin (CPT). Next, they analyze DNA damage signaling in yeast mutants that impair triacylglycerol (TAGs) or sterol (STEs) esterification. They observe a slight anticipation in Rad53/CHK2 phosphorylation (indicative of DDR signaling) in yeast stem mutants, as well as in yeast cells or human cells lines pre-treated with oleate upon zeocin treatment. Yeast stem mutants are sensitive to zeocin and captothecin, but only confer sensitivity to hydroxyurea upon combination with tagD mutations. Authors relate these phenotypes to a somewhat decreases DSB resection in yeh2D mutants (expected to have reduced steryl esters pools) and RPA-foci in steD yeast cells. Next, a reduction in single strand annealing recombination repair events upon zeocin treatment is reported using a genetic reporter in steD mutants and oleate-treated cells. From these data they conclude that inability to process sterols in response to DSBs leads to an exacerbated DDR and prevents DNA repair. Next, it is shown that Flag-tagged Tel1 distinctly interacts with mono-phosphate phosphoinositides, including PI(4)P. An interaction in vivo is also inferred through Proximity Ligation Assays (PLA) using anti-PI(4)P and anti-ATM antibodies in human cell lines, which was moderately downregulated upon treatment with MMS or zeocin. Over-expression of the Osh4/OSBP1 transporter, which consumes PI(4)P, increased the number of Tel1 (nuclear) foci upon zeocin treatment. Conversely Sac1 ablation, in which accumulation of PI(4)P is expected, abrogated nuclear Tel1 foci formation and reduced telomere length (a phenotype related to lack of Tel1 function). From these results authors conclude that Tel1 availability in the nucleus is influenced by PI(4)P availability. Lastly, treatment with an OSBP1 inhibitor led to a cell line and damaging agent -variable reduction of ATM phosphorylation and a mostly non-significant reduction of DNA resection, measured by native BrdU detection, in response to CPT treatment. Overall, authors conclude that i) biding of Tel1/ATM to PI(4)P modulates its functional availability in the nucleus, and that ii) DNA damage elicits the esterification and storage of sterols toward LDs, which contributes to tritate Tel1/ATM away from the nucleus dampening the DDR and affecting long-range resection.

Minor comments:

• Figure S1D and E, experiments should be carried out to include time points in which LD accumulation and cell cycle arrest are observed upon zeocin treatment (i.e., up to 210' as in Figure 1A)

• How do authors explain increased single strand annealing recombination frequencies in steD and oleate-treated wild type cells (Figure 4A). Should it not be expected that increased STEs also impair recombination induced by endogenous damage?

• Data presented in figure 4B and 4C are not fully convincing. Performing time course experiments might help concluding if the differences observed represent a relevant defect in DSB processing.

• Is Figure 5B referring to Flag-tagged Tel1 or GFP-tagged Tel1 as stated in the figure legend?

• Treatment with the ATM inhibitor AZD0156 increased PI(4)P-ATM PLA signals. From these authors conclude that "association of ATM and PI(4)P inversely correlated with the need for ATM within the nucleus. Do they imply that treatment with ATM-inhibitors reduces the requirement for ATM function in the nucleus? The interpretation of this result should be further elaborated to sustain this conclusion.

• An increase of GFP-Tel1 foci upon OSH4 overexpression is described on Figure 7B. These are described as nuclear in the results, but no reference is made in the figure or legend as to how nucleus positions are addressed in these experiments. This should be clarified. Also, WT controls and quantifications should be included in the experiments shown on Figure 7C.

Major comments:

• While the conclusion that Tel1/ATM binds PI(4)P and this interaction modulates Tel1/ATM functional availability at the nucleus is convincing, the conclusion that DSBs elicit a change in the metabolism of this lipid to "control" Tel1/ATM function is not demonstrated.

• The notion that sterol processing occurs in response to DSBs is not sufficiently supported by the data presented, as the increase in LD numbers is observed much after activation of the DDR (Rad53 phosphorylation) in Zeozin-treated yeast cells. In addition, evidence is not provided on the mechanisms by which PI(4)P metabolism would be controlled, which would be expected to be DDR-independent as they are placed upstream of this signaling pathway in the author's model. The damaging agents used have been suggested to alter the redox metabolism and even lipid peroxidation (Kitanovic 2009, Mizumoto 1993, Krol 2015, Todorova 2015, Ren 2019, Singh 2014). Hence it is possible that PI(4)P changes are not due to DSBs, but an indirect though relevant effect.

• In absence of direct evidence supporting an active regulation of PI(4)P dynamics in response to DNA breaks, this conclusion remains speculative and this should be noted in the manuscript.

• Authors conclude that LD is specific to DSB induction. This seems an overstatement as they just reported LD increases in response to two agents that also induce other kinds of DNA damage. To also strengthen the link between DSBs and PI(4)P modulation of Tel1 function, authors should analyze LD numbers, Rad53 phosphorylation and Tel1 nuclear re-localization in response to HO-induced DNA breaks (e.g., using the system employed in Figure 3C)

• In addition, on figure 5A, significant differences in GFP-Tel1 foci abundance between WT and steD or yeh2D cells are only observed after 210', way after the slight effect on Rad53 phosphorylation is observed. This is at odds with the conclusion that Tel1 association to STEs modulates DDR signaling.

Minor comments:

• Figure S1D and E, experiments should be carried out to include time points in which LD accumulation and cell cycle arrest are observed upon zeocin treatment (i.e., up to 210' as in Figure 1A)

• How do authors explain increased single strand annealing recombination frequencies in steD and oleate-treated wild type cells (Figure 4A). Should it not be expected that increased STEs also impair recombination induced by endogenous damage?

• Data presented in figure 4B and 4C are not fully convincing. Performing time course experiments might help concluding if the differences observed represent a relevant defect in DSB processing.

• Is Figure 5B referring to Flag-tagged Tel1 or GFP-tagged Tel1 as stated in the figure legend?

• Treatment with the ATM inhibitor AZD0156 increased PI(4)P-ATM PLA signals. From these authors conclude that "association of ATM and PI(4)P inversely correlated with the need for ATM within the nucleus. Do they imply that treatment with ATM-inhibitors reduces the requirement for ATM function in the nucleus? The interpretation of this result should be further elaborated to sustain this conclusion.

• An increase of GFP-Tel1 foci upon OSH4 overexpression is described on Figure 7B. These are described as nuclear in the results, but no reference is made in the figure or legend as to how nucleus positions are addressed in these experiments. This should be clarified. Also, WT controls and quantifications should be included in the experiments shown on Figure 7C.

Significance

While the conclusion of lipid metabolism responding to DSBs is not convincing, the observation that Tel1/ATM function is modulated by PI(4)P biding is significant and advances the understanding on the function and regulation of this key kinase in promoting genome integrity maintenance. This is an unanticipated result which is highly novel and has implications for the modulation of Tel1/ATM function through pharmacological manipulation of lipid metabolism. This finding would be of broad interest for scientists working on the response to DNA damage and the maintenance of genome integrity. This reviewer belongs to that group and has limited expertise to evaluate the lipid metabolism genetic manipulation in the manuscript.

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Reply to the reviewers

Reviewer #1 Virant and colleagues have devised well-thought-out experimentation and analysis pipelines to obtain unbiased measurements of kinetochore protein counts and distances from the centromeric histone known as Cnp1 in fission yeast. My concerns with this study are mainly regarding the clarity of some of the data analysis strategies and data presentation. The authors should be able to address these concerns without new experimentation.

We would like to thank reviewer 1 for their valuable comments. We have addressed all comments and highlighted the changed sections in our revised manuscript.

1. Segmentation of individual centromeres: In general, the authors are to be commended for including a detailed description of their procedures and analysis method. However, it wasn't readily clear to me exactly how they segmented individual centromeres. The lack of a consistent offset between the fluorescence spots corresponding to the protein of interest and Cnp1 in image in Figure 1 makes this issue even more confusing. It will help to display representative segmented individual kinetochores either in the main figure or a supplementary figure.

We thank reviewer #1 for this comment and highly appreciate that they value our effort for detailed method descriptions. We strongly agree: Correct segmentation and best-possible visualization are crucial for our analyses. We hope that the following clarifications help to understand our work better:

All images of the manuscript are reconstructed from localization files using Rapidstorm, which linearly interpolates the localizations on a subpixel grid and fills the pixels based on the distance between the localization and the center of the main subpixel bin to avoid discretization errors (Wolter et al., 2012). These images are then overlaid with a Gaussian blur corresponding to their localization uncertainty. In our opinion, this procedure gives the most realistic image impression of the data and results in reconstructed images that as best as possible mimic real fluorescence images. This is in our opinion a very important aspect when presenting SMLM data in reconstructed images as it is crucial that one - when looking at those images - does not over- or under-interpret the SMLM data. We extended the explanation in the manuscript: “For visualization, we aimed to reconstruct SMLM images that neither over- nor under-interpret the resolution of the SMLM data and resemble fluorescence images as closely as possible. Localizations were tracked together using the Kalman tracking filter in Rapidstorm 3.2 with two sigma, and the NeNA value used as sigma. Images were then reconstructed in Rapidstorm 3.2 with a pixel size of 10 nm. Rapidstorm linearly interpolates the localizations and fills neighboring pixels based on the distance between the localization and the center of the main subpixel bin to avoid discretization errors (Wolter et al., 2012). These images were then processed with a Gaussian blur filter based on their NeNA localization uncertainty in the open-source software ImageJ 1.52p (Schindelin et al., 2012). Importantly, images were only used for image representation purposes, all data analysis steps were conducted on the localization data directly (see data analysis).”

Importantly, individual centromeres were segmented not on the images but on the localization data directly which we visualized in a self-written 3D visualization software that has the functionality to e.g. zoom in and out and to switch or overlay channels. This flexible visualization tool allowed us to make the best-possible informed decisions for the cluster selections and pairing of POI/cnp1CENP-A pairs. We extended our explanation by: “For several manual steps, localizations were visualized in a custom software, which allows to zoom in/out flexibly and to switch/overlay between the sad1/POI/ cnp1CENP-A channels. Using this tool, individual localizations could be selected and classified. For channel alignment, localizations belonging to the same fiducial marker in all three channels were grouped together. Cells with visible kinetochore protein clusters in the focal plane were selected and classified as individual region of interests (ROIs) and all clusters were annotated. cnp1CENP-A clusters were paired together with corresponding POI clusters. Whenever there was any doubt whether two clusters belonged to the same kinetochore or whether a cluster represented a single centromere region or several, the clusters were discarded. Two exemplary data sets can be found in the zip-file Supplementary Data 1. The annotation work was quality-checked by cross-checking the annotation of two different persons.” Maybe interesting to add is that we initially and extensively tried several ways to fully automate the annotation. As all tested routines could not reach the quality of manually annotated data and had to a large extend be manually rechecked and corrected, we in the end directly annotated the data manually. We were rigorous in case of doubt: “Whenever there was any doubt whether two clusters belonged to the same kinetochore or whether a cluster represented a single centromere region or several, the clusters were discarded (manuscript page 10, section Visualization and Manual Analytics).”

Furthermore, the reviewer is right, we didn’t include too much visual data/results into our manuscript. We now showcase some examples for our annotation. In the zip-folder “Supplementary Data 1”, the reviewer will find two csv SMLM data examples of annotated localization data of cells with a mitotic spindle that passed the quality checks of drift control and channel overlay. For the first example, a cell with dam1 as POI, all 6 kinetochores are visible and all were grouped and separated from noise. One can also nicely see (due to the large distance of dam1 to cnp1CENP-A) which of the six belong to which spindle by the spatial orientation of the cnp1CENP-A and dam1 cluster to each other, and both groups of three have a pair that is spatially closer to the wrong pole, important for question 2 below. The second example, with spc7 as the example POI, has only 5 visible clusters. A closer look shows that one of them has unusual dimensions and a high number of localizations, representing most likely two overlapping centromeric regions. Thus, for this cell, only 4 kinetochore pairs were annotated for further analysis. Also, the cluster pairs are overlapping much more, so a direct decision to which spindle they belong to gets difficult.

Finally, we realized that the example cell used for figure 1 which we chose a long time ago for representative purposes actually is a dataset that did not pass the final quality controls of drift correction and channel overlay. Thus, it is not part of the data that was used for the results of this work. While it is pretty embarrassing that we did not realize earlier, we are really grateful for the reviewers’ question about it. We now replaced it by another example which nicely represents the data that went into the analysis and also represents the biological heterogeneity, not only in offset but also e.g. in shape: In this work, we simplify by ignoring any shape in our current analysis and only use cluster centroid distances. Kinetochore POI cluster shapes are currently investigated in a more detailed follow-up study.

1. Use the mixture coefficient: The authors use the coefficient λ to create a mixture model for the Bayesian inference of distances. The description provided in the methods section is not sufficient for an average reader to understand how this coefficient is ultimately used (I had to look up the code and then the Stan manual for a superficial understanding of this procedure). It will be very helpful to flesh out this part of the model. Similarly, notation for the model that they use should be included either in the Methods or in supplementary data so that casual readers can get some understanding of the model.

We added the following sentence to explain the significance of the mixture coefficient:

“The coefficient then corresponds to the prior probability that the centromere is attached to the first spindle pole.”

We are not sure whether we understand the last sentence of this comment correctly. We added more explanations and definitions to the Stan code (see kinetochore.stan) to make it easier to understand. However, the section “Distance calculation” is intended to give the reader a full understanding of all relevant parts of the model, a look at the code should therefore not be necessary. The Stan implementation of the model uses non-centered parameterization, which might make it appear more complex than what is described in the text. However, this is an implementation detail that is intended to make the posterior more well-suited for Monte Carlo estimation and does not change the underlying statistical model. It should therefore be of no concern to casual readers. Finally, we prepared a new Supplementary Figure S6 to visualize the model for all readers.

1. The regional centromeres in fission yeast can incorporate varying levels of Cnp1 depending on its expression level (e.g. see Aravamudhan et al. 2013 Current Biology, Joglekar et al. 2008 JCB). Much of this "extra" Cnp1 is likely to be incorporated at sites distal to the Cnp1 molecules that directly nucleate the kinetochore. Therefore, the centroid of Cnp1 molecules is likely to be "shifted" to some extent from the foundation of the kinetochore. Any shift in the Cnp1 centroid will be important especially when comparing the fission yeast measurements with the budding yeast data. The authors should ascertain whether such a shift can be detected by comparing the budding yeast and fission yeast measurements.

The reviewer is absolutely right, there is an active discussion in the field to which extend there are cnp1CENP-A molecules at distal sites and thus not part of the platform for the kinetochore structure. While different quantification methods in the literature partly disagree in cnp1CENP-A numbers, we have no indications that our own assessment by PALM imaging is wrong. In this study, we get a very stable (Suppl. Figure S9 b) cnp1CENP-A read-out by PamCherry1, which agrees with our Lando et al. 2012 study (a single color study with a different, much simpler protocol and using a different microscope with different settings and analysis routines, mainly using mEos2 but also some SI data on PamCherry1 for counting cnp1CENP-A molecules). Furthermore, the recombinant fusions in the native locus of cnp1CENP-A are stable and the strains show no signs of growth or phenotypic defects.

While we therefore can argue that we see a native level and undisturbed distribution of cnp1CENP-A, we nevertheless do not know how much of this cnp1CENP-A is involved in building up the kinetochore. What we believe to know is the following:

1. With our ChipSeq data in Lando et al. 2012 we explored the distribution and read-out hits of cnp1CENP-A within the outer repeats as well as the inner centromeric region of all three chromosomes (Figure 3 and SI in Lando et al. 2012). While cnp1CENP-A is highly populated within the ~ 10 to 15 kb large inner centromeric regions, there are less detections in the outer regions. Thus, while ChipSeq is not a quantitative method, we believe it’s showing the correct trend with some cnp1CENP-A in the outside regions but most cnp1CENP-A localizing in the inner region. We believe that in overexpression studies (like e.g. done both in Joglekar et al. 2008 & Aravamudhan et al. 2013), this most likely will differ (but we did not experimentally explore this).
2. We generally would argue that our distances are rather accurate using a symmetry and compaction argument. The about 10kb inner regions are a roughly 3.4 µm long DNA strands at a linear 1-dimensional scale but in vivo are highly compacted. Total kinetochore sizes as seen in EM data for mammalian cells are “approximately 250 nm wide and 80 nm deep, with an electron-opaque inner plate juxtaposed to the centromeric chromatin, a translucent gap layer, and an electron-opaque, chromatin-distal outer plate apparently embedding the plus ends of spindle microtubules” (Musacchio and Desai, Biology 2017, 6(1), 5; 10.3390/biology6010005) and for * pombe also in the 200 nm range (Ding et al., J Cell Biol (1993) 120 (1); 10.1083/jcb.120.1.141). We evaluated the cnp1CENP-A cluster shapes as seen in our SMLM data. The clusters show a major axis length of 218 ± 88 nm and a minor axis length of 110 ± 29 nm on average. Taking into account our NeNA localization precisions, this is in nice agreement with the EM data measuring the lateral extend of the kinetochore structure. All together, we would argue a) that there is no reason or any indication in the literature that cnp1CENP-A not directly involved in kinetochore nucleation preferably gets incorporated on only one of the distal sites and thus would cause an asymmetry. We rather would argue that they are randomly inserted on both sides at low level and thus keep the symmetry needed to determine the center of the cnp1CENP-A cluster involved as the kinetochore platform. We also would argue b) that the structure is highly compacted and thus errors caused by additional cnp1CENP-A molecules will be small in respect to our resolution. We cannot completely exclude that there is such an effect that would increase the measured distances, however, and given all other sources of error (drift correction, channel alignment, cluster selection etc.) this most likely is not the main factor in defining the widths of the posterior distributions as we obtain them (Suppl. Figure S7). This argument is supported by the fact that we do not see any indication of such an effect for cnp1CENP-A-close proteins. We carefully checked fta2, fta7 and cnp20 data and also included some examples for the reviewer (see innerPOIexamples.zip). We hope that the reviewer agrees with us that there is no indication for a systematic asymmetric offset between the POI and cnp1CENP-A clusters. Finally, our distance numbers nicely agree with the distances the Ries group has measured for S. cerevisiae in the co-submitted manuscript. They a) have a point centromere with presumably only one kMT and b) did not use cnp1CENP-A *as their reference, they used spc7KNL1 (spc105).

Virant and colleagues present a rigorous single-molecule localization-based analysis of the kinetochore protein copy number and organization within the fission yeast kinetochore. Although the fission yeast kinetochore has been extensively studied, the spatial organization of its kinetochore components has remained uncharacterized. This manuscript addresses this deficiency, and in concert with the budding yeast study, highlights the conserved and diverged features of the kinetochore in the two yeast species. Therefore, this manuscript will be of great interest to the kinetochore and cell division field.

We would like to thank the reviewer again for their very helpful and highly constructive review.

Reviewer #2

In this study, Virant and colleagues have applied single molecule localization microscopy to map the positions of proteins in the pombe kinetochore. This has not been reported previously and this study is both well-conducted and the data appear solid. They also use a modification of this technique to assess the stoichiometry of kinetochore proteins. The results that they obtain are broadly in line with several previous studies that use other methodology but not in fission yeast nor to this level of detail. There are some important novel conclusions from this work. I would like the authors to address the following concerns prior to publication:

We would like to thank Reviewer #2 for their appreciation of our work and their helpful remarks regarding our manuscript which we will answer below.

1. It is not clear to me why the sad1-Scarlet-I signal in Figure 1C, displays a grid-like pattern? This must be an artefact of image collection or processing. Could the authors explain this pattern since this may affect the ability to find a centroid position of this signal?

Thanks a lot for this comment. Yes, the grid-like pattern the reviewer observed is an artefact from image processing when compiling the exemplary composite 3-color images. We revisited the raw movie data and changed the procedure to produce the exemplary images to avoid this ugly artifact (which did not influence our data analysis as it is not present in the raw movies used for centroid determinations). Please note: we also changed the example cell for figure 1 due to reasons explained in the answer 1 to reviewer 1.

1. It is my understanding that the distances reported are based on the positions of the proteins in one dimension, along the spindle axis, consistent with other studies and as illustrated in Figure 1b. This should be clearly stated in the results section.

The model underlying our Bayesian inference is that cnp1CENP-A-POI and one of the two sad1 spindles are all on one “mitotic” axis, along the kinetochore microtubule. BUT the orientation of this mitotic axis is NOT necessarily parallel to the spindle axis. See Figure 1a, the in red drawn spindle axis is not necessarily parallel to the green drawn microtubules connecting the kinetochores to the spindle poles. (Please note, thanks to this comment, we found that our original sketch of Figure 1a was misleading and corrected for that.). Figure 1b in this respect is a bit misleading as only one spindle pole is shown. The slight difference between the kinetochore and spindle axis cannot be visualized with only half a spindle. For answering the reviewers comment no. 5, we also now plotted the measured offset from and relative position of cnp1CENP-A cluster centroids to the spindle axis, see below.

1. The distances between proteins in this study are measured during anaphase, whereas the distances measured in cerevisiae previously were in both metaphase and anaphase (Joglekar et al 2009) and in the accompanying manuscript (Cielinski et al) in metaphase. In the comparison of distances, it would be worth describing how the mitotic stage may have affected distances, since Joglekar et al, found significant positional changes in cerevisiae kinetochore proteins from metaphase to anaphase.

We would like to thank the reviewer for this comment. It sparked a longer discussion to precisely disentangle the cell cycle states. We afterwards went carefully through the literature again and added a column to Table S4 stating for which cell cycle phase(s) the individual works were conducted which we believe is highly useful when comparing the different data.

Discussing with the Ries group we made sure that we indeed measured the cells in the same state and that we in our manuscript made mistakes in defining it correctly. Important for S. pombe is, that while it is not possible to decide for 100% between metaphase and anaphase A, we can safely exclude anaphase B so that we can state that we did not image anaphase B: Supplementary Figure S10 shows that all spindle distances measured are smaller than one nuclear diameter which is given by 2-3 µm (MacLean 1964, 10.1128/jb.88.5.1459-1466.1964; Tda et al 1981, 10.1242/jcs.52.1.271) plus we ourselves measured a nup132 strain in early G2 phase and obtained 2.4 µm ± 0.19 µm (data not shown)). This is nicely in line with Joglekar et al. 2009 (this paper actually has a very good SI figure on exactly this topic, see Fig. S1) and corrected the manuscript accordingly. Thanks for pointing this out to remove this lapse in definitions.

__ 4. __It is hard to interpret the POI copy numbers in terms of each kMT. I am assuming that each cluster measured represents a single pombe kinetochore, containing 2-4 kMTs? If we assume that each pombe kinetochore can contain 2, 3, or 4 kMTs, then we might expect to see a trimodal dataset, I am guessing this was not seen in the data? Would it be possible to estimate protein numbers per kMT in Table 2, as done for the Cielinski et al study? I realize this would require an estimate of the number of kMTs per kinetochore. Alternatively, the authors are resolving individual kMTs, in which case this should be made clear.

Yes, the reviewer is absolutely correct, the clusters are associated with 2-4 kMT (as nicely resolved in Ding et al, J Cell Biol (1993) 120 (1); 10.1083/jcb.120.1.141). Thus, we can assume that 2-4 kinetochore structures are also involved per centromeric region. In our current analysis, we have to work with the average of 2-4 kMTs. The shapes of POI and cnp1CENP-A clusters we have in the SMLM data are definitely diverse, and we plan to extract more data on spatial distribution in the future, perhaps even at the level of individual centromeric regions, but we did not systematically explore shapes in this work. Thus currently, we cannot give a precise answer how individual regional kinetochores look like at the level of a single kinetochore, but we strongly agree with the reviewer that this will be highly interesting to explore further. In this manuscript, therefore, to compare the stoichiometries between the point centromere of S. cerevisiae and the regional centromere of S. pombe, we used ratios as given in Suppl. Table S4. These ratios provided us with comparable results across a wide range of literature since the ratios are only calculated internally for each study and not across studies (which would lead to compatibility issues).

For this study, we also labeled MT via atb2. Unfortunately, the SMLM experiments were very difficult as atb2 is also present everywhere else in the nucleus, in particular at the dense central MT bundle (see image below, white sad1-mScarlet-I, blue PamCherry1- cnp1CENP-A, and red mEos3.2-A69T-atb2). Thus, we could not resolve such fine details as single fibers for the kMTs: Most kMTs overlapped with the central fiber and due to the dense central MT bundle of atb2, the data of the atb2 channel could not be read-out neither in a quantitative nor complete way and we could not extract which percentage of atb2 molecules we actually successfully recorded in the SMLM data. Thus, especially visualizing fine fibers was difficult and the images obtained do not meet our quality standards – but the exemplary one below is maybe nevertheless informative in a qualitative way. Our current idea would be to use ExM plus SMLM, but this work would be a stand-alone study requiring the set-up and optimization of such a protocol.

1. The same kMT issue may affect the measurements of distances. Each pombe kinetochore contains multiple kMTs and it is not clear whether these would align perfectly on the spindle axis. Did the authors see anything in their data that would support the notion that individual kMTs are aligned on the axis (as illustrated in Figure 2) or whether they are slightly separated? This is itself a potentially important result.

It is important to note that we did not measure the distance in projection of the spindle axis (defined as sad1-sad1 centroid axis), see also question 2. We can show in our data that the main microtubule bundle between the spindles is angled to the kinetochore microtubules that connect the centroids of our three-color channels for each centromeric region in a sad1-POI-cnp1 axis. For sad1, we cannot simply determine which one of the two spindles is the correct one, thus we implemented a mixture model for our Bayesian model, see also answers to reviewer 1).

While in the budding yeast literature it has been measured by EM that there are only small angles of up to 6° between the two axes present (Joglekar et al. 2009, 10.1016/j.cub.2009.02.056, Figure S1), Ding et al. 1993 showed larger deviations for S. pombe. Our data agrees with these findings. In the new Suppl. Figure S12, we plotted the height of all measured cnp1CENP-A centroids, normalized to the spindle lengths to represent the angular distribution between the spindle and kMT axes and in absolute nanometer distances to show that most kinetochores are in direct vicinity to the central bundle and only few show heights larger than 150 nm (also technically important as our focal z-range is ~600 nm).

1. In all measurements of kinetochore protein intensity (both in this study and previous studies) there seems to be significant variation in the data for individual kinetochores, even for S. cerevisiae, which supposedly has a fixed number of the kMTs. The coefficient of variation is ~ 0.5 in the data shown in Table 2. Could the authors discuss the variability in POI copy numbers since it either reflects an inability to measure protein levels accurately or that there is some flexibility in kinetochore protein stoichiometry (or in this case differing numbers of kMTs per kinetochore - see point above)?

Regarding the variability in our counting data we indeed expect a mixture of biological and technical nature in line with what the reviewer argues above but intuitively would lean towards the latter, being technically limited by the read-out precision of quantitative PALM imaging using fluorescent proteins, which have finite maturation- and read-out efficiencies and possess limited signal-to-noise contrast. When discussing this comment and how we possibly could support our intuition by evidence, we realized that the main argument to be made is that the FtnA oligomer is a biologically highly defined structure and that the variance we obtain for our FtnA calibration standard indeed also directly can serve as a proxy for our technical variance. Using the results of 21.63 counts ± 10.2 STD for the 24mers and of 7.27 counts ± 2.72 STD for the 8mers, we thus can estimate that the technical variance causes a coefficient of variance of 0.35 to 0.5, thus almost completely explaining the experimentally seen coefficient of ~ 0.5. we added this argument to our manuscript by “The POI protein copy numbers as given in Table 2 show a large coefficient of variation. To assess to which extend this variability reflects a technical inability to measure protein levels accurately or some flexibility in kinetochore protein stoichiometry (e.g. due to differing numbers of kMTs per kinetochore), we can use the data of the FtnA oligomer counting standard: The FtnA oligomer is a biologically highly defined structure. Thus, our FtnA measurements can directly serve as a proxy for the contribution of the technical inaccuracy of our PALM imaging and analysis strategy to the variance. Using the results of 21.63 counts ± 10.2 STD for the 24mers and of 7.27 counts ± 2.72 STD for the 8mers, we can estimate that the technical inaccuracy causes a coefficient of variance of 0.35 to 0.5, thus almost completely explaining the experimentally seen coefficient of ~ 0.5 for our POI data (Table 2). Due to this high technical inaccuracy, we cannot resolve sub-populations of possibly different kinetochore structures (and thus POI copy numbers) on 2-4 kMTs in our current counting data (Supplementary Figure S9).”. Secondly, as the reviewer also pointed out earlier, we have a biological variance of 2-4 kMTs and thus must assume smaller and larger kinetochores on individual centromeres. Due to the high technical variance, we nevertheless cannot resolve sub-populations in our current counting data (please also compare to the data in Supplementary Figure S9).

Minor points:

Delete "an" from "...structure at an about 100 nm resolution" (page 3).

Thanks!

In Figure 2 the proteins in the schematic are color coded, but it is not clear what the coloured proteins are in all cases. Would it be possible to color code the adjacent text, e.g. Spc7 in orange.

Thanks for this suggestion, adjusted figure accordingly.

Also in this figure, the POI copy numbers are indicated by color coding of the data points. However, the points will likely be too small in the final figure for these colors to be clearly visible. Perhaps copy numbers could be indicated in another way or the "mean value" boxes could be larger?

We tested several options and decided to adjust the widths of the boxes.

Please define "N" in Table 2. e.g. N = number of kinetochores measured.

We added this information to the caption: “N number of centromeric regions analyzed.”

Reviewer #2 (Significance (Required)):

This manuscript, together with an accompanying one from Cielinski et al., are nice complementary studies that provide the first single molecule localization studies of the yeast kinetochore. Although other labs have used super-resolution methods to study individual kinetochore proteins; both of these new studies map distances between many proteins at the kinetochore and thus are able to produce maps of the overall kinetochore structure. Like the previous study using standard resolution methods (Joglekar et al, 2009. Current Biology 19, 694-699); these studies will likely provide a benchmark for future studies on eukaryotic kinetochore architecture, including those in mammalian systems. Additionally, this work will appeal to super-resolution microscopists.

My expertise is as a yeast kinetochore cell biologist.

We would like to thank Reviewer #2 again for their appreciation of our work and their valuable remarks and discussion points which improved our manuscript substantially during the revision phase.

Additional comments for both reviewers:

As the co-submitted manuscript from Cieslinski et al. 2021 re-analyzed all their distances and numbers during the revision phase, we updated the comparisons in Suppl. Table S4, S5 and our summary text: 1) their cnn1 distance measurement got corrected and no shows no deviation anymore to our data. Also, their protein copy numbers changed slightly. So we changed the summary from “Additionally, two organism-specific differences surfaced: cnp20CENP-T (cnn1) is located between spindle pole and cnp1CENP-A in our case (at similar distance as fta2CENP-P and fta7CENP-Q), whereas Cieslinski et al. position cnn1 (and mif2) behind cnp1CENP-A. Furthermore, the ratio of cnp20CENP-T to COMA is 1:0.9 in our case and 1:2.1 for S. cerevisiae“ to “Importantly, one substantial organism-specific difference for the inner kinetochore strategy surfaced: The ratio of cnp20CENP-T to COMA is 1:0.9 in our case and 1:2.0 for S. cerevisiae.” 2) Additionally, we were able to add a discussion about their new measurement of ask1 of the dam1 complex. Ask1 is a protein of the DASH ring. Their new distance measurement of S. cerevisiae ask1 fits to the distance we measure for S. pombe dam1 and thus supports our discussion that, for S.pombe, the C-terminus of dam1 localizes at the DASH ring and not at the ndc80 heads like for S. cerevisiae. We added this sentence to the summary: “Furthermore, the S. cerevisiae work measured the position of ask1, a protein of the DASH ring. Their positioning of S. cerevisiae ask1 is consistent with the distance we measured for S. pombe dam1 and thus directly supports our reasoning that the C-terminus of S. pombe dam1 is localized to the DASH ring and not to the ndc80 heads (like for S. cerevisiae).”

We found that we – very unfortunately - did a calculation mistake ourselves and used the inverse of the correction factor (multiplied with 0.9 instead of dividing with 0.9) when correcting our SMLM localizations to absolute protein counts. Thus, the numbers we gave in Table 2 and the color bar in Figure 2 were wrongly converted. We now corrected for this lapse.

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Referee #2

Evidence, reproducibility and clarity

In this study, Virant and colleagues have applied single molecule localization microscopy to map the positions of proteins in the pombe kinetochore. This has not been reported previously and this study is both well-conducted and the data appear solid. They also use a modification of this technique to assess the stoichiometry of kinetochore proteins. The results that they obtain are broadly in line with several previous studies that use other methodology but not in fission yeast nor to this level of detail. There are some important novel conclusions from this work. I would like the authors to address the following concerns prior to publication:

1. It is not clear to me why the sad1-Scarlett-I signal in Figure 1C, displays a grid-like pattern? This must be an artefact of image collection or processing. Could the authors explain this pattern since this may affect the ability to find a centroid position of this signal?
2. It is my understanding that the distances reported are based on the positions of the proteins in one dimension, along the spindle axis, consistent with other studies and as illustrated in Figure 1b. This should be clearly stated in the results section.
3. The distances between proteins in this study are measured during anaphase, whereas the distances measured in cerevisiae previously were in both metaphase and anaphase (Joglekar et al 2009) and in the accompanying manuscript (Cielinski et al) in metaphase. In the comparison of distances, it would be worth describing how the mitotic stage may have affected distances, since Joglekar et al, found significant positional changes in cerevisiae kinetochore proteins from metaphase to anaphase.
4. It is hard to interpret the POI copy numbers in terms of each kMT. I am assuming that each cluster measured represents a single pombe kinetochore, containing 2-4 kMTs? If we assume that each pombe kinetochore can contain 2, 3, or 4 kMTs, then we might expect to see a trimodal dataset, I am guessing this was not seen in the data? Would it be possible to estimate protein numbers per kMT in Table 2, as done for the Cielinski et al study? I realise this would require an estimate of the number of kMTs per kinetochore. Alternatively, the authors are resolving individual kMTs, in which case this should be made clear.
5. The same kMT issue may affect the measurements of distances. Each pombe kinetochore contains multiple kMTs and it is not clear whether these would align perfectly on the spindle axis. Did the authors see anything in their data that would support the notion that individual kMTs are aligned on the axis (as illustrated in Figure 2) or whether they are slightly separated? This is itself a potentially important result.
6. In all measurements of kinetochore protein intensity (both in this study and previous studies) there seems to be significant variation in the data for individual kinetochores, even for S. cerevisiae, which supposedly has a fixed number of the kMTs. The coefficient of variation is ~ 0.5 in the data shown in Table 2. Could the authors discuss the variability in POI copy numbers since it either reflects an inability to measure protein levels accurately or that there is some flexibility in kinetochore protein stoichiometry (or in this case differing numbers of kMTs per kinetochore - see point above)?

Minor points:

Delete "an" from "...structure at an about 100 nm resolution" (page 3).

In Figure 2 the proteins in the schematic are color coded, but it is not clear what the coloured proteins are in all cases. Would it be possible to color code the adjacent text, e.g. Spc7 in orange. Also in this figure, the POI copy numbers are indicated by color coding of the data points. However, the points will likely be too small in the final figure for these colors to be clearly visible. Perhaps copy numbers could be indicated in another way or the "mean value" boxes could be larger?

Please define "N" in Table 2. e.g. N = number of kinetochores measured.

Significance

This manuscript, together with an accompanying one from Cielinski et al., are nice complementary studies that provide the first single molecule localization studies of the yeast kinetochore. Although other labs have used super-resolution methods to study individual kinetochore proteins; both of these new studies map distances between many proteins at the kinetochore and thus are able to produce maps of the overall kinetochore structure. Like the previous study using standard resolution methods (Joglekar et al, 2009. Current Biology 19, 694-699); these studies will likely provide a benchmark for future studies on eukaryotic kinetochore architecture, including those in mammalian systems. Additionally, this work will appeal to super-resolution microscopists.

My expertise is as a yeast kinetochore cell biologist.

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Referee #1

Evidence, reproducibility and clarity

Virant and colleagues have devised well-thought-out experimentation and analysis pipelines to obtain unbiased measurements of kinetochore protein counts and distances from the centromeric histone known as Cnp1 in fission yeast. My concerns with this study are mainly regarding the clarity of some of the data analysis strategies and data presentation. The authors should be able to address these concerns without new experimentation.

1. Segmentation of individual centromeres: In general, the authors are to be commended for including a detailed description of their procedures and analysis method. However, it wasn't readily clear to me exactly how they segmented individual centromeres. The lack of a consistent offset between the fluorescence spots corresponding to the protein of interest and Cnp1 in image in Figure 1 makes this issue even more confusing. It will help to display representative segmented individual kinetochores either in the main figure or a supplementary figure.
2. Use the mixture coefficient: The authors use the coefficient λ to create a mixture model for the Bayesian inference of distances. The description provided in the methods section is not sufficient for an average reader to understand how this coefficient is ultimately used (I had to look up the code and then the Stan manual for a superficial understanding of this procedure). It will be very helpful to flesh out this part of the model. Similarly, notation for the model that they use should be included either in the Methods or in supplementary data so that casual readers can get some understanding of the model.
3. The regional centromeres in fission yeast can incorporate varying levels of Cnp1 depending on its expression level (e.g. see Aravamudhan et al. 2013 Current Biology, Joglekar et al. 2008 JCB). Much of this "extra" Cnp1 is likely to be incorporated at sites distal to the Cnp1 molecules that directly nucleate the kinetochore. Therefore, the centroid of Cnp1 molecules is likely to be "shifted" to some extent from the foundation of the kinetochore. Any shift in the Cnp1 centroid will be important especially when comparing the fission yeast measurements with the budding yeast data. The authors should ascertain whether such a shift can be detected by comparing the budding yeast and fission yeast measurements.

Significance

Virant and colleagues present a rigorous single-molecule localization-based analysis of the kinetochore protein copy number and organization within the fission yeast kinetochore. Although the fission yeast kinetochore has been extensively studied, the spatial organization of its kinetochore components has remained uncharacterized. This manuscript addresses this deficiency, and in concert with the budding yeast study, highlights the conserved and diverged features of the kinetochore in the two yeast species. Therefore, this manuscript will be of great interest to the kinetochore and cell division field.

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Reply to the reviewers

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Referee #2

Evidence, reproducibility and clarity

Summary:

Wang et al. present an evaluation of a new generation of time-of-flight-based mass spectrometer that improves on the fraction of ions factually used for detection of peptide analytes, thus boosting the sensitivity of the Zenotof 7600 system when compared to the same instrument with the duty-cycle-enhancing Zenotrap module disabled and also when compared to the previous generation instrument of the same vendor in some of the comparisons.

The authors position the MS acquisition technique as particularly suitable in combination with medium (micro-) and high ('analytical') flow and throughput methods where higher flow rates (vs. conventional nanoflow-LCMS) allow rapid sample turnover and high throughput, yet limit the efficiency of electrospray and ion transfer into the MS system, thus being in dire need for enhanced sensitivity of the MS system employed for detection. The competency of such an MS system for very low input materials as e.g. encountered in emerging single-cell proteomic workflows, typically employing nanoflow chromatography, was thus not part of the study.

Accordingly, a medium- (micro-flow) and very high ('analytical'-flow) throughput LC method were screened on the three MS (parameter) setups using human cell lysate digests typically utilized in such technical evaluations. Well-received, the authors further extended their analysis (for the new instrument) across additional sample types of clinical and extended biological interest and spanning different levels of complexity and dynamic range of contained protein analytes.

In addition, the authors also performed a controlled ratio 2-species mixture experiment which allows detailed benchmarking of proteome coverage as well as the quality of protein quantification in a known differential comparison for the medium throughput (micro-flow) method.

The data quite convincingly demonstrate an increased sensitivity of the instrument based on similar identification performance in DIA bottom up proteomics from ca. 3- to 8-fold lower input peptide mass. However, I see a number of shortcomings mainly in the presentation and in part the completeness of the work, with specific comments below.

Major comments:

• Are the key conclusions convincing?

  • The concluded 10x sensitivity increase is overstating the observed numbers (x5-x8). In addition, the authors should at least discuss other changes than the Zeno trap incurred in the Zeno SWATH vs non-Zeno-SWATH DIA setups, particularly changes in accumulation times per m/z range, with Zeno Swath accumulating ~42 % longer per cycle spanning the same m/z range (85 vs 60 windows with 11ms per window) in the uflow method set and ~ 18 % longer in the high-flow method set (same window number but 13 ms vs. 11 ms dwell time per window). This should be discussed as one of the optimizations/factors contributing to the increased sensitivity observed in Zeno Swath measurements vs conventional SWATH. On that note, it was unclear to me when and where the 40 variable window SWATH method mentioned in the methods was used and where the settings can be found.
  • Since injected material is a critical parameter here, it would be good if it was mentioned also with the key conclusion on the increased number of confidently quantified peptides in microflow (based on the 2-species controlled quantity experiment).
  • Conclusions 'increasing protein identification numbers through the use of analytical-flow-rate chromatography' does not capture the observed data; the use of analytical-flow-rate does not convey an increase in protein identification numbers but enhanced sensitivity rather enables the maintenance of high protein identification numbers / proteome coverage despite/concurrent with analytical-flow chromatography
  • In titration curve experiments like these, probing proteome coverage from relatively small sample amounts, special care

  • Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

  • 'Zeno SWATH increases protein identification in complex samples<br /> 5- to 10-fold when compared to current SWATH acquisition methods on the same instrument' - At no point this is shown, a decrease of required input amounts by 5-8-fold (increase in sensitivity) is shown by the data, not a multiplication of protein identification rates by that factor.

  • 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.

  • Figure 1f, Supplemental Figure 1b, Figure 3 and Supplemental Figure 3 lack data for the Zeno SWATH method's performance at higher concentration. Given the fact that there is a clear, continuous trend of significant enhancement of proteomic depth in the highest 3 concentrations sampled by the Zeno SWATH method, I lack an assessment of the upper limit of proteome coverage achievable by the new platform when input material is not limited, or at least learn why injecting more is not advisable on the ZenoTOF 7600 system. It is clear that the region of interest is the lower loads where sensitivity gains are most pronounced, but with the strong trend in IDs per ng injected in the sampled range and discrepant range sampled by the non-Zeno method I feel there is a gap in the dataset and the upper ceiling of proteome coverage could be mapped out more thoroughly (At least for human cell lysate and possibly human plasma where trends appear most (log2-)linear).

  • Similarly, unless constrained for technical or practical reasons, I would suggest to find the ceiling for achievable proteome depth in analytical flow (4, 8 ug?)

  • 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.

  • All these should be re-injections of existing samples on these MS setups and a minor effort provided instrument availability (<1w) and rapid re-analysis via DIA-NN.

  • Are the data and the methods presented in such a way that they can be reproduced?

  • The raw data have not been deposited to a public repository. Reproducibility of the study would benefit significantly by raw data (including search results and spectral libraries with log files of creation) upload/sharing e.g. via ProteomeXchange/PRIDE.

  • If any software versions or firmwares on the hardware are required to perform the measurements on the ZenoTOF on the market today, these versions and prospective release dates should be included or the accessibility of these settings commented on.

  • Are the experiments adequately replicated and statistical analysis adequate?

  • Figures 3 and Supplemental Figure 3 need a clarification in the legend as to the nature and origin of ID numbers (mean? Number of replicates? Add error bars if possible)

  • The usage of DIA-NN for data analysis is somewhat unclear, in particular the in Methods/Spectral libraries "For the analysis of plasma samples, a project-independent public spectral library [29] was used as described previously [15]. The Human UniProt [30] isoform sequence database (UP000005640, 19 October 2021) was used to annotate the library and the processing was performed using the MBR mode in DIA-NN." The authors should address in a revised version whether the identification numbers reported stem from two-pass or single-pass analysis (i.e. when the feature termed Match-between-runs implemented since DIANNv1.8 was enabled and whether all runs, spanning different injection amounts were co-analyzed and data-re-queried for a targeted library containing precursors identified in high load samples in first pass analysis and then queried in low-load samples. In other words, are the low-load IDs independent of high load IDs? If not (i.e. the different loads were co-analyzed with MBR), what proteome coverage to the low sample loads reach bona fide, without the 'guidance' of high-load IDs?

Side note: Turning this around, could a high-load injection e.g. from a pool of limited-amount samples serve as a guiding element in a MBR-enabled analysis of a large cohort with limited sample amounts available per biological condition?

Minor comments:

• Specific experimental issues that are easily addressable.

  • The authors state the impact on dynamic range of identification when comparing ID sets against an external dataset with presumable cellular concentration numbers. I would in addition suggest comparing the dynamic range of the quantititative values observed from the available data which should provide a direct assessment of the dynamic range of quantification of the two methods.

  • Are prior studies referenced appropriately?

  • The statement that conventional DIA methods rely on nanoflow chromatography (p3, paragraph 3) is not accurate as there is previous implementations of data-independent acquisition MS of microflow separations, in part the group's work and referred to later in the text.

o Vowinckel, J. et al. Cost-effective generation of precise label-free quantitative proteomes in high-throughput by microLC and data-independent acquisition. Sci. Rep. 8, 4346 (2018)

o Bruderer, R. et al. Analysis of 1508 plasma samples by capillary-flow data-independent acquisition profiles proteomics of weight loss and maintenance. Mol. Cell Proteom. 18, 1242-1254 (2019).

It is correct that most early implementations of DIA-MS utilized nanoflow separations due to sensitivity and proteome coverage but DIA as such is a chromatography-flow-speed-agnostic principle and the concept to combine microflow LC with DIA not new, yet powerful as demonstrated by the authors and others previously and once again, here. - P.3 paragraph 3 'Moreover, the increased sensitivity of DIA methods has facilitated applications in large-scale proteomics, including system-biology studies in various model organisms, disease states, and species [5-9]' Include Ref 4 where improved sensitivity of DIA was demonstrated (at proteomic breadth..) - Are the text and figures clear and accurate?

-   Text and Figures need to be edited for typos, language, and clarity/accuracy.

1. Abstract 'Zeno SWATH increases protein identification in complex samples<br /> 5- to 10-fold when compared to current SWATH acquisition methods on the same instrument' - At no point this is shown, a drop of required input amounts by 5-8-fold (increase in sensitivity) is shown by the data, not a multiplication of protein identification rates.
2. P. 4 paragraph 3: Use terms 'consensus' or 'shared' identifications or similar to refer to the proteins identified in all 3 replicates, rather than 'reproducible' when discussing the reproducibility of peptide and protein quantification (as contrast to reproducibility of identification).
3. P.3 paragraph 2 'selects and fragments multiple charge ions' -> multiply charged (?)
4. P. 4 p. 1 'leading to under-detection' please clarify (leading to partial ion usage and limited sensitivity?)
5. P. 6 paragraph 3 'The gain in identification number of Zeno SWATH versus SWATH is mostly explained by an increased dynamic range: i.e. more low-abundance proteins are detected' - Reformulate/clarify: Is increased dynamic range of identifications against external quantities an explanation or perhaps simply the increased sensitivity with improved duty cycle?
6. Term 'active gradient' unclear. An inactive gradient is isocratic flow. Omit 'active'. Isocratic/other portions are overhead.
7. Figure 1 panel a) iteration scheme a-d) is redundant with the rest of the figure; use alternative iter scheme within panel a). Panel a) is further contains illegibly small fonts and should be edited for legibility
8. Revisit y-axis labels. Example: Fig. 1f) 'Precursors Identificaiton' -> Precursors identified/Precursor identifications. Correct throughout manuscript
9. ID bar graphs in all Figures: Cumulative IDs shade of grey is not properly visible, suggest alternate color scheme or add black color outline to the bars
10. Figure 1 e) legend 'along gradient length' -> gradient time / retention time
11. Figure 1 d) too small, trend lines mentioned in text invisible in graph. Boxplots very small.
12. There is three different terms used for the high throughput method (analytical-flow, high-flow, and another one.. please align where possible for clarity (i.e. choose 2 names for the 2 methods throughout the manuscript) etc..

13. Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

    • They authors may consider adding a short explanation of the term 'dynamic range coverage of identification' to contrast this from a direct assessment of dynamic range of quantitative values observed in this study.
    • 2-species controlled experiment: The discrepancy of observed vs true mixing ratios suggests the data were scaled during the analysis which, with these mixture ratios, tends to distort the accuracy (i.e. generates offset of observed from true ratio. That's very likely not a pipetting error on a log scale). In other words, you may want to evaluate the raw quantitative ratios (w/o any normalization/scaling applied) which should be more reflective of true/manual pipetting ratios in light of normalization strategy incompatibily with certain species mix scenarios (compare Supplementary Figure 1 a). Note to the editor(s): This will not affect the clear benefit of Zenotrap usage demonstrated by the 2-species benchmark as is but can be considered a minor yet recommended improvement (thus here).
    • The 2-species controlled experiment can reveal more information than currently extracted and I would recommend to show Zeno Swath and Swath xy scatters, including count-scaled density distributions of the observed ratios, side-by side. This would give deeper understanding of the large impact of the Zeno SWATH method. Also, I believe I haven't seen any instrument to date delivering precise quantification over as broad a dynamic range as surmisable from Fig. 1d) which might be worth wile highlighting.

Significance

Wang et al. describe a technical advance in ion usage and sensitivity based on an ion-trap device storing and focusing ions for TOF-based bottom-proteomics measurements. The study demonstrates improved sensitivity relative to previous generation instrumentation and also explores the impact of the specific trap device relative to the general improvements of the remaining MS system. The work outlines a route towards high coverage proteomics at very high throughput and robustness, as desirable in clinical proteomics and prospective personalized medicine approaches. While not all sample types of interest are limited to the amounts where the strongest improvements are seen in the presented data, large scale studies across expansive cohorts will likey be rendered more practical and realistic due to reduced instrument contamination at reduced loads and also further applications beyond those discussed in the manuscript will be rendered feasible on the newer generation instrument.

The improved ZenoTOF system and SWATH method follows a series of innovations in the mass spectrometry instrumentation, most notably and related the drastic improvement of ion utilization by storage e.g in a trapped ion mobility device earlier in the ion stream where, beyond an accumulation-based boost of sensitivity, ion mobility as a further biophysical properties is assessed in addition to the conventional m/z, as reviewed recently (doi: 10.1016/j.mcpro.2021.100138.). While these developments culminated and have been targeting low-flow, ultra-high sensitivity applications such as single-cell proteomics, the present study takes a different angle towards higher throughput measurements from significantly larger than single cell, but also significantly lower than historically required sample amounts that were prohibitive to a range of applications that are now easier to accomplish thanks to this and related work of the authors and others. The presented research appears of broad relevance and interest to the scientific community interested in protein abundance pattern analysis, in particular in larger (clinical) cohorts. Furthermore, the performance metrics on proteomic depth from human cell lysate digests will likely allow researchers with analytical quests other than those exemplified in the manuscript to extrapolate the ZenoTOF and Zeno SWATH suitability for their respective analytical targets.

Reviewer Field of expertise/background:

Quantitative proteomics. DIA mass spectrometry method & algorithm development & heavy usage. Protein Biochemistry. Molecular Biology.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript Wang et al, benchmark the new ZenoTOF with analytical and micro-flow set up and show impressive numbers of proteins identified and quantified. The paper is well written, and I have only a few minor comments:

1. Figure 1. many of the panels are hard to read. Especially 1a
2. Figure 1d. can the human amount not be normalised to log2=0?
3. Please provide in the legend the bin size for the figure in 1e.
4. Page 10 top: did SWATH identify more proteins than Zeno SWATH in plasma? There is something wrong as the figure shows something else. Also: That sentence in brackets is confusing.
5. Typo: page 10: respectively.
6. Please add raw data to PRIDE or a similar repository.

Significance

This is an impressive new technology that has been benchmarked by the Ralser group. It outperforms current state-of-the-art approaches.

The primary audience is the proteomics community.

My expertise is proteomics and quantitative mass spectrometry. I am well qualified to review this paper.

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Reply to the reviewers

1. General Statements [optional]

In our work, we quantified the abundance and positions of major kinetochore proteins within the metaphase kinetochore in budding yeast using single-molecule localization microscopy. Based on these measures, we revised the current model of the kinetochore and provided a nanoscale view of the complex.

We now revised our manuscript according to reviewers’ points. We performed new analyses to quantify the measurement errors and to justify our data analysis workflows. We further exploited the correlation-based analysis and found a correlation between the spreads of kinetochore proteins perpendicular to the spindle axis and their positions along the axis. We also discussed the potential non-centromeric pools and revised our model of the kinetochore. Further information on our analyses was now provided to improve the clarity. Changes to the text were implemented to better reflect our data. Information from relevant works was incorporated to better connect this work to the field.

We thank the reviewers for their points, which help us show the rigorousness of our analyses, further demonstrate the potential of our work, and improve clarity.

2. Point-by-point description of the revisions

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

The authors have developed a rigorous methodology for using single-molecule imaging of exogenously labeled kinetochore proteins to count and estimate their copy numbers and the average distance from the kinetochore protein Spc105. Although the method is technically sound, its application to the kinetochore raises some crucial questions below. My biggest concern is the effect of non-centromeric pools of the centromeric proteins Cse4, Cep3, and Ctf19 on the estimated copy number per kinetochore. The authors should be able to address most, if not all, questions by presenting a more in-depth data analysis.

Major points

1. Accounting for tilt of the yeast spindle relative to the image plane: It is not clear to me how the authors ascertain whether the spindle being imaged is nearly parallel to the image plane. In the companion fission yeast study, spindle poles are used for this purpose, but this study seems to rely only on the labeled kinetochore proteins. The criteria used to select the in-plane spindles should be clearly defined.

We thank the reviewer for pointing this out. We selected the in-plane spindles based on their average PSF size, which informs the z positions of the center of the kinetochore cluster (for simplicity, now all ’half-spindle’ was changed to ‘kinetochore cluster’). To calibrate the z position of kinetochore clusters, we first measured the width of the kinetochore cluster by fitting a cylindrical distribution. Overall, the kinetochores are likely symmetrically distributed around the spindle axes. Therefore, the height and the width of a kinetochore cluster should be the same. We then calibrated the z positions of the PSF size based on fluorescent bead data. Next, we plugged in the cylindrical distribution to the calibration curve to correlate the mean PSF size and position of the kinetochore cluster. We only took the kinetochore clusters with a mean PSF size

1. The effects of PSF depth on counting kinetochore proteins: The authors use a well-characterized nuclear pore protein as the reference to estimate kinetochore protein counts per half-spindle. Although this method appears rigorous in principle, I am unsure about the effect of the spatial distribution of kinetochores on the accuracy of the estimated number. Nuclear pore proteins are all localized within an 100 nm away from the focal plane even when the spindle is perfectly parallel to the focal plane. A discussion of this possibility, its effect on the protein count/distance estimates, and any mitigating factors is essential to highlight the caveats associated with the conclusions.

Based on the cylindrical distribution (see please the reply to point 1) of kinetochore clusters and their positions in z, we calculated the upper and lower boundaries of the distribution of kinetochore proteins in z, given a specific mean PSF size cutoff of a kinetochore cluster. Regardless of how stringent the cutoff is (130 and 135 nm), we made sure the boundaries do not exceed the imaging depth defined by our choice of the PSF size filtering (

1. Presentation of the cross-correlation analysis: The authors use cross-correlation for an unbiased calculation of the axial separation between a protein of interest and Cse4, but I am curious about the structure of the underlying data, and the intensity image in Figure 1 is not easy to examine. It will be helpful to include more analysis of the underlying data for at least a subset of the proteins (e.g., proteins at short, intermediate, and long distances from Cse4) as supplementary data.

2. The authors should include X and Y projections of the cross-correlation function.

3. Do the widths of cross-correlation functions (i.e., their spread perpendicular to the spindle axis) match across all proteins and experiments? This should be an almost invariant characteristic of the measurements, assuming that proteins within each kinetochore tightly cluster around the 25 nm microtubule. This line of thinking makes the large width of the cross-correlation shown in Figure 1 somewhat surprising.

4. It will also be interesting to test if the correlation between the positions of Spc105 molecules, especially perpendicular to the spindle axis, is comparable to the known separations between adjacent microtubules in the yeast spindle (the authors could use Winey et al. 1995 for serial-section EM of yeast spindles for comparison).

The reviewer is interested in the spread, or the size of the distribution, of a protein in a kinetochore along and perpendicular to the spindle axis. This is an interesting idea and can be done practically. However, the information can be more easily obtained based on auto-correlation instead of cross-correlation, due to its better signal-to-noise ratio along the dimension perpendicular to the spindle axis. Cross-correlations in that dimension are convoluted with background localizations and different localization precisions of the two channels. These factors are hard to interpret and disentangled. In auto-correlations, although the background is still present, it can be modeled and then removed easily, as now mentioned on page 15 lines 500-516.

Accordingly, we performed auto-correlation analysis on all the proteins and compared them to simulations representing different sizes. We find that the size of the distribution correlates to the position of the protein along the spindle axis. The results are now included as the new Fig. S5 and discussed on page 6 lines 169-176.

The cross-correlation analysis was based on only the position of the maximum value, not the projections. To keep the figure concise, we decided not to include the projections. However, the auto-correlation analysis was indeed based on projections, which we now included in Fig. S5.

Regarding the correlation between the positions of Spc105 molecules, we believe the reviewer actually refers to the correlation between the positions of kinetochores. Auto-/cross-correlations contain the information of the cluster sizes, based on the first peak (as shown in Fig. S5), and the relative distance (if the pattern is periodic). Unfortunately, the positions of kinetochores perpendicular to the spindle axis are not periodically distributed. Therefore, we cannot comment on the separations between adjacent microtubules.

1. Cse4 count (4 per kinetochore) and the model presented: One of the surprising conclusions of the study is that there are two nucleosomes associated with each microtubule attachment, with Mif2/CENP-C potentially interacting with both nucleosomes. There are two critical issues that the authors must consider.

(1) Fluorescent protein chimeras of Cse4 and CBF3 and COMA complex members do not exclusively localize to kinetochores. Biochemical studies show that both Cse4 and CBF3 proteins interact with non-centromeric DNA, e.g., see work from the Biggins lab regarding Cse4 over-expression and also from the Henikoff group that used ChIP-seq. I can't think of a similar reference for the CBF3 complex, but the DNA-binding proteins are also likely to interact with other parts of the genome. The non-centromeric protein is visible as a significant background fluorescence in wide-field microscopy, e.g., see Cep3 localization here: https://images.yeastrc.org/imagerepo/viewExperiment.do?id=202308&experimentGroupOffset=3&experimentOffset=0&experimentGroupSize=3

Similar background fluorescence can be detected for Cse4 and Ctf19. This extra-centromeric localization of Cse4, Cep3, and Ctf19 makes it possible that the protein counts included by the authors are "contaminated" to some extent by the extra-centromeric protein. The authors should discuss this possibility and how it might affect their counts.

After consideration, we agree with the reviewer that, specifically, a fraction of counted Cse4 molecules should be considered non-centromeric. We agree that the previous data is certainly sufficient to conclude it. The reviewer made a similar suggestion about COMA and CBF3 subcomplexes. In recent years a substantial portion of inner kinetochore components has been reconstituted. In Harrison et al. 2019, the Ctf19 complex structure has been solved. Two copies of the complex were observed. Therefore, the non-centromeric pool of COMA is certainly possible and we now made the adjustments to the text (page 8, lines 219-225) and Fig. 4. Accordingly, we now also modified the abstract (page 1, lines 26-27) and restructured the sections (page 10) to accommodate the different possibility of Cse4 copy numbers. While, fluorescence imaging of CBF3 presents a signal throughout the nuclear region we observed only four copies of Cep3 (part of CBF3). A CBF3 structure also has been resolved by Yan et al. 2018, in which the complex was proposed to exist as a dimer. This translates into four copies of Cep3. Therefore, we find it more suitable to leave all observed Cep3 (CBF3) molecules within a kinetochore model.

(2) The model drawn in Figure 4 makes explicit assumptions about the positioning of the four Cse4 molecules (or two nucleosomes) in each kinetochore relative to the rest of the kinetochore components. Yet, the data shown do not justify this specific arrangement. Lawrimore et al. 2011 claim that the non-centromeric Cse4 nucleosomes must be randomly distributed in the pericentromeric chromatin to evade detection in biochemical tests. Therefore, the nearest-neighbor analysis suggested above will be valuable for gaining new insights into the relative positioning of the centromeric- and non-centromeric Cse4 nucleosomes. A similar analysis for Cep3 and Ctf19 will also be helpful. If stereotypical positioning of these molecules cannot be detected, then the model should be revised accordingly (alternative models that are also consistent with the data can be included).

The reviewer has pointed out that Lawrimore et al. 2011 proposed and justified the existence of a non-centromeric Cse4 pool. This arrangement, also potentially along other inner kinetochore components, makes sense and our data did not indicate it otherwise. Therefore, we now revised our model accordingly by applying changes in the main text on page 10 lines 302-305 __as well as in __Fig. 4.

(3) I suggest one experiment that can help the authors better understand protein organization in one kinetochore. Joglekar et al. 2006 used a dicentric chromosome to isolate single kinetochores on the spindle axis to test the assumption that each kinetochore consists of approximately the same number of molecules of kinetochore proteins. The strains are easy to construct (transform existing strains with a linearized plasmid). Single kinetochores can be seen with a low but reasonable frequency. I leave the decision to perform the experiment to the authors' discretion depending on whether the experiment will be worth the effort in strengthening or enhancing their conclusions.

We performed the suggested experiment using the strain published in Joglekar et al. 2006 (kindly provided by Prof. Kerry Bloom) with Cse4 additionally tagged with mMaple. However, we always observed several super-resolved Cse4 clusters (likely of several kinetochores) overlapping with Nuf2-GFP diffraction-limited signal, therefore unable to assign a single isolated kinetochore to the lagging centromere.

1. Information regarding the degree of correction applied to calculate protein count per half-spindle: It will be helpful to include data regarding the degree of correction applied to the expected and measured numbers of NPC protein as supplementary data so that the readers can see the magnitude of this correction relative to the measured counts.

We would like to clarify that we did not correct the data. Instead, we calibrate the copy number, given that the copy number of Nup188 per NPC is known. We assume the same ratio between localization and copy number applies to both Nup188 and the kinetochore proteins. We now include a new Table S4 listing calibration factors of all experiments shown in Fig. 3.

Minor points:

1. McIntosh et al. JCB 2013 used microtubule plus-ends in serial section electron micrographs of yeast spindles to align the centromeric region and found a disk-shaped structure that roughly corresponds to the size of a single nucleosome ~ 80 nm away from the tip of the microtubule and centered the microtubule axis. The authors should refer to this finding in their discussion of the model that they present with two nucleosomes. In my opinion, this is compelling evidence for a nucleosome-like structure serving as the kinetochore foundation.

We agree with this reviewer's comment. The study, among others, present compelling evidence for a point-centromere. We now included the finding in the discussion on page 10, lines 293-294.

1. As discussed by the authors, the number of Cse4 molecules per kinetochore has been the subject of some controversy. Biochemical data from the Biggins group and ChIPseq data from the Westermann group (Altunkaya et al. 2016 Current Biology) strongly suggest that Cse4 molecules can only be found centered on the centromeric sequence. The latter reference should be included in the discussion.

Thank you for pointing this out. Indeed, this is important. We have now added the relevant reference in the discussion on__ page 10 lines 291-292__.

1. Although microscopy-based methods have estimated anywhere from 1, 2, to 6 Cse4 molecules per kinetochore, these studies generally agree on the stoichiometry between Cse4 and the rest of the kinetochore proteins, e.g., Ndc80 complex proteins are ~ 4-fold more abundant that Cse4, etc. The present study seems to disagree with protein stoichiometry. The authors may find it worthwhile to note this feature of their data.

We now discuss the stoichiometry difference between our results and others on page 11 lines 322-324.

1. Omission of the Dam1 complex from this study is disappointing to me personally, but I am sure that the authors have good reasons for this. They should briefly comment on the absence of the Dam1 complex in this study.

To provide information on the Dam1 complex, we imaged Ask1, a component of the complex. The measured positioning and copy number of the protein are now included in Fig. 2 and Fig. 3 respectively, and described and discussed in respective parts of the manuscript.

Reviewer #1 (Significance (Required)):

Cieslinski and colleagues present a single-molecule localization-based study to define the copy numbers and relative organization of kinetochore proteins in budding yeast. These numbers confirm and significantly refine prior measurements of the same aspects of the kinetochore. They also raise new questions and point to new research directions. The measurements also reveal a model of the protein organization of the budding yeast kinetochore in metaphase. For these reasons, the manuscript is of significant interest to the cell division field.

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

In this study, Cielinski and colleagues have applied single molecule localization microscopy to map the positions of proteins in the yeast kinetochore. This has not been reported previously and this study is both well-conducted and the data appear solid. They also use a modification of this technique to assess the stoichiometry of kinetochore proteins. The results that they obtain are broadly in line with several previous studies that use other methodology. There may be an improvement in accuracy using this new approach that has not been obtained previously and there are some important novel conclusions from this work. I would like the authors to address the following concerns prior to publication:

Major points

1. One interesting finding is that there is a discrepancy in the length of both the MIND and NDC80 complexes (from crystallographic data) with their relative positions. The authors suggest that the outer complexes could be twisted or rotated in respect of the spindle axis. It would be great if the authors could illustrate this in their model (or discuss it in the text), to demonstrate the required angle of twist/rotation of both complexes to account for the discrepancy. A twisted filament structure to the outer kinetochore does have some implications for its response to tension - a key determinant of kinetochore-microtubule attachment. It also may provide some flexibility to the structure under tension.

The discussion about this discrepancy has now been incorporated in the main text, page 9 lines 263-267. For clarity, we only partially reflect this in our schematic model (Fig. 4A; the MIND complex) but we already reflected this in the illustrative structural model in Fig. 4B.

1. For the experiment with cycloheximide, the authors state "Although we observed minor changes in copy numbers, the overall effect of CHX was small." For some proteins, Cse4i for example, there appears to be a significant decrease in intensity (30-40%) after cycloheximide treatment, see Figure S3. While the conclusion that tag maturation does not affect copy number measurements is sound, I suggest modifying this section to reflect the data.

We now modified the section accordingly by pointing out that Cse4i under CHX measurements led to reduction of the signal. The modification can be found on page 8 lines 207-211.

1. Page 5. The statement "These data agree reasonably well with previous diffraction-limited dual-color microscopy studies ..." provides readers with little ability to compare the data. I would like to see a supplementary figure comparing these new data with previous studies, especially those of Joglekar et al 2009, see Figure 3 in this paper.

We thank the reviewer for suggesting such a table. This will allow readers a direct comparison of the data between our study and Joglekar at al. 2009. The comparison can be found in new Table S1 __and __Fig. S4, which are now mentioned on page 5.

1. In terms of the distances quoted, are they in one dimension (as per Jogelkar et al 2009) or in three? The results section is entitled "...positions of kinetochore proteins along the metaphase spindle axis", which suggests a single dimension. Please make this very clear in the results section. In the discussion, is the statement "we mapped the relative positions of 15 kinetochore proteins along the kinetochore axis", which is not entirely clear. It seems from the methods that this is one dimension "...we determined the average distance between the two proteins along the spindle axis. “I suggest clarifying the results section briefly and clearly to indicate that this is a single dimension being measured and also using consistent wording of the axis measured throughout the text.

We agree the previous description may not be clear to the viewers. We now changed the text accordingly in the results section, page 5 lines 129-130.

Minor points:

Abstract: I would drop "all" from "For all major kinetochore proteins...", since full characterisation was performed on 14 proteins (9 in terms of copy number).

We now deleted “all” in the abstract as the reviewer suggested__.__

Page 2: "trough" to through.

Corrected.

Page 2 "S. cerevisiae" to italics

Corrected.

Methods p11. How do the MKY strains relate to common yeast genetic backgrounds? (e.g. are they S288C?).

MKY strains are derivative of S288C. The information was now updated in the Methods section and in Table S2.

Reviewer #2 (Significance (Required)):

This manuscript, together with an accompanying one from Virat et al., are nice complementary studies that provide the first single molecule localization studies of the yeast kinetochore. Although other labs have used super-resolution methods to study individual kinetochore proteins; both of these new studies map distances between many proteins at the kinetochore and thus are able to produce maps of the overall kinetochore structure. Like the previous study using standard resolution methods (Joglekar et al, 2009. Current Biology 19, 694-699); these studies will likely provide a benchmark for future studies on eukaryotic kinetochore architecture, including those in mammalian systems. Additionally, this work will appeal to super-resolution microscopists.

My expertise is as a yeast kinetochore cell biologist.

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Referee #2

Evidence, reproducibility and clarity

In this study, Cielinski and colleagues have applied single molecule localization microscopy to map the positions of proteins in the yeast kinetochore. This has not been reported previously and this study is both well-conducted and the data appear solid. They also use a modification of this technique to assess the stoichiometry of kinetochore proteins. The results that they obtain are broadly in line with several previous studies that use other methodology. There may be an improvement in accuracy using this new approach that has not been obtained previously and there are some important novel conclusions from this work. I would like the authors to address the following concerns prior to publication:

Major points

1. One interesting finding is that there is a discrepancy in the length of both the MIND and NDC80 complexes (from crystallographic data) with their relative positions. The authors suggest that the outer complexes could be twisted or rotated in respect of the spindle axis. It would be great if the authors could illustrate this in their model (or discuss it in the text), to demonstrate the required angle of twist/rotation of both complexes to account for the discrepancy. A twisted filament structure to the outer kinetochore does have some implications for its response to tension - a key determinant of kinetochore-microtubule attachment. It also may provide some flexibility to the structure under tension.
2. For the experiment with cycloheximide, the authors state "Although we observed minor changes in copy numbers, the overall effect of CHX was small." For some proteins, Cse4i for example, there appears to be a significant decrease in intensity (30-40%) after cycloheximide treatment, see Figure S3. While the conclusion that tag maturation does not affect copy number measurements is sound, I suggest modifying this section to reflect the data.
3. Page 5. The statement "These data agree reasonably well with previous diffraction-limited dual-color microscopy studies ..." provides readers with little ability to compare the data. I would like to see a supplementary figure comparing these new data with previous studies, especially those of Joglekar et al 2009, see Figure 3 in this paper.
4. In terms of the distances quoted, are they in one dimension (as per Jogelkar et al 2009) or in three? The results section is entitled "...positions of kinetochore proteins along the metaphase spindle axis", which suggests a single dimension. Please make this very clear in the results section. In the discussion, is the statement "we mapped the relative positions of 15 kinetochore proteins along the kinetochore axis", which is not entirely clear. It seems from the methods that this is one dimension "...we determined the average distance between the two proteins along the spindle axis."I suggest clarifying the results section briefly and clearly to indicate that this is a single dimension being measured and also using consistent wording of the axis measured throughout the text.

Minor points:

Abstract: I would drop "all" from "For all major kinetochore proteins...", since full characterisation was performed on 14 proteins (9 in terms of copy number).

Page 2: "trough" to through.

Page 2 "S. cerevisiae" to italics

Methods p11. How do the MKY strains relate to common yeast genetic backgrounds? (e.g. are they S288C?).

Significance

This manuscript, together with an accompanying one from Virat et al., are nice complementary studies that provide the first single molecule localization studies of the yeast kinetochore. Although other labs have used super-resolution methods to study individual kinetochore proteins; both of these new studies map distances between many proteins at the kinetochore and thus are able to produce maps of the overall kinetochore structure. Like the previous study using standard resolution methods (Joglekar et al, 2009. Current Biology 19, 694-699); these studies will likely provide a benchmark for future studies on eukaryotic kinetochore architecture, including those in mammalian systems. Additionally, this work will appeal to super-resolution microscopists.

My expertise is as a yeast kinetochore cell biologist.

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Referee #1

Evidence, reproducibility and clarity

The authors have developed a rigorous methodology for using single-molecule imaging of exogenously labeled kinetochore proteins to count and estimate their copy numbers and the average distance from the kinetochore protein Spc105. Although the method is technically sound, its application to the kinetochore raises some crucial questions below. My biggest concern is the effect of non-centromeric pools of the centromeric proteins Cse4, Cep3, and Ctf19 on the estimated copy number per kinetochore. The authors should be able to address most, if not all, questions by presenting a more in-depth data analysis.

1. Accounting for tilt of the yeast spindle relative to the image plane: It is not clear to me how the authors ascertain whether the spindle being imaged is nearly parallel to the image plane. In the companion fission yeast study, spindle poles are used for this purpose, but this study seems to rely only on the labeled kinetochore proteins. The criteria used to select the in-plane spindles should be clearly defined.
2. The effects of PSF depth on counting kinetochore proteins: The authors use a well-characterized nuclear pore protein as the reference to estimate kinetochore protein counts per half-spindle. Although this method appears rigorous in principle, I am unsure about the effect of the spatial distribution of kinetochores on the accuracy of the estimated number. Nuclear pore proteins are all localized within an < 100 nm3 volume. Therefore, all proteins within an in-focus nuclear pore will also be in focus. This is not the case with yeast kinetochores, especially in metaphase. A fraction of the kinetochores is likely to be > 100 nm away from the focal plane even when the spindle is perfectly parallel to the focal plane. A discussion of this possibility, its effect on the protein count/distance estimates, and any mitigating factors is essential to highlight the caveats associated with the conclusions.
3. Presentation of the cross-correlation analysis: The authors use cross-correlation for an unbiased calculation of the axial separation between a protein of interest and Cse4, but I am curious about the structure of the underlying data, and the intensity image in Figure 1 is not easy to examine. It will be helpful to include more analysis of the underlying data for at least a subset of the proteins (e.g., proteins at short, intermediate, and long distances from Cse4) as supplementary data.
   • The authors should include X and Y projections of the cross-correlation function.
   • Do the widths of cross-correlation functions (i.e., their spread perpendicular to the spindle axis) match across all proteins and experiments? This should be an almost invariant characteristic of the measurements, assuming that proteins within each kinetochore tightly cluster around the 25 nm microtubule. This line of thinking makes the large width of the cross-correlation shown in Figure 1 somewhat surprising.
   • It will also be interesting to test if the correlation between the positions of Spc105 molecules, especially perpendicular to the spindle axis, is comparable to the known separations between adjacent microtubules in the yeast spindle (the authors could use Winey et al. 1995 for serial-section EM of yeast spindles for comparison).
4. Cse4 count (4 per kinetochore) and the model presented: One of the surprising conclusions of the study is that there are two nucleosomes associated with each microtubule attachment, with Mif2/CENP-C potentially interacting with both nucleosomes. There are two critical issues that the authors must consider.
   • (1) Fluorescent protein chimeras of Cse4 and CBF3 and COMA complex members do not exclusively localize to kinetochores. Biochemical studies show that both Cse4 and CBF3 proteins interact with non-centromeric DNA, e.g., see work from the Biggins lab regarding Cse4 over-expression and also from the Henikoff group that used ChIP-seq. I can't think of a similar reference for the CBF3 complex, but the DNA-binding proteins are also likely to interact with other parts of the genome. The non-centromeric protein is visible as a significant background fluorescence in wide-field microscopy, e.g., see Cep3 localization here: https://images.yeastrc.org/imagerepo/viewExperiment.do?id=202308&experimentGroupOffset=3&experimentOffset=0&experimentGroupSize=3 Similar background fluorescence can be detected for Cse4 and Ctf19. This extra-centromeric localization of Cse4, Cep3, and Ctf19 makes it possible that the protein counts included by the authors are "contaminated" to some extent by the extra-centromeric protein. The authors should discuss this possibility and how it might affect their counts.
   • (2) The model drawn in Figure 4 makes explicit assumptions about the positioning of the four Cse4 molecules (or two nucleosomes) in each kinetochore relative to the rest of the kinetochore components. Yet, the data shown do not justify this specific arrangement. Lawrimore et al. 2011 claim that the non-centromeric Cse4 nucleosomes must be randomly distributed in the pericentromeric chromatin to evade detection in biochemical tests. Therefore, the nearest-neighbor analysis suggested above will be valuable for gaining new insights into the relative positioning of the centromeric- and non-centromeric Cse4 nucleosomes. A similar analysis for Cep3 and Ctf19 will also be helpful. If stereotypical positioning of these molecules cannot be detected, then the model should be revised accordingly (alternative models that are also consistent with the data can be included).
   • (3) I suggest one experiment that can help the authors better understand protein organization in one kinetochore. Joglekar et al. 2006 used a dicentric chromosome to isolate single kinetochores on the spindle axis to test the assumption that each kinetochore consists of approximately the same number of molecules of kinetochore proteins. The strains are easy to construct (transform existing strains with a linearized plasmid). Single kinetochores can be seen with a low but reasonable frequency. I leave the decision to perform the experiment to the authors' discretion depending on whether the experiment will be worth the effort in strengthening or enhancing their conclusions.
5. Information regarding the degree of correction applied to calculate protein count per half-spindle: It will be helpful to include data regarding the degree of correction applied to the expected and measured numbers of NPC protein as supplementary data so that the readers can see the magnitude of this correction relative to the measured counts.

Minor points:

1. McIntosh et al. JCB 2013 used microtubule plus-ends in serial section electron micrographs of yeast spindles to align the centromeric region and found a disk-shaped structure that roughly corresponds to the size of a single nucleosome ~ 80 nm away from the tip of the microtubule and centered the microtubule axis. The authors should refer to this finding in their discussion of the model that they present with two nucleosomes. In my opinion, this is compelling evidence for a nucleosome-like structure serving as the kinetochore foundation.
2. As discussed by the authors, the number of Cse4 molecules per kinetochore has been the subject of some controversy. Biochemical data from the Biggins group and ChIPseq data from the Westermann group (Altunkaya et al. 2016 Current Biology) strongly suggest that Cse4 molecules can only be found centered on the centromeric sequence. The latter reference should be included in the discussion.
3. Although microscopy-based methods have estimated anywhere from 1, 2, to 6 Cse4 molecules per kinetochore, these studies generally agree on the stoichiometry between Cse4 and the rest of the kinetochore proteins, e.g., Ndc80 complex proteins are ~ 4-fold more abundant that Cse4, etc. The present study seems to disagree with protein stoichiometry. The authors may find it worthwhile to note this feature of their data.
4. Omission of the Dam1 complex from this study is disappointing to me personally, but I am sure that the authors have good reasons for this. They should briefly comment on the absence of the Dam1 complex in this study.

Significance

Cieslinski and colleagues present a single-molecule localization-based study to define the copy numbers and relative organization of kinetochore proteins in budding yeast. These numbers confirm and significantly refine prior measurements of the same aspects of the kinetochore. They also raise new questions and point to new research directions. The measurements also reveal a model of the protein organization of the budding yeast kinetochore in metaphase. For these reasons, the manuscript is of significant interest to the cell division field.

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Reply to the reviewers

1. General Statements [optional]

Thank you for the peer review of our manuscript entitled “Hypoxia causes pancreatic β____-cell dysfunction by activating a transcriptional repressor BHLHE40” (RC-2022-01560). We greatly appreciate the reviewers’ constructive suggestions and your invitation to revise the manuscript. Below, we address the comments point-by-point and provide details of the changes we are planning to or have implemented. We believe that the revision plan will meet with the approval of the editor and reviewers. We also would be happy to respond to any further questions and comments that you may have.

2. Description of the planned revisions

Response to comments of reviewer 1

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

The authors examine the role of hypoxia-induced transcriptional repression in mediating loss of β-cell function in type2 diabetes. Transcriptional profiling of mouse and human islets exposed to low oxygen conditions revealed downregulation of β-cell identity and oxidative phosphorylation genes, and upregulation of genes associated with hypoxia. Identification of genes commonly upregulated in Min6 cells, mouse and human islets under hypoxic conditions, revealed induction of two transcriptional repressors BHLHE40 and ATF3. The authors further show that Bhlhe40 deficiency rendered β-cells resistant to hypoxic stress and restored glucose- and KCl-stimulated insulin secretion. This rescue in β-cell function was at least, in part, due to restoration of ATP generation and exocytosis of insulin granules. Furthermore, transcriptional profiling of Min6 cells overexpressing Bhlhe40 indicated down-regulation of key β-cell genes including Mafa. The authors elegantly show that BHLHE40 blocks PDX1 binding to Mafa transcription start site by binding to two E-box sites within the Mafa promoter/enhancer region. Lastly, Cre-mediated β-cell-specific deletion of Bhlhe40 in ob/ob mice restored expression of Mafa and exocytotic genes, accompanied by improvements in ATP generation and insulin secretion.

Major comments 1. The authors conclude that BHLHE40 regulates insulin secretion at two key steps: ATP generation and exocytosis. However, insulin secretory profiles with glucose and KCl seem to be similar with genetic manipulations of Bhlhe40 both in vivo and ex vivo. As the authors indicate in line 176, this suggests a more prominent role of BHLHE40 in regulating exocytotic events downstream of Ca2+ influx. Further experiments are therefore necessary to adequately address the effects on ATP generation. Given the observation that PGC1____α, a regulator of mitochondrial biogenesis is suppressed by BHLHE40, mitochondrial assessments would be crucial. Additionally, the effect on mitochondrial mass in Fig 3K seem to be marginal and need to be confirmed using additional measurements listed below.

We appreciate your constructive suggestion. According to your suggestions, we will explore the role of BHLHE40 in mitochondrial function in more detail.

a. In fig 3F, the authors show no change in KCl stimulated Ca2+ influx. Glucose stimulated Ca2+ influx needs to be examined to confirm regulation of ATP generation.

We thank the reviewer for pointing this out. We performed the experiment according to the suggestion. Please see section 3.

b. OXPHOS subunits, TOM20 levels by western blotting

We thank the reviewer for pointing this out. We will perform Western blotting to check the protein levels of OXPHOS subunits and TOM20 in control (Ctrl) and Bhlhe40 knockdown (KD) MIN6 cells cultured under 20% or 5% O­­­2.

c. mtDNA content, transcript levels by qRT-PCR

We will perform qRT-PCR to check the mtDNA content in Ctrl and Bhlhe40 KD MIN6 cells cultured under 20% or 5% O­­­2.

d. Functional assessments: Changes in mitochondrial membrane potential or oxygen consumption

We will evaluate mitochondrial membrane potential by MitoTracker Red staining in Ctrl and Bhlhe40 KD MIN6 cells cultured under 20% or 5% O­­­2.

2. Data presented in Figure 4 and 5 indicates transcriptional repression of Mafa by BHLHE40 as a mechanism of beta-cell dysfunction under hypoxic conditions. However, additional experiments are necessary to confirm that repression of PDX1-Mafa binding specifically is responsible for defects in GSIS -

a. Fig 5G shows inhibition of PDX1-binding to Mafa with overexpression of Bhlhe40. This needs to be confirmed under hypoxic conditions.

We thank the reviewer for pointing this out. Hypoxia for 16 to 24 hours decreases the expression levels of Pdx1 in mouse islets and MIN6 cells (Figure 1A and Sato Y., PLoS One 2014). In that condition, it is difficult to assess whether the reduction in PDX1 binding to Mafa enhancer is attributed to inhibition of PDX1 binding or PDX1 downregulation. Therefore, we will aim to determine the hypoxia exposure time during which Mafa expression is downregulated but Pdx1 expression is not affected. If we fail to identify the time, we plan to generate Pdx1-overexpressing MIN6 cell lines and evaluate PDX1 binding to Mafa enhancer in hypoxic conditions.

Sato Y. et al. Moderate Hypoxia Induces β-Cell Dysfunction with HIF-1–Independent Gene Expression Changes. PLoS One. 2014;9(12):e114868.

b. Fig 4H and 4I show restoration of insulin secretion normalized to total protein with AAV-Mafa. This needs to be supplemented with insulin content as MAFA has been implicated in regulating insulin gene expression (PMID: 25500951).

We thank the reviewer for pointing this out and agree with the comment on our original manuscript. We will evaluate insulin content by insulin ELISA assay in samples from AAV-Ctrl and AAV-Mafa-overexpressing MIN6 cells cultured under 20% or 5% O2. If the insulin content is affected by Mafa overexpression, insulin secretion will be adjusted by the intracellular insulin content.

c. qRT-PCR of exocytosis genes and ATP generation with hypoxia and AAV-Mafa.

We thank the reviewer for pointing this out. We will evaluate expression of exocytosis genes and ATP generation in AAV-Ctrl and AAV-Mafa-overexpressing MIN6 cells cultured under 20% or 5% O2.

d. Would mutation of A and C E-box sites restore PDX1 binding to Mafa TF region under hypoxia?

To address this question, we plan to introduce mutations in A and C sites of the Mafa gene in MIN6 cells by using CRISPR-Cas9 technology and then to examine PDX1 binding to the Mafa gene by ChIP assay under hypoxic conditions.

3. β-dedifferentiation has been proposed to be involved in loss of insulin secretion in T2D (PMID: 22980982, 16123366). One can speculate that transcriptional repression of Mafa by BHLHE40 is a component of a larger dedifferentiation phenomenon occurring under hypoxia, as other ____β-cell genes were decreased with hypoxia (Fig 1A) and Bhlhe40-OE in Fig 4A. Identifying differences in dedifferentiation and ____β-cell disallowed genes with Bhlhe40 overexpression (RNA seq, qRT-PCR) would therefore potentially reveal a dedifferentiation mechanism.

We thank the reviewer for pointing this out. Please see section 3.

4. The authors identify Atf3 as another transcriptional repressor enriched under hypoxia although to a lesser degree than Bhlhe40. The role of ATF3 in hypoxia-induced apoptosis and adaptive UPR has been previously suggested (PMID: 20519332, 20349223). Additionally, hypoxia represses adaptive UPR in models of T2D and drives ____β-cell apoptosis (PMID: 27039902). The authors discuss the role of ATF3 under hypoxia in the discussion (lines 319-324) and addressing these research gaps regarding ATF3 function would be insightful.

We are grateful for the reviewer’s comment. We will generate Atf3 knockdown MIN6 cell lines and examine the effect of ATF3 on hypoxia-induced apoptosis by PI/AnnexinV staining. If ATF3 is involved in hypoxia-induced apoptosis, we will also measure the mRNA expression levels involved in adaptive UPR.

Minor comments 1. In Fig 2E, increasing replicates would confirm no induction of Bhlhe40 with Thapsigargin.

Thank you for pointing out this issue. We will perform additional experiments to confirm the effect of thapsigargin on Bhlhe40 expression.

2. In Fig 2B, BHLHE40 bands need to be quantified to show time-dependent increase in protein levels.

Thank you for pointing out this issue. Please see section 3.

3. In Fig 3C, insulin content needs to be shown with Bhlhe40-OE as in Fig 3B with hypoxia.

Thank you for pointing out this issue. Please see section 3.

4. In Fid 4E-F, band intensities need to quantified by densitometry to determine degree of downregulation of MAFA.

We performed three independent experiments for Figure 4E. Please see section 3. We plan to perform additional experiments to determine the expression levels of MAFA (Figure 4F).

5. In Fig4H and 6G, insulin content needs to be shown as stated above.

We thank the reviewer for pointing this out. We will perform additional experiments to check the insulin content in these settings.

6. In Supplemental Figure 3C, apoptosis induced by hypoxia was assessed by PI staining that detects late apoptosis. No significant changes were observed with Bhlhe40-KD, but additional cell death assessments can be used to confirm that B40 does not affect ____β-cell death.

We thank the reviewer for mentioning this issue. To address this concern, we plan to investigate the effects of Bhlhe40 KD on the number of Annexin V-positive cells (early apoptosis) and cleaved (activated) caspase 3 expression in Ctrl and Bhlhe40 KD MIN6 cells under hypoxic conditions.

7. It would be interesting to see the rates of diabetes incidence in Bhlhe40KO: ob/ob mice and if Bhlhe40 deficiency protects against or delays development of diabetes.

Thank you for mentioning this issue. Please see section 3.

8. Knockdown efficiency shown in Supplementary figure 3A needs to be estimated by quantifying band intensities.

We plan to perform additional experiments to quantify the band intensities.

9. Line 43 should say "...reversed defects in insulin secretion."

We apologize for our incorrect explanation in the original manuscript. We have corrected this error in the text. Please see section 3.

Reviewer #1 (Significance (Required)):

The data presented provides novel mechanistic insights into the role of hypoxia in β-cell dysfunction. Studies in multiple models of type 2 diabetes (T2D) have shown the loss of signature β-cell genes including Ins1, Pdx1, Mafa, Slc2a2 as a result of excess nutrient stimulation and hypoxia; the precise causal mechanisms, however, still remain to be determined (PMID: 22980982, 28270834). A previous paper from the same group demonstrated downregulation of β-cell signature genes with hypoxia by a HIF1α independent mechanism (PMID: 25503986). Data presented in this report extend those observations and reveal a previously unappreciated role for transcriptional repressor BHLHE40 in the downregulation of a key β-cell gene Mafa. As the authors have identified additional transcriptional repressors including ATF3 and differentially expressed genes in both human and rodent β-cells, this paper would be of great value in understanding the effects of hypoxia. Moreover, studies in mouse models of T2D extend the association of BHLHE40 to clinical β-cell dysfunction and diabetes.

My areas of interest are pancreatic β-cell and mitochondrial physiology. GSE analysis and repression of PGC1α by BHLHE40, as appropriately discussed by the authors, point towards impaired mitochondrial function and ATP generation. Additional experiments would greatly support the role of BHLHE40 in mitochondrial dysfunction under hypoxia.

We thank the reviewer for his/her valuable comments.

Response to comments of reviewer 2

Reviewer #2 (Evidence, reproducibility and clarity (Required)): This study examines the role of BHEH40 in beta-cell function and its role in mediating the changes with 'hypoxia'. Most of the studies use 5% oxygen which is probably close to normal oxygen tension for islets, although it is not great for islet survival once the islets are removed from their normal vasculature. The human islet studies use 2% oxygen which would be actual hypoxia.

Major comments: Why were different oxygen concentrations used for mouse and human islets? What were the effects of 5% oxygen in human islets? Why was 5% oxygen chosen? 5% is close to normal oxygen tension that islets are exposed to in vivo, whereas 2% is not physiological.

We apologize for the lack of explanation in the original manuscript. Please see section 3.

If there was only 1 human donor, are the 2 and 3 RNA-seq technical replicates? If so, they do not show high replicability. Please discuss.

The reviewer is correct. We analyzed human islets from one donor for RNA-seq (Figure 1A). It would be preferable to obtain additional data derived from different human donor samples. Therefore, we plan to analyze human islets from another donor to show the replicability of increased expression of Bhlhe40 under hypoxic conditions.

Are the sequencing results from individual mice? Were the same mouse's islets used for normal and 5% oxygen or are they all different animals?

We apologize for the lack of explanation in the original manuscript. Results of RNA-seq were obtained from different animals. Please see section 3.

The whole gels with appropriate size markers need to be shown for all Westerns - they are not able to be appropriately reviewed in their current formats.

We apologize for the mistake. Please see section 3.

The histology in Figure 1K does not appear to match with the Western blot results in 1B, 1C which show a smaller but still clear band in the control 20% conditions, and in figures 1I and J in ob/ob and db/db controls. Lower power views showing most of the pancreas with a zoom-in shot of an example islet would be more appropriate. The immunofluorescence should be repeated to also include insulin so that beta-cells can be identified.

We thank the reviewer for mentioning this issue. We will repeat the immunohistochemical analysis according to the reviewer’s comments. We also plan to show the data on insulin staining.

What was the ____β-cell deletion efficiency of the knockdown mouse?

We apologize for the lack of explanation in the original manuscript. Please see section 3.

In the setting of hypoxia, would it be 'clinically' beneficial to have increased insulin secretion and thus metabolic demand? Please discuss.

We thank the reviewer for mentioning this important issue. Our results show that BHLHE40 controls at least two steps of insulin secretion: exocytosis and ATP generation. A relatively smaller reduction of Ppargc1a might suggest a more prominent role of BHLHE40 in regulating exocytosis rather than ATP generation (oxygen consumption step). Chronic hyperglycemia induces b-cell damage and impairs insulin secretion, a process known as glucotoxicity (Weir GC, Diabetes 2004, 2020). We believe that inactivation of BHLHE40 may help to reduce glucotoxicity by increasing insulin secretion. However, we would like to discuss this topic in more detail once we have investigated the roles of BHLHE40 in ATP generation (as suggested by reviewer 1).

Weir GC. et al. Five stages of evolving beta-cell dysfunction during progression to diabetes. Diabetes. 2004;53 Suppl 3:S16-21.

Weir GC. Glucolipotoxicity, β-Cells, and Diabetes: The Emperor Has No Clothes. Diabetes. 2020;69(3):273-278.

- Are the key conclusions convincing? Hard to assess the data in some cases - see above. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes, some of the conclusions are too strongly worded. An example is "However, hyperactivation of HIF in ____β-cells impairs insulin secretion by switching glucose metabolism from aerobic oxidative phosphorylation to anaerobic glycolysis (14-16)," this is too broad a statement. Hyperactivation of HIF in ____β-cells BY VHL DELETION impairs insulin secretion by that mechanism. Other ways of increasing HIF in ____β-cells do not all have this effect. So, the following part "suggesting that activation of HIF underlies ____β-cell dysfunction and glucose intolerance in hypoxia." Is not warranted. It would be fair to say "suggesting that unregulated over-activation of HIF may cause ____β-cell dysfunction.

We apologize for our incorrect explanation in the original manuscript. Please see section 3.

The paper is not off to a good start when the author spell Abstract as Abstruct - it suggests a spell-check was not performed. For the last sentence of the abstract, 'and its implication' - what implication?

We apologize for the typo and the poor description in the original manuscript. Please see section 3.

Line 64 High glucose conditions generate RELATIVE, not absolute hypoxia in beta-cells. This statement should also be referenced.

We apologize for our inaccurate explanation in the original manuscript. Please see section 3.

- Would additional experiments be essential to support the claims of the paper? See above.

- Are the data and the methods presented in such a way that they can be reproduced? Not enough detail for methods, but what is presented looks OK.

- Are the experiments adequately replicated and statistical analysis adequate? Unclear, see above.

- Specific experimental issues that are easily addressable.

- Are prior studies referenced appropriately? No, only the body of work on VHL, not HIFs.

- Are the text and figures clear and accurate? See above comments.

- Do you have suggestions that would help the authors improve the presentation of their data and conclusions? See comments about gels etc above.

We thank the reviewer for his/her valuable comments. Please see section 3 regarding to references.

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

The authors conclude that BHLHE40 regulates insulin secretion at two key steps: ATP generation and exocytosis. However, insulin secretory profiles with glucose and KCl seem to be similar with genetic manipulations of Bhlhe40 both in vivo and ex vivo. As the authors indicate in line 176, this suggests a more prominent role of BHLHE40 in regulating exocytotic events downstream of Ca2+ influx. Further experiments are therefore necessary to adequately address the effects on ATP generation. Given the observation that PGC1____α, a regulator of mitochondrial biogenesis is suppressed by BHLHE40, mitochondrial assessments would be crucial. Additionally, the effect on mitochondrial mass in Fig 3K seem to be marginal and need to be confirmed using additional measurements listed below.

a. In fig 3F, the authors show no change in KCl stimulated Ca2+ influx. Glucose stimulated Ca2+ influx needs to be examined to confirm regulation of ATP generation.

We thank the reviewer for pointing this out. In accordance with the reviewer’s comments, we examined the glucose-stimulated Ca2+ influx and found that the influx stimulated by 22mM glucose in Bhlhe40-overexpressing (OE) MIN6 cells was significantly smaller than that in control MIN6 cells (Figure 3, J and K). We have added this information to the manuscript, as follows: “In addition, glucose-stimulated [Ca2+]i levels were significantly attenuated by Bhlhe40 overexpression (Figure 3, J and K). These results indicate that BHLHE40 suppresses glucose-stimulated ATP generation and the increase of [Ca2+]i levels in MIN6 cells” (lines 197 to 200).

3. β-dedifferentiation has been proposed to be involved in loss of insulin secretion in T2D (PMID: 22980982, 16123366). One can speculate that transcriptional repression of Mafa by BHLHE40 is a component of a larger dedifferentiation phenomenon occurring under hypoxia, as other ____β-cell genes were decreased with hypoxia (Fig 1A) and Bhlhe40-OE in Fig 4A. Identifying differences in dedifferentiation and ____β-cell disallowed genes with Bhlhe40 overexpression (RNA seq, qRT-PCR) would therefore potentially reveal a dedifferentiation mechanism.

We thank the reviewer for pointing this out. To check whether genes involved in dedifferentiation and the expression of b-cell disallowed genes are controlled by BHLHE40, we examined the expression of these genes in Bhlhe40 OE MIN6 cells and found that it was not increased by BHLHE40. However, because the findings were detected under limited experimental conditions, at this point we cannot conclude that BHLHE40 does not cause dedifferentiation of b-cells and induction of b-cell disallowed genes.

Minor comments 2. In Fig 2B, BHLHE40 bands need to be quantified to show time-dependent increase in protein levels.

Thank you for pointing out this issue. We performed three independent experiments and showed statistically significant upregulation of BHLHE40 (Figure 2B).

3. In Fig 3C, insulin content needs to be shown with Bhlhe40-OE as in Fig 3B with hypoxia.

Thank you for pointing out this issue. Bhlhe40 OE did not affect the insulin content in MIN6 cells (Supplemental Figure 3F).

4. In Fid 4E-F, band intensities need to quantified by densitometry to determine degree of downregulation of MAFA.

We performed three independent experiments for Figure 4E. Bhlhe40 OE led to a 67.4% decrease in the expression of MAFA in MIN6 cells (Figure 4E).

7. It would be interesting to see the rates of diabetes incidence in Bhlhe40KO: ob/ob mice and if Bhlhe40 deficiency protects against or delays development of diabetes.

Thank you for pointing out this issue. We found that nonfasting blood glucose concentrations were similar in Ctrl:ob/ob (239.9 ± 19.6 mg/dl; n = 9) and bB40KO:ob/ob mice (215.2 ± 17.1 mg/dl; n = 6) at 12 weeks of age (Supplemental Figure 5F). We have added this information to the revised manuscript, as follows: “In these mice, BHLHE40 deficiency in b-cells had no effect on obesity (Figure 6B), insulin sensitivity (Supplemental Figure 5E), or nonfasting glucose concentrations (Supplemental Figure 5F)” (lines 282 to 285).

9. Line 43 should say "...reversed defects in insulin secretion."

We apologize for our incorrect explanation in the original manuscript and have corrected it accordingly.

Response to comments of reviewer 2

Reviewer #2 (Evidence, reproducibility and clarity (Required)): This study examines the role of BHEH40 in beta-cell function and its role in mediating the changes with 'hypoxia'. Most of the studies use 5% oxygen which is probably close to normal oxygen tension for islets, although it is not great for islet survival once the islets are removed from their normal vasculature. The human islet studies use 2% oxygen which would be actual hypoxia.

Major comments: Why were different oxygen concentrations used for mouse and human islets? What were the effects of 5% oxygen in human islets? Why was 5% oxygen chosen? 5% is close to normal oxygen tension that islets are exposed to in vivo, whereas 2% is not physiological.

We apologize for the lack of explanation in the original manuscript. We previously reported that hypoxic responses occur at 5% to 7% oxygen tension in MIN6 cells and mouse islets and that 3% hypoxia for 24 hours markedly increases MIN6 cell death (Sato Y., J Biol Chem 2011, Sato Y., PLoS One 2014). We also examined whether hypoxic responses occur at the same oxygen tension in human islets. Interestingly, in human islets, exposure to 2% but not 5% oxygen tension induced the upregulation of the SLC2A1 gene without apparent cell death. Another group also reported a hypoxic response in human islets in 2% oxygen (Puri S., Genes Dev. 2013). We have no adequate explanation as to why hypoxic responses occur at different oxygen tensions in mouse and human islets, but because of these findings, we used 5% oxygen in MIN6 cells and mouse islets and 2% oxygen in human islets. We have added this information to the text (lines 98 to 104) and Supplemental Figure 1A.

Sato, Y. et al. Cellular hypoxia of pancreatic beta-cells due to high levels of oxygen consumption for insulin secretion in vitro. J Biol Chem. 2011;286(14):12524-32.

Sato, Y. et al. Moderate hypoxia induces β-cell dysfunction with HIF-1-independent gene expression changes. PLoS One. 2014;9(12):e114868.

Puri S. VHL-mediated disruption of Sox9 activity compromises β-cell identity and results in diabetes mellitus. Genes Dev. 2013;27(23):2563-2575.

Are the sequencing results from individual mice? Were the same mouse's islets used for normal and 5% oxygen or are they all different animals?

We apologize for the lack of explanation in the original manuscript. Each sample was derived from different mice. We have clarified this point by describing “n = 3” as “n = 3 mice/group” and have added this information to the legends of Figure 1 and Supplemental Figure 1.

The whole gels with appropriate size markers need to be shown for all Westerns - they are not able to be appropriately reviewed in their current formats.

We apologize for the inappropriate presentation of the data. We have included whole gel images with molecular weight markers as supplemental material.

What was the ____β-cell deletion efficiency of the knockdown mouse?

We apologize for not including this information. Although we showed the expression levels of Bhlhe40 in the islets of bB40KO mice (original Supplemental Figure 5B), we did not explain the data in the text. The deletion efficiency in the islets was 74.1%. We have added this information to the revised text (lines 274 to 275).

- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes, some of the conclusions are too strongly worded. An example is "However, hyperactivation of HIF in ____β-cells impairs insulin secretion by switching glucose metabolism from aerobic oxidative phosphorylation to anaerobic glycolysis (14-16)," this is too broad a statement. Hyperactivation of HIF in ____β-cells BY VHL DELETION impairs insulin secretion by that mechanism. Other ways of increasing HIF in ____β-cells do not all have this effect. So, the following part "suggesting that activation of HIF underlies ____β-cell dysfunction and glucose intolerance in hypoxia." Is not warranted. It would be fair to say "suggesting that unregulated over-activation of HIF may cause ____β-cell dysfunction.

We apologize for our incorrect explanation in the original manuscript. We have corrected this accordingly, as follows: “However, hyperactivation of HIF in b-cells by von Hippel-Lindau (VHL) deletion impairs insulin secretion by switching glucose metabolism from aerobic oxidative phosphorylation to anaerobic glycolysis (15-17), suggesting that unregulated overactivation of HIF may cause b-cell dysfunction (12, 14)” (lines 73 to 77).

The paper is not off to a good start when the author spell Abstract as Abstruct - it suggests a spell-check was not performed. For the last sentence of the abstract, 'and its implication' - what implication?

We apologize for the typo and the poor description in the original manuscript. The spell check was performed by an editing company, and we did not notice the error. We have changed the last sentence of the Abstract, as follows: “Collectively, this work identifies BHLHE40 as a key hypoxia-induced transcriptional repressor in b-cells that negatively regulates insulin secretion by suppressing MAFA expression” (lines 47 to 49).

Line 64 High glucose conditions generate RELATIVE, not absolute hypoxia in beta-cells. This statement should also be referenced.

We apologize for our inaccurate explanation in the original manuscript. We have corrected this accordingly, as follows: “high glucose conditions generate relative hypoxia in b-cells because these cells consume large amounts of oxygen (Sato Y., J Biol Chem 2011; Bensellam M., PLoS One 2012; Bensellam M., J Endocrinol 2018; Ilegems E, Sci Transl Med 2022)” (lines 64 to 65).

Sato, Y. et al. Cellular hypoxia of pancreatic beta-cells due to high levels of oxygen consumption for insulin secretion in vitro. J Biol Chem. 2011;286(14):12524-32.

Bensellam, M. et al. Glucose-induced O₂ consumption activates hypoxia inducible factors 1 and 2 in rat insulin-secreting pancreatic beta-cells. PLoS One 2012;7(1):e29807.

Bensellam M. et al. Mechanisms of β-cell dedifferentiation in diabetes: recent findings and future research directions. J Endocrinol. 2018;236(2):R109-R143

Ilegems, E. et al. HIF-1α inhibitor PX-478 preserves pancreatic β cell function in diabetes. Sci Transl Med. 2022;14(638):eaba9112.

- Are prior studies referenced appropriately? No, only the body of work on VHL, not HIFs.

We apologize for our inadequate references about the involvement of HIFs in hypoxia-induced β-cell dysfunction. We have included the following references in the text (line 77):

Catrina, S.B. et al. Hypoxia and hypoxia-inducible factors in diabetes and its complications. Diabetologia. 2021;64(4):709-716

Gulton JE. Hypoxia-inducible factors and diabetes. J Clin Invest. 2020; 130(10):5063-5073

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

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Referee #2

Evidence, reproducibility and clarity

This study examines the role of BHEH40 in beta-cell function and its role in mediating the changes with 'hypoxia'. Most of the studies use 5% oxygen which is probably close to normal oxygen tension for islets, although it is not great for islet survival once the islets are removed from their normal vasculature. The human islet studies use 2% oxygen which would be actual hypoxia.

Significance

Major comments:

Why were different oxygen concentrations used for mouse and human islets? What were the effects of 5% oxygen in human islets? Why was 5% oxygen chosen? 5% is close to normal oxygen tension that islets are exposed to in vivo, whereas 2% is not physiological.

If there was only 1 human donor, are the 2 and 3 RNA-seq technical replicates? If so, they do not show high replicability. Please discuss.

Are the sequencing results from individual mice? Were the same mouse's islets used for normal and 5% oxygen or are they all different animals?

The whole gels with appropriate size markers need to be shown for all Westerns - they are not able to be appropriately reviewed in their current formats.

The histology in Figure 1K does not appear to match with the Western blot results in 1B, 1C which show a smaller but still clear band in the control 20% conditions, and in figures 1I and J in ob/ob and db/db controls. Lower power views showing most of the pancreas with a zoom-in shot of an example islet would be more appropriate. The immunofluorescence should be repeated to also include insulin so that beta-cells can be identified.

What was the β-cell deletion efficiency of the knockdown mouse?

In the setting of hypoxia, would it be 'clinically' beneficial to have increased insulin secretion and thus metabolic demand? Please discuss.

• Are the key conclusions convincing? Hard to assess the data in some cases - see above.
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes, some of the conclusions are too strongly worded. An example is "However, hyperactivation of HIF in β-cells impairs insulin secretion by switching glucose metabolism from aerobic oxidative phosphorylation to anaerobic glycolysis (14-16)," this is too broad a statement. Hyperactivation of HIF in β-cells BY VHL DELETION impairs insulin secretion by that mechanism. Other ways of increasing HIF in β-cells do not all have this effect. So, the following part "suggesting that activation of HIF underlies β-cell dysfunction and glucose intolerance in hypoxia." Is not warranted. It would be fair to say "suggesting that unregulated over-activation of HIF may cause β-cell dysfunction. The paper is not off to a good start when the author spell Abstract as Abstruct - it suggests a spell-check was not performed. For the last sentence of the abstract, 'and its implication' - what implication? Line 64 High glucose conditions generate RELATIVE, not absolute hypoxia in beta-cells. This statement should also be referenced.
• Would additional experiments be essential to support the claims of the paper? See above.
• Are the data and the methods presented in such a way that they can be reproduced? Not enough detail for methods, but what is presented looks OK.
• Are the experiments adequately replicated and statistical analysis adequate? Unclear, see above.
• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately? No, only the body of work on VHL, not HIFs.
• Are the text and figures clear and accurate? See above comments.
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? See comments about gels etc above.

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

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors examine the role of hypoxia-induced transcriptional repression in mediating loss of β-cell function in type2 diabetes. Transcriptional profiling of mouse and human islets exposed to low oxygen conditions revealed downregulation of β-cell identity and oxidative phosphorylation genes, and upregulation of genes associated with hypoxia. Identification of genes commonly upregulated in Min6 cells, mouse and human islets under hypoxic conditions, revealed induction of two transcriptional repressors BHLHE40 and ATF3. The authors further show that Bhlhe40 deficiency rendered β-cells resistant to hypoxic stress and restored glucose- and KCl-stimulated insulin secretion. This rescue in β-cell function was at least, in part, due to restoration of ATP generation and exocytosis of insulin granules. Furthermore, transcriptional profiling of Min6 cells overexpressing Bhlhe40 indicated down-regulation of key β-cell genes including Mafa. The authors elegantly show that BHLHE40 blocks PDX1 binding to Mafa transcription start site by binding to two E-box sites within the Mafa promoter/enhancer region. Lastly, Cre-mediated β-cell-specific deletion of Bhlhe40 in ob/ob mice restored expression of Mafa and exocytotic genes, accompanied by improvements in ATP generation and insulin secretion.

Major comments

1. The authors conclude that BHLHE40 regulates insulin secretion at two key steps: ATP generation and exocytosis. However, insulin secretory profiles with glucose and KCl seem to be similar with genetic manipulations of Bhlhe40 both in vivo and ex vivo. As the authors indicate in line 176, this suggests a more prominent role of BHLHE40 in regulating exocytotic events downstream of Ca2+ influx. Further experiments are therefore necessary to adequately address the effects on ATP generation. Given the observation that PGC1α, a regulator of mitochondrial biogenesis is suppressed by BHLHE40, mitochondrial assessments would be crucial. Additionally, the effect on mitochondrial mass in Fig 3K seem to be marginal and need to be confirmed using additional measurements listed below.
   • a. In fig 3F, the authors show no change in KCl stimulated Ca2+ influx. Glucose stimulated Ca2+ influx needs to be examined to confirm regulation of ATP generation.
   • b. OXPHOS subunits, TOM20 levels by western blotting
   • c. mtDNA content, transcript levels by qRT-PCR
   • d. Functional assessments: Changes in mitochondrial membrane potential or oxygen consumption
2. Data presented in Figure 4 and 5 indicates transcriptional repression of Mafa by BHLHE40 as a mechanism of beta-cell dysfunction under hypoxic conditions. However, additional experiments are necessary to confirm that repression of PDX1-Mafa binding specifically is responsible for defects in GSIS -
   • a. Fig 5G shows inhibition of PDX1-binding to Mafa with overexpression of Bhlhe40. This needs to be confirmed under hypoxic conditions.
   • b. Fig 4H and 4I show restoration of insulin secretion normalized to total protein with AAV-Mafa. This needs to be supplemented with insulin content as MAFA has been implicated in regulating insulin gene expression (PMID: 25500951).
   • c. qRT-PCR of exocytosis genes and ATP generation with hypoxia and AAV-Mafa.
   • d. Would mutation of A and C E-box sites restore PDX1 binding to Mafa TF region under hypoxia?
3. β-dedifferentiation has been proposed to be involved in loss of insulin secretion in T2D (PMID: 22980982, 16123366). One can speculate that transcriptional repression of Mafa by BHLHE40 is a component of a larger dedifferentiation phenomenon occurring under hypoxia, as other β-cell genes were decreased with hypoxia (Fig 1A) and Bhlhe40-OE in Fig 4A. Identifying differences in dedifferentiation and β-cell disallowed genes with Bhlhe40 overexpression (RNA seq, qRT-PCR) would therefore potentially reveal a dedifferentiation mechanism.
4. The authors identify Atf3 as another transcriptional repressor enriched under hypoxia although to a lesser degree than Bhlhe40. The role of ATF3 in hypoxia-induced apoptosis and adaptive UPR has been previously suggested (PMID: 20519332, 20349223). Additionally, hypoxia represses adaptive UPR in models of T2D and drives β-cell apoptosis (PMID: 27039902). The authors discuss the role of ATF3 under hypoxia in the discussion (lines 319-324) and addressing these research gaps regarding ATF3 function would be insightful.

Minor comments

1. In Fig 2E, increasing replicates would confirm no induction of Bhlhe40 with Thapsigargin.
2. In Fig 2B, BHLHE40 bands need to be quantified to show time-dependent increase in protein levels.
3. In Fig 3C, insulin content needs to be shown with Bhlhe40-OE as in Fig 3B with hypoxia.
4. In Fid 4E-F, band intensities need to quantified by densitometry to determine degree of downregulation of MAFA.
5. In Fig4H and 6G, insulin content needs to be shown as stated above.
6. In Supplemental Figure 3C, apoptosis induced by hypoxia was assessed by PI staining that detects late apoptosis. No significant changes were observed with Bhlhe40-KD, but additional cell death assessments can be used to confirm that B40 does not affect β-cell death.
7. It would be interesting to see the rates of diabetes incidence in Bhlhe40KO: ob/ob mice and if Bhlhe40 deficiency protects against or delays development of diabetes.
8. Knockdown efficiency shown in Supplementary figure 3A needs to be estimated by quantifying band intensities.
9. Line 43 should say "...reversed defects in insulin secretion."

Significance

The data presented provides novel mechanistic insights into the role of hypoxia in β-cell dysfunction. Studies in multiple models of type 2 diabetes (T2D) have shown the loss of signature β-cell genes including Ins1, Pdx1, Mafa, Slc2a2 as a result of excess nutrient stimulation and hypoxia; the precise causal mechanisms, however, still remain to be determined (PMID: 22980982, 28270834). A previous paper from the same group demonstrated downregulation of β-cell signature genes with hypoxia by a HIF1α independent mechanism (PMID: 25503986). Data presented in this report extend those observations and reveal a previously unappreciated role for transcriptional repressor BHLHE40 in the downregulation of a key β-cell gene Mafa. As the authors have identified additional transcriptional repressors including ATF3 and differentially expressed genes in both human and rodent β-cells, this paper would be of great value in understanding the effects of hypoxia. Moreover, studies in mouse models of T2D extend the association of BHLHE40 to clinical β-cell dysfunction and diabetes. My areas of interest are pancreatic β-cell and mitochondrial physiology. GSE analysis and repression of PGC1α by BHLHE40, as appropriately discussed by the authors, point towards impaired mitochondrial function and ATP generation. Additional experiments would greatly support the role of BHLHE40 in mitochondrial dysfunction under hypoxia (as discussed under comments).

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Reply to the reviewers

Manuscript number: RC-2022-01594

Corresponding authors: Hidehiko Kawai and Hiroyuki Kamiya

1. General Statements [optional]

We would like to extend our gratitude to the Editor and both Reviewers for their constructive and insightful comments to our manuscript. We deeply appreciate the Reviewers’ careful consideration of our work, in result of which we think the paper has greatly improved. Below, we have responded to all points raised by the Reviewers.

2. Point-by-point description of the revisions

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

The analysis of mutations in mammalian, including human, genomes has been of interest for many decades. Early DNA sequencing technologies enabled direct identification of mutations in target genes provided that the mutant genes could be readily isolated. This requirement stimulated the development of shuttle vector plasmids that carried a mutation marker gene and could replicate in both mammalian and bacterial cells. These were used in experiments in which the plasmids, treated with a mutagen, would be passaged through mammalian host cells after which the progeny plasmids were introduced into an indicator bacterial strain. Colonies with mutant marker genes could be distinguished by color or survival, the plasmids recovered, and the sequence of the mutant gene determined. The shuttle vector plasmid that became the most widely used contained as the marker the supF amber suppressor tyrosyl tRNA gene positioned in the plasmid such that deletion mutations associated with mammalian cell transfection were selected against. Although various improvements have been introduced since its introduction in the mid-1980s, including bar codes to distinguish independent from sibling mutations (in the early 1990s), the basics of the system have been maintained, and it and variations are still in use. The Kamiya group has made several adjustments to the supF shuttle vectors, including the construction of indicator bacterial strains based on survival of bacteria containing mutant supF genes (the initial system relied on colony color). They have published many studies of mutagenesis by various agents, error prone polymerases, etc. In the current submission they describe a comprehensive approach to identifying mutations in the supF gene that exploits Next Generation Sequencing technology that can identify the full spectrum of mutations including those that escape detection in phenotypic screens. The study is exhaustive and presents a methodical validation of each component of their approach. They report UV induced mutations, the mechanism of which has been well characterized in previous literature. They also describe a category of multiple mutations, which had been observed in the early work with the supF plasmids, and whose relationship to UV photoproducts is most likely indirect.

*We thank the Reviewer for their very insightful feedback to our manuscript and their positive assessment. We have added some discussion points based on the essential references mentioned in the Reviewer’s comments, which we believe made the explanation of our study more complete. *

Major comments: This manuscript presents a technical advance on the use of the supF mutation reporter system. The extent of the validation of each component of the system, including the bar code is rigorous. Their data on the nature and location of UV induced mutations are in very good agreement with previous studies with supF and other reporter genes, a further validation of their approach. Their discussion of the mechanism of the UV induced mutations is in accord with prior work from other laboratories. However, their interpretation of the multiple mutations, although reasonable in invoking a role for APOBEC deamination of cytosines (see eLife. 2014; 3: e02001 for another discussion of this issue), overlooks a much earlier study on the same topic that showed that nicks in the vicinity of the marker gene are mutagenic and can induce multiple mutations (Proc Natl Acad Sci 1987 84:4944-8). It would be useful for the authors to consider their data on the multiple mutations in the light of the earlier analysis. Furthermore, a check to verify the covalently closed circular integrity of the plasmid preparations would be an important quality control and could reduce the mutagenesis observed in 0 UV controls.

We thank the Reviewer for the valuable comments that made our manuscript clearer and more emphatic. We are hereby addressing all of the Reviewer’s concerns. The available data accumulated from previous studies have proved the high sensitivity of the supF assay as a mutagenesis assay, which now has been clearly supported by the results in the current study. We believe that this NGS assay will be able to fulfil the data requirements to tackle many questions related to mutagenesis, thanks to the simplicity and cost-effectiveness of the procedure. However, to meet the experimental objectives, the preparation and analysis of the library are crucially important procedures in the stages of initial setting up of the assay. The covalently closed circular integrity of the vector library is definitely one of the important points we should pay attention to when performing this assay. After the construction of the BC12-library, we have to check the quality of the library by agarose gel electrophoresis. The background mutation frequency and the sequence of the library itself (uploaded as described in the DATA AVAILABILITY section of this manuscript) also needs to be analyzed by NGS before the experiment. We are also routinely constructing the double-stranded shuttle vector from a single-stranded circular DNA with a variety of site-specific damaged oligonucleotides. The treatment with T5 exonuclease followed by purification is absolutely essential to decrease the background mutation frequency. Without the treatment with the exonuclease, cluster mutations may be increased under specific experimental conditions. For this study, we carried out the conventional supF assay using the BC12-library purified after T5 exonuclease treatment. However, in this case the process of purification slightly increased the mutant frequency of the BC12-library to about 2 x10-4 (corresponding to 1x10-6/bp).Therefore, when setting up the essay, we have to consider the background control that we will need for the data analysis. In response to the Reviewer’s comments, we have now added the following paragraph in the DISCUSSION section:

Page 16, line 25:

”5) For the supF assay, spontaneous cluster mutations at TC:GA sites were often observed, and it was well illustrated in an earlier study that a nick in the shuttle vector was a trigger for these asymmetric cluster mutations (54). Therefore, we need to be aware of the quality of each library and how it affects the outcome of each analysis, especially for detection of very low levels of mutations. Depending on the purpose of the experiments, in the preparation of covalently closed circular vector libraries it is essential to eliminate the background level of mutations. In fact, the in vitro construction of the library of double-stranded shuttle vectors from single-stranded circular DNA requires the process of treatment with T5 Exonuclease, which drastically decreases background mutations.”

Minor points The authors state that only 30% of the base sequence of the supF gene can be "used for dual-antibiotic selection on the indicator E. coli". An earlier review (Mutation Res 220: 61,1989) indicated that within the mature tRNA region single or tandem mutations had been reported at 87% of sites, using the colony color assay. The direct NGS analyses would be indifferent to phenotype, and one would expect the maximum number of mutable sites would be recovered from this approach. It would be helpful for an explicit statement regarding the number of mutant sites to be in the Discussion, as this should strengthen the case for the NGS strategy.

We thank the Reviewer for the helpful comment. These are important points we should indeed mention. This method will complement previous data, and especially the data from titer plates will provide us with non-biased mutation spectra for the whole analyzed region. We have now explained in detail about the coverage of mutation spectra in the DISSCUSSION section.

Page 14, line 14:

“The mutation spectra of single or tandem base-substitutions for inactive supF genes identified by using the blue-white colony color assays were comprehensively summarized in an earlier review article, and it was noted that the mutations were detected at 86 sites within a 158-bp region covering the supF gene (54%) and at 74 sites within the 85-bp mature tRNA region (87%), thus demonstrating the great sensitivity of the supF assay system for analysis of mutation spectra (19). However, obtaining reliable datasets by the conventional supF assay requires skill and experience, especially for studies where the mutations of interest are induced with low frequency. The method has been advanced by the construction of indicator bacterial strains with different supF reporter genes which allow selection based on survival of bacteria containing mutant supF genes. However, the fact that the supF phenotypic selection process relies on the structure and function of transfer RNAs that may be differently affected by different mutations means that the improvement of the efficiency of the selection process may cause loss of coverage of the mutation spectra, as it is under our experimental conditions, where the coverage is about 30% (19,20).”

Page 15, line 4:

“From this point of view, we believe that we can secure a sufficient number of experiments to improve the accuracy of the analysis and to confirm the reproducibility of the experiments. Furthermore, the data from colonies grown on titer plates provides us, at least in principle, and with the exception of large deletions and insertions, with non-biased mutation spectra for the whole analyzed region.

Supplementary Figure 1 shows the organization of 8 supF reporter plasmids. Were these discussed in the text and employed in the experiments? It was not clear in the text.

We thank the Reviewer for the helpful comment. It was indeed not clear which vectors we used and why we constructed a series of vectors. Now, we have added the vectors we used for the constructions of the library and each experiment in the RESULTS and MATERIALS AND METHODS sections. Since this is quite important for us and, we believe, the readers, we also added the explanations in the DISCUSSION section, detailing why we have constructed a series of shuttle vectors, as follows:

Page 19, line 36:

“Mutational signatures identified in cancer cells are emerging as valuable markers for cancer diagnosis and therapeutics. Innumerable physical, chemical and biological mutagens, including anticancer drugs, induce characteristic mutations in genomic DNA via specific mutagenic processes. The mutation spectra obtained here by using the presented advanced method were in good agreement with accumulated data from previous papers where the conventional method had been used, with the advantage that our method provided less-biased mutation spectra data. As described above, the datasets presented here highlighted novel mutational signatures and also cluster mutations with a strand-bias, which could be associated with the processes of replication, transcription, or repair of DNA-damage, including a single strand break (a nick). In this study, eight series of supF shuttle vector plasmids were constructed, as presented in Supplementary Figure S1; however, the analysis was carried out using N12-BC libraries prepared from either pNGS2-K1 (Figures 1-4) or pNGS2-K3 (Figures 5-10). The pNGS2-K1/-A1/-K4/-A4 and pNGS2-K2/-A2/-K3/-A3 vector series contain an M13 intergenic region with opposite orientations relative to the supF gene, which allows us to incorporate specific types of DNA-damage at specific sites in the opposite strand of the vector library. Also, the pNGS2-K1/-A1/-K3/-A3 and pNGS2-K2/-A2/-K4/-A4 vector series contain the SV40 replication origin, which enables bidirectional replication and transcription, at opposite sides of the supF gene. Although this is still preliminary data, it is notable that the spontaneously induced mutations for the different vectors in U2OS cells were not significantly different. Therefore, the here presented mutagenesis assay with NGS, by using these series of libraries, can be applied in many different types of experiments to address both quantitative and qualitative features of mutagenesis. It is possible to design series of libraries containing DNA lesions or sequences suitable for the investigation of specific molecular mechanisms, such as TLS, template switching, and asymmetric cluster mutations.”

CROSS-CONSULTATION COMMENTS Comment on the issue raised by Reviewer #2 regarding plasmids with unrepaired DNA damage introduced into E. coli after passage through U2OS cells: treatment of the plasmid harvest with Dpn1 eliminates un-replicated plasmid DNA. Also, SV40 T antigen drives run away replication of the plasmids, which contain the SV40 origin of replication. This greatly dilutes plasmids with remaining UV photoproducts.

Reviewer #1 (Significance (Required)):

Significance This is a comprehensive description of a technical advance for the analysis of mutations based on the most widely used system for reporting mutations in mammalian, including human, cells. As costs for NGS decline it is likely to become the approach of choice.

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

In this manuscript, the authors developed a novel mutagenesis assay by combining the conventional supF forward mutagenesis assay with NGS technology. The manuscript is well written, providing design, methods, and results of the experimental system in very much details, which this reviewer highly evaluates. However, the manuscript may be too long and could be more concise. In addition, this reviewer is afraid that main figures seem difficult to fit printed pages (especially multi-paneled figures of large size, such as Fig. 5 through 8). The authors should re-organize the figures by reducing size and/or moving partly to supplementary information.

We thank the Reviewer for the helpful comments to our manuscript. It is true that the multi-paneled figures were too large, and we have now re-analyzed and optimized most of the figures by reducing size, transferring to Supplementary Figures, and separating one figure into two. Although the number of Figures and Supplementary Figures have now increased, we believe that it has become easy to follow for readers and to fit printed pages. *We considered carefully the Reviewer’s remark about the length of the manuscript, but we feel that the text was already as concise as we could make it, and we have already left out some more detailed explanations. *

1. Some UV-induced DNA damage (typically CPD) is repaired only slowly in human cells, so that the replicated plasmid DNAs recovered from U2OS cells may still contain damage and possibly induce mutations in E. coli after transfection. As the result of high sensitivity of NGS analysis, it is worried that such mutations could be also included in the results. To obtain even more accurate mutational characteristics in mammalian cells, the authors could consider to treat the DNA samples with photolyases before transformation of E. coli. The authors could consider to discuss on this point.

*We thank the Reviewer for the helpful comment, indeed Dpn I treatment is one of the very important procedures for avoiding analysis bias. We have now expanded the explanation why the libraries have to be treated with Dpn I, as follows: *

Page 11, line 4:

“the libraries were extracted from the cells, and treated with dam-GmATC-methylated DNA specific restriction enzyme Dpn I to digest un-replicated DNAs that contain UV-photoproducts.”

1. It is quite intriguing that multiple mutations in a single BC clone tend to occur in the same DNA strand. Is there any trend in a distance between the mutated sites? Considering participation of TLS polymerases in the first round of replication, it may be interesting if multiple DNA lesions occur in relatively close positions so that TLS polymerases elongate the DNA strand without switching back to replicative polymerases.

We thank the Reviewer for the valuable and insightful suggestions for this assay. We have analyzed the positions of SNSs in multiple-mutations shown in Supplementary Figures S11 and S12. As the reviewer mentioned, we may be able to address the mechanisms of TLS switching in mammalian cells by using this assay. In this study, the obtained non-biased mutation spectra of multiple mutations may not be enough for the static analysis, but our results indicate that multiple mutations were induced at relatively close positions. It would be interesting if we could address the mechanisms of TLS polymerase switching. We believe that the accumulation of large numbers of non-biased mutation spectra will provide us with growing opportunities to address more questions in mutagenesis. We have now added the Supplementary Figures S11 and S12, as well as the following discussion points:

Page 14, line 6:

“5) The distance between two SNSs in multiple mutations induced by UV irradiation was relatively shorter than the theoretically expected based on the sequence (Supplementary Figures S11 and S12).”

Page 18, line 27:

“In addition, the positions of SNSs in the multiple mutations were closer to each other compared to the theoretically expected positions (Supplementary Figures S11 and S12), which may reflect switching events involving TLS polymerases. It should be noted that the presented data for the distance between two SNSs in the multiple mutations was analyzed from the data from selection plates in order to secure a sufficient number of mutations, and therefore, there may be a bias due to hot spots associated with the selection process. However, the results from the limited number of mutations from the titer plates are similar to these from the selection plates. It can be proposed that this assay may also be applied for analysis of TLS polymerases in mammalian cells.”

1. This reviewer is wondering whether the results of mammalian cells are influenced by transcription-coupled repair in this experimental system. Because the SV40 replication origin functions as bidirectional promoters, the supF region may be transcribed in U2OS cells so that DNA damage on transcribed strands may be removed more efficiently than non-transcribed strands. Please comment on this, if relevant.

*We thank the Reviewer for the insightful comments. This issue is also very important and interesting, and should be addressed in the mutagenesis research. That is exactly the reason why we presented series of vectors for the assay in this paper. The SV40 replication origin has an effect on the background mutations, which this is also dependent on the experimental conditions. However, this needs to be confirmed by further studies. We hope the idea for these constructions will be helpful for many laboratories. We have now added the following parts in the DISCUSSION section. *

Page 18, line 36:

“Mutational signatures identified in cancer cells are emerging as valuable markers for cancer diagnosis and therapeutics. Innumerable physical, chemical and biological mutagens, including anticancer drugs, induce characteristic mutations in genomic DNA via specific mutagenic processes. The mutation spectra obtained here by using the presented advanced method were in good agreement with accumulated data from previous papers where the conventional method had been used, with the advantage that our method provided less-biased mutation spectra data. As described above, the datasets presented here highlighted novel mutational signatures and also cluster mutations with a strand-bias, which could be associated with the processes of replication, transcription, or repair of DNA-damage, including a single strand break (a nick). In this study, eight series of supF shuttle vector plasmids were constructed, as presented in Supplementary Figure S1; however, the analysis was carried out using N12-BC libraries prepared from either pNGS2-K1 (Figures 1-4) or pNGS2-K3 (Figures 5-10). The pNGS2-K1/-A1/-K4/-A4 and pNGS2-K2/-A2/-K3/-A3 vector series contain an M13 intergenic region with opposite orientations relative to the supF gene, which allows us to incorporate specific types of DNA-damage at specific sites in the opposite strand of the vector library. Also, the pNGS2-K1/-A1/-K3/-A3 and pNGS2-K2/-A2/-K4/-A4 vector series contain the SV40 replication origin, which enables bidirectional replication and transcription, at opposite sides of the supF gene. Although this is still preliminary data, it is notable that the spontaneously induced mutations for the different vectors in U2OS cells were not significantly different. Therefore, the here presented mutagenesis assay with NGS, by using these series of libraries, can be applied in many different types of experiments to address both quantitative and qualitative features of mutagenesis. It is possible to design series of libraries containing DNA lesions or sequences suitable for the investigation of specific molecular mechanisms, such as TLS, template switching, and asymmetric cluster mutations.”

1. page 13: Please check whether the description of Fig. 9C is correct (6th line, graph on top; 9th line, bottom graph).

We thank the Reviewer for carefully checking our manuscript, it was mislabeled in the text. Now, following the Reviewer’s comments, most figures have been changed from the figures in the previous submission. We appreciate the careful review.

CROSS-CONSULTATION COMMENTS Reviewer #1 gives quite relevant comments as an expert of the mutagenesis field. It would improve this manuscript greatly for the authors to make appropriate modifications according to his/her suggestions.

Reviewer #2 (Significance (Required)):

It is quite convincing that this method has a great potential to give much more extensive information on mutational characteristics, most importantly, by eliminating the bias caused by phenotypic selection. Therefore, this work certainly must be worth being published in an appropriate journal.

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

In this manuscript, the authors developed a novel mutagenesis assay by combining the conventional supF forward mutagenesis assay with NGS technology. The manuscript is well written, providing design, methods, and results of the experimental system in very much details, which this reviewer highly evaluates. However, the manuscript may be too long and could be more concise. In addition, this reviewer is afraid that main figures seem difficult to fit printed pages (especially multi-paneled figures of large size, such as Fig. 5 through 8). The authors should re-organize the figures by reducing size and/or moving partly to supplementary information.

Specific comments

1. Some UV-induced DNA damage (typically CPD) is repaired only slowly in human cells, so that the replicated plasmid DNAs recovered from U2OS cells may still contain damage and possibly induce mutations in E. coli after transfection. As the result of high sensitivity of NGS analysis, it is worried that such mutations could be also included in the results. To obtain even more accurate mutational characteristics in mammalian cells, the authors could consider to treat the DNA samples with photolyases before transformation of E. coli. The authors could consider to discuss on this point.

2. It is quite intriguing that multiple mutations in a single BC clone tend to occur in the same DNA strand. Is there any trend in a distance between the mutated sites? Considering participation of TLS polymerases in the first round of replication, it may be interesting if multiple DNA lesions occur in relatively close positions so that TLS polymerases elongate the DNA strand without switching back to replicative polymerases.

3. This reviewer is wondering whether the results of mammalian cells are influenced by transcription-coupled repair in this experimental system. Because the SV40 replication origin functions as bidirectional promoters, the supF region may be transcribed in U2OS cells so that DNA damage on transcribed strands may be removed more efficiently than non-transcribed strands. Please comment on this, if relevant.

4. page 13: Please check whether the description of Fig. 9C is correct (6th line, graph on top; 9th line, bottom graph).

CROSS-CONSULTATION COMMENTS

Reviewer #1 gives quite relevant comments as an expert of the mutagenesis field. It would improve this manuscript greatly for the authors to make appropriate modifications according to his/her suggestions.

Significance

It is quite convincing that this method has a great potential to give much more extensive information on mutational characteristics, most importantly, by eliminating the bias caused by phenotypic selection. Therefore, this work certainly must be worth being published in an appropriate journal.

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

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The analysis of mutations in mammalian, including human, genomes has been of interest for many decades. Early DNA sequencing technologies enabled direct identification of mutations in target genes provided that the mutant genes could be readily isolated. This requirement stimulated the development of shuttle vector plasmids that carried a mutation marker gene and could replicate in both mammalian and bacterial cells. These were used in experiments in which the plasmids, treated with a mutagen, would be passaged through mammalian host cells after which the progeny plasmids were introduced into an indicator bacterial strain. Colonies with mutant marker genes could be distinguished by color or survival, the plasmids recovered, and the sequence of the mutant gene determined. The shuttle vector plasmid that became the most widely used contained as the marker the supF amber suppressor tyrosyl tRNA gene positioned in the plasmid such that deletion mutations associated with mammalian cell transfection were selected against. Although various improvements have been introduced since its introduction in the mid-1980s, including bar codes to distinguish independent from sibling mutations (in the early 1990s), the basics of the system have been maintained, and it and variations are still in use.

The Kamiya group has made several adjustments to the supF shuttle vectors, including the construction of indicator bacterial strains based on survival of bacteria containing mutant supF genes (the initial system relied on colony color). They have published many studies of mutagenesis by various agents, error prone polymerases, etc. In the current submission they describe a comprehensive approach to identifying mutations in the supF gene that exploits Next Generation Sequencing technology that can identify the full spectrum of mutations including those that escape detection in phenotypic screens. The study is exhaustive and presents a methodical validation of each component of their approach. They report UV induced mutations, the mechanism of which has been well characterized in previous literature. They also describe a category of multiple mutations, which had been observed in the early work with the supF plasmids, and whose relationship to UV photoproducts is most likely indirect.

Major comments:

This manuscript presents a technical advance on the use of the supF mutation reporter system. The extent of the validation of each component of the system, including the bar code is rigorous. Their data on the nature and location of UV induced mutations are in very good agreement with previous studies with supF and other reporter genes, a further validation of their approach. Their discussion of the mechanism of the UV induced mutations is in accord with prior work from other laboratories. However, their interpretation of the multiple mutations, although reasonable in invoking a role for APOBEC deamination of cytosines (see eLife. 2014; 3: e02001 for another discussion of this issue), overlooks a much earlier study on the same topic that showed that nicks in the vicinity of the marker gene are mutagenic and can induce multiple mutations (Proc Natl Acad Sci 1987 84:4944-8). It would be useful for the authors to consider their data on the multiple mutations in the light of the earlier analysis. Furthermore, a check to verify the covalently closed circular integrity of the plasmid preparations would be an important quality control and could reduce the mutagenesis observed in 0 UV controls.

Minor points:

The authors state that only 30% of the base sequence of the supF gene can be "used for dual-antibiotic selection on the indicator E. coli". An earlier review (Mutation Res 220: 61,1989) indicated that within the mature tRNA region single or tandem mutations had been reported at 87% of sites, using the colony color assay. The direct NGS analyses would be indifferent to phenotype, and one would expect the maximum number of mutable sites would be recovered from this approach. It would be helpful for an explicit statement regarding the number of mutant sites to be in the Discussion, as this should strengthen the case for the NGS strategy. <br /> Supplementary Figure 1 shows the organization of 8 supF reporter plasmids. Were these discussed in the text and employed in the experiments? It was not clear in the text.

CROSS-CONSULTATION COMMENTS

Comment on the issue raised by Reviewer #2 regarding plasmids with unrepaired DNA damage introduced into E. coli after passage through U2OS cells: treatment of the plasmid harvest with Dpn1 eliminates un-replicated plasmid DNA. Also, SV40 T antigen drives run away replication of the plasmids, which contain the SV40 origin of replication. This greatly dilutes plasmids with remaining UV photoproducts.

Significance

Significance:

This is a comprehensive description of a technical advance for the analysis of mutations based on the most widely used system for reporting mutations in mammalian, including human, cells. As costs for NGS decline it is likely to become the approach of choice.

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

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Reply to the reviewers

Reviewer #1:

Review of "Identifying novel regulators of placental development using time series transcriptomic data and network analyses."

The authors present a detailed bioinformatic assessment of mouse developmental time series of the placenta. They apply current data mining and analysis methods to identify protein-centred networks that are likely enriched to specific cell types of the placenta. They then translate these findings to humans using statistical comparisons of human single-cell sequencing data of the placenta. Lastly, they use knock-down experiments to validate the conserved functional importance of the hub genes in the mouse protein networks in human cells.

The strengths of this paper are the rigorous data mining methods and the functional translation to humans from mice. There are no critical weaknesses to the article. There is a blend of statistical analysis with anecdotal or hand curation from databases and the literature, but it is unclear if these curated finings are circumstantial or statistically meaningful. In the end, the hypothesis seems to hold in that 4/4 gene knocked down in the human cells gave a migration phenotype.

Comments, questions, critique:

1. Given the translational aims of the paper, more introduction/discussion material on the comparative aspects of mice and humans are needed. Are giant cells and EVT the same? What are the cell equivalents that you are discovering? The Soncin et al. paper is cited, but I think underused. This publication contains time series data on mice and humans and could be used as external validation of clusters, networks, and other analyses. Other publications to consider for context are

2. Cox B, et al. Mol Syst Biol 5: 279.

3. Silva JF, Serakides R. 2016. Cell Adhes Migr 10: 88-110. (specifically discusses migration difference between the species placentae)

We thank the reviewer for the comment and valuable resources. We agree that more information about the similarities and differences between the migratory cells needs to be provided. We have added the following details in the introduction of the manuscript:

“Although there are certain differences between the mouse and human placenta (Hemberger, Hanna, and Dean 2020; Soncin, Natale, and Parast 2015), they do express common genes during gestation, including common regulators and signaling pathways involved in placental development (Cox et al. 2009; Soncin et al. 2018; Soncin, Natale, and Parast 2015; Watson and Cross 2005). For example, Ascl2/ASCL2 and Tfap2c/TFAP2C are required for the trophoblast (TB) cell lineage in both mouse and human models (Guillemot et al. 1994; Kuckenberg, Kubaczka, and Schorle 2012; Varberg et al. 2021). Another example is the HIF signaling pathway, which regulates TB differentiation in both mouse and human placenta (Soncin, Natale, and Parast 2015).”

“Although the structure of the placenta is not identical between mouse and human, certain mouse placental cell types are thought to be equivalent to human placental cell types (Soncin, Natale, and Parast 2015). For example, parietal TGCs and glycogen TBs have been described as equivalent to human extravillous trophoblasts (EVTs) (Soncin, Natale, and Parast 2015). Mouse TGCs are not as invasive as human EVTs (Soncin, Natale, and Parast 2015), and they have different levels of polyploidy and copy number variation (Morey et al. 2021); however, both EVTs and TGCs are able to degrade extracellular matrix to enable TB migration into the decidua (Silva and Serakides 2016).”

Added to discussion:

“These genes were selected primarily based on the network analyses, but also based on expression data from human cells to account for possible differences between mouse and human placental gene expression.”

As the reviewer suggested, we used the Soncin et al., 2015 data for validation. Only 6,317 of the 11,713 protein-coding genes used for hierarchical clustering were detected in the mouse dataset in Soncin et al., 2015. This issue could be because the Soncin data was generated using microarrays.

Nevertheless, we still compared our e7.5 and e9.5 hierarchical groups with: (1) Soncin et al. gene clusters in mouse that were downregulated over time, had highest expression from e9.5-12.5, or were upregulated over time; and (2) Soncin et al. gene clusters in human that were best correlated with mouse clusters and were either downregulated over time or upregulated over time. We observed a general consensus that our e7.5-hierarchical group had the highest percent of agreement with Soncin et al. gene groups that are downregulated over time, and our e9.5-hierarchical group had the highest percent of agreement with Soncin et al. gene groups that either have highest expression at e9.5-e12.5 or genes that are upregulated over time. This data is added below, described in the results section 1, and included in Supplementary Table S1.

Comparison with Soncin et al. mouse data:

Having expression > 0 (in Soncin et al.) and being in any hierarchical clusters

E7.5-hierarchical genes (down-regulation trend)

E9.5-hierarchical genes (up-regulation trend)

Cluster 2, 3 and 7 (Soncin et al., downregulation trend)

1009

800 (79.3%)

279 (27.7%)

Cluster 6 (Soncin et al., highest at e9.5 – e12.5)

120

51 (42.5%)

110 (91.7%)

Cluster 1, 4 and 5 (Soncin et al., upregulation trend)

1019

415 (40.7%)

881 (86.5%)

Comparison with Soncin et al. human data:

Having expression > 0 (in Soncin et al.) and being in any hierarchical clusters

E7.5-hierarchical genes (down-regulation trend)

E9.5-hierarchical genes (up-regulation trend)

HS Cluster 5 (Soncin et al., downregulation trend)

164

92 (56.1%)

52 (31.7%)

HS Cluster 2 and 4 (Soncin et al., upregulation trend)

111

44 (39.6%)

72 (64.9%)

The following statement was added to the result section:

“Second, we compared our hierarchical groups with previously published mouse and human placental microarray time course data from Soncin et al., 2015 (Soncin, Natale, and Parast 2015). Despite the technical differences between the datasets, we observed a consensus that our e7.5 hierarchical cluster had the highest percent of overlap with Soncin et al. gene groups that are downregulated over time, and our e9.5 hierarchical cluster had the highest percent of overlap with Soncin et al. gene groups that either have highest expression at e9.5 - e12.5 or genes that are upregulated over time (Supplementary Table S1).”

Clustering represented in Figure 1B, was this a supervised model? Why only three clusters?) Did you specify that there would be three models and force each gene profile into one of the categories? How robust are the fits? A fitted model might be a better approach as you can specify the ideal models (early high, late high and mid-high), then determine each gene profile that fits each model and only assess those genes with a significant fit to the model. Forcing clustering to the three-model fit likely gives many poorly fitting profiles. While in the end, this works out, it may be due to applying other post hoc methods for gene enrichment, where noise distributes randomly.

We carried out unsupervised transcript clustering using hierarchical clustering (agglomerative approach using Euclidean distance and complete linkage). The resulting dendrogram was cut at the second highest level to obtain three clusters. We have added additional validation with different numbers of clusters (k = 3, 4 and 5) and quantification of agreement between different clustering methods to show the robustness of the hierarchical clusters. We acknowledge that hierarchical clustering could be sensitive to noise and could result in poorly fitted transcripts in each group; however, it was a necessary first step for us to identify genes relevant to the distinct placental processes at the three timepoints. Acknowledging this disadvantage, we only focused the analyses on genes that are differentially expressed over time and were present in the timepoint hierarchical groups.

We added the additional analysis as Supplementary Figure S1, and the following statements were added in the results section:

"First, we used three different algorithms, K-means clustering, self-organizing maps, and spectral clustering, to validate the trends of the expression levels in hierarchical groups, as well as the number of transcript groups (k = 3, 4 and 5). Only with k = 3 did we obtain groups with median expression level trends consistent in all four algorithms (Supplementary Figure S1). Moreover, with k = 3, the maximum percent of agreement (see Materials and Methods) between hierarchical clusters and clusters obtained using each of the different algorithms was 70.34-87.26% (Supplementary Figure S1), while the maximum percent of agreement between hierarchical clusters and clusters obtained from other algorithms decreases to between 55.67-65.72% with k = 4 and 54.81-59.19% with k = 5.”

We agree model-based clustering could be an alternative approach and have added it to the discussion section:

“Combining hierarchical clustering with differential expression analysis, we were able to identify gene groups using an unsupervised approach. It has also been shown that for times-series analyses with fewer than eight timepoints, pairwise differential expression analysis combined with additional methods identifies a more robust set of genes (Spies et al. 2019). Alternatively, model-based clustering using RNA-seq profiles (Si et al. 2014) could also be useful for gene group identification. However, it is still important to evaluate the robustness and functional relevance of the fitted models by carrying out additional downstream analyses.”

Several statements are made about the conservation of importance between mouse and human hub genes. For example, "We predict these highly expressed genes to be generally important for TB function and processes such as cell migration, a term associated with multiple timepoint specific networks (Figure 2A)." While your knock-down assay of migration results shows these hub genes to be necessary to humans, what do they mean to the mouse? You did not use mouse TSC to assess functional importance concurrently. You note a small number of genes as of known importance, "127 hub genes of which 16 have been annotated as having a role in placental development". Were the others knocked out but lack a developmental phenotype or not assessed? Are these functionally redundant in the mouse or not involved in the same processes between the species?

To assess the possible role of hub genes in mouse development more comprehensively, we extended our search for gene functions on the Mouse Genome Informatics (MGI) database to include not only placenta related GO and MGI phenotype terms (defined as “genes with known roles”), but also embryo related GO and MGI phenotype terms (defined as “genes with possible roles”). We included embryo related terms as “genes with possible roles” because embryonic lethal mouse knockout lines frequently have placentation defects, and because defects in placental development can be associated with the development of other embryonic tissues (Brown and Hay 2016; Perez-Garcia et al. 2018; Woods, Perez-garcia, and Hemberger 2018). This change resulted in an increase in the number of genes with relevant functions in mouse, including several annotated as embryonic lethal or with abnormal embryonic growth (see Supplementary Table S6). With the additional annotations:

• 6 out of 17 hub genes of e7.5 networks have known/possible roles.
• 17 out of 28 hub genes of e8.5 networks have known/possible roles.
• 48 out of 127 hub genes of e9.5 networks have known/possible roles. We also carried out randomization tests to determine if the number of known/possible genes we identified were significant. Randomization tests were carried out with the following procedure: for each timepoint, from the respective timepoint-specific groups, we sampled 10,000 gene sets of the same number as the hub gene numbers. Then we counted the number of known/possible genes in each random set. A p-value is calculated as the number of times a random gene set has ≥ known/possible genes than the observed number, divided by 10,000. We found that the number of genes with known/possible roles at each time point are statistically significant (Supplementary Figure S3). This result indicates that the gene sets we identified are significantly associated with relevant phenotypes in mouse.

The remaining hub genes are unannotated as related to placental or embryonic functions in the MGI database. Based on that, it is difficult to determine if they lack a relevant phenotype, or if there has not been a detailed assessment of the placenta.

Added to section 2 of the result section:

“Briefly, genes annotated under any GO or MGI phenotype terms related to placenta, TB cells, TE and the chorion layer are considered as having a “known” role in the placenta. Genes annotated under terms related to embryo are considered as having a “possible” role in the placenta, because embryonic lethal mouse knockout lines frequently have placentation defects, and because defects in placental development can be associated with the development of other embryonic tissues (Brown and Hay 2016; Perez-Garcia et al. 2018; Woods, Perez-garcia, and Hemberger 2018). Hereafter, such genes are referred to as “known/possible genes”. In the e7.5 networks, there were 17 hub genes in which six genes were known/possible. The number of hub genes that are labelled as known/possible is statistically significant when comparing to random gene sets selected from the e7.5 timepoint-specific group (Supplementary Figure S3). In the e8.5 and e9.5 networks, 17 out of 28 and 48 out of 127 hub genes were known/possible, respectively. Similar to e7.5, the number of hub genes labelled as known/possible in e8.5 networks and e9.5 networks were both statistically significant when comparing to random gene sets selected from the corresponding timepoint-specific groups (Supplementary Figure S3). These results indicate that the gene sets we identified are significantly associated with relevant phenotypes in the mouse.”

For the four genes that we tested in HTR-8/SVneo cells, we also added more information about the current known role of the gene in mouse.

Added to the discussion section:

“We identified hub genes and their immediate neighboring genes which could regulate placental development and confirmed the roles of four novel genes (Mtdh, Siah2, Hnrnpk and Ncor2) in regulating cell migration in the HTR-8/SVneo cell line. These genes were selected primarily based on the network analyses, but also based on expression data from human cells to account for possible differences between mouse and human placental gene expression. Previous studies suggested these four candidates are functionally important in mouse. Mtdh has been suggested to regulate cell proliferation in mouse fetal development (Jeon et al. 2010). The Siah gene family is important for several functions (Qi et al. 2013). Of relevance to the placenta, Siah2 is an important regulator of HIF1α during hypoxia both in vitro and in vivo (Qi et al. 2008). Moreover, while Siah2 null mice exhibited normal phenotypes, combined knockouts of Siah2 and Siah1a showed enhanced lethality rates, suggesting the two genes have overlapping modulating roles (Frew et al. 2003). Hnrnpk-/- mice were embryonic lethal, and Hnrnpk+/- mice had dysfunctions in neonatal survival and development (Gallardo et al. 2015) . Ncor2-/- mice were embryonic lethal before e16.5 due to heart defects (Jepsen et al. 2007). According to the International Mouse Phenotyping Consortium database (Dickinson et al. 2016), Ncor2 null mice also showed abnormal placental morphology at e15.5. However, none of these genes have been studied in TB migration function.”

In determining conservation between mouse and human networks, were only 1:1 orthologs examined or did you consider more complex 1:many mapping conditions between the two species?

In this work, we used only one-to-one orthology between mouse and human avoid duplication while sampling in the enrichment tests. We added this detail in the method section. However, as found in Cox et al., 2009, genes with one-to-many orthologs could be highly intriguing and should be investigated in future studies.

Should the migration assay be normalized to survival/adhesion? If 70,000 cells were seeded but had 50% cell death (or reduced adhesion), then it may appear to be poor migration. Should the migration be evaluated as a ratio of top to bottom cell densities to control for poor adhesion or survival?

We thank the reviewer for bringing up this important point. Unfortunately, with the method we used we cannot quantify the densities on top, because the cells on top need to be scraped off prior to measuring the cells at the bottom (the two densities cannot be measured separately). To help with this concern, in a separate experiment we instead counted cell numbers 48-hours post-transfection for cells treated with target gene siRNA and cells treated with negative control siRNA to determine if apoptosis or changes in proliferation rate could be leading to changes in the observed migration. From this data, we determined that none of the siRNA knockdowns resulted in a significant change of cell counts (p-value > 0.05). We do note that Siah2 siRNA #1 has some decrease in counts (p-value = 0.081) and Ncor2 siRNA #1 and #2 have some increase in cell counts (p-value = 0.081 and p-value = 0.077) (Supplementary Figure S7). Additional follow up experiments we have performed with our targets of interest, which are out of the scope of this paper, demonstrate that different pathways and processes could be involved in the resulting decrease in migration we observed (we are following up experimentally in more detail for each gene). Proliferation and other assays could also be used to further examine the increase in Ncor2 cell counts that were observed. We have added the cell count results and additional text to the discussion.

Added to results, section 4:

“When comparing the number of cells 48 hours post-transfection for cells treated with target gene siRNA to cells treated with negative control siRNA, we determined that none of the target gene siRNA treatments resulted in significant changes in cell counts. We do note that Siah2 siRNA #1 has some decrease in cell counts (p-value = 0.081), and Ncor2 siRNA #1 and Ncor2 siRNA #2 have some increase in cell counts (p-value = 0.081 and p-value = 0.077) compared to negative control treated samples (Supplementary Figure S7). This provides evidence that, in general, the reduction in cell migration capacity was likely not due to the target gene impacting the rate of cell death.”

To the discussion:

“Moreover, we observed that cell counts generally were not decreased upon target gene knockdown compared to negative control knockdown. However, more detailed analysis and process specific assays are needed. For example, future studies assessing each gene’s role in cell adhesion, cell-cell fusion, cell proliferation and cell apoptosis can be done to better understand their roles in placental development.”

Reviewer #1 (Significance (Required)):

This significantly advances previous publications on this topic by functionally testing the discovered genes.

This highlights an excellent data mining strategy for a developmental disease using mice and translating to humans.

The audience is likely developmental biologists and reproductive specialists.

My expertise is bioinformatics and developmental biology.

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

The authors used RNA-seq data from mouse fetal placenta at e7.5, e8.5, and e9.5 to create timepoint-specific gene expression interaction networks to find genes that they predicted would regulate placental development. They confirmed four novel candidate genes and showed that in the transfected human trophoblast HTR-8/SVneo cell line, these four candidates reduced cell migration capacity. Additionally, the authors show that bulk RNA-seq data can be used to infer cell-type composition and when used with single-cell RNA-seq, can be a powerful tool to study the biological processes that involve multiple cell-types.

Overall, the authors are rigorous in their analyses, their conclusions appear sound, and the work could be an asset to the broader placental biology field. However, although the authors present an approach that future studies might find useful to replicate and their work has produced numerous novel transcripts/genes that warrant further investigation, the approach is not entirely novel, and could be expanded/improved (as suggested by the authors in the discussion), particularly with regard to validation of the genes/networks identified. Major and minor comments are listed below.

Major comments:

1) The authors used clustering and differential expression analysis to define sets of timepoint-specific genes. However, it was not clear to me the benefits of this approach. Why would using this approach be better than differential expression analysis alone such as in a typical ANOVA?

We have added more discussion on this matter to explain our approach. We believe using hierarchical clustering and pairwise differential expression analysis can help identify gene lists with higher confidence. These are the new details we added to the discussion section:

“Combining hierarchical clustering with differential expression analysis, we were able to identify gene groups using an unsupervised approach. It has also been shown that for times-series analyses with fewer than eight timepoints, pairwise differential expression analysis combined with additional methods identifies a more robust set of genes (Spies et al. 2019). Alternatively, model-based clustering using RNA-seq profiles (Si et al. 2014) could also be useful for gene group identification. However, it is still important to evaluate the robustness and functional relevance of the fitted models by carrying out additional downstream analyses.”

2) Related to number 1 above, although the authors are interested in timepoint-specific transcripts, the author's methods would filter out possibly interesting transcripts that turn on and off during development. The authors might want to check to see if there are transcripts that are up in e7.5 and then down in e8.5 but then up again in e9.5. Also, the author's methods seem to include transcripts that are not exclusive to one timepoint (i.e. are up in e7.5 and e8.5 but not e9.5). It might be interesting to differentiate transcripts that are exclusive to one timepoint from those that are in more than one timepoint.

We thank the reviewer for their valuable comment. We agree genes that turn on and off during the time course could be very interesting. In performing this analysis, we found that the number of such genes is rather small (38 genes that are up-regulated at e7.5 compared to e8.5 and up-regulated at e9.5 compared to e8.5). These genes were not enriched for processes that we observed with timepoint-specific gene groups, such as “trophoblast giant cell differentiation” (e7.5-specific genes), “labyrinthine layer development” (e8.5- and e9.5-specific genes), "blood vessel development” (e7.5- and e9.5-specific genes) and “response to nutrient” (e9.5-specific genes) (Supplementary Table S3). They are generally enriched for processes related to cytokine production and regulation of secretion.

We also agree that it is interesting to differentiate transcripts that are exclusive to one time point from those that are in more than one time point. In the revised manuscript, we added additional analysis for genes that belong to multiple timepoint groups due to different transcripts of the same gene being annotated as timepoint-specific, and genes unique to each timepoint (Added to results section 1):

“It is possible that timepoint-specific groups share genes that have timepoint-specific transcripts. Indeed, we identified 37 genes shared between e7.5 and e8.5, 5 genes shared between e7.5 and e9.5, and 109 genes shared between e8.5 and e9.5 (Supplementary Table S3). We found that genes only present at one timepoint (timepoint-unique genes) were generally enriched for similar terms as the full group of timepoint-specific genes (Supplementary Table S3). However, terms related to the development of labyrinth layer like “labyrinthine layer morphogenesis” and “labyrinthine layer blood vessel development” were only enriched when using all e8.5-specific genes but not when using e8.5 timepoint-unique genes. Moreover, we found that, unlike genes shared between e9.5 and e7.5, genes shared between e9.5 and e8.5 were enriched for processes such as “blood vessel development” and “insulin receptor signaling pathway”. This observation may indicate that different transcripts of the same genes could be expressed at different timepoints for the continuation of certain biological processes.”

3) In the network analysis it would be interesting and helpful to the reader to highlight, if any, nodes or terms that were found to be significant (i.e. hubs or genes that have a high centrality metric etc.) in both the STRING and GENIE3 networks or overlap the networks created by the two different algorithms to compare them. This might help readers better rank genes when using these data to decide what genes are most important at each timepoint.

We observed only one hub gene shared among networks inferred by the two methods (Vegfa in the e9.5 networks). However, hub genes of networks inferred by one method could be nodes in networks inferred by the other method. Hence, we have added lists of such genes in section 2. Interestingly, many of these genes have known roles in placental development. In terms of biological functions shared between the networks at the same timepoints, there were multiple interesting processes such as “positive regulation of cell migration”, “epithelium migration” and “vasculature development”, which we highlighted in Figure 2A.

In the revised manuscript, we have added the following details in different paragraphs of section 2 of the results:

“Although the networks inferred by the two methods did not share any hub genes, hub genes identified with one method could be members of the other method’s networks. These hub genes are Mmp9 (e7.5_1_STRING), Frk, Hmox1, and Nr2f2 (e7.5_2_GENIE3) (Table 1). This observation strengthens the potential roles of Frk gene in placental development.”

“Hub genes identified with one method and present in the other method’s networks are Hsp90aa1, Akt1, and Mapk14 (e8.5_1_STRING), Dvl3 and Msx2 (e8.5_2_GENIE3) (Table 1).”

“Hub genes identified with one method and present in the other method’s networks include important genes such as Rb1 (Sun et al. 2006), Yap1 (Meinhardt et al. 2020) (e9.5_1_GENIE3) and Vegfa (e9.5_2_STRING) (Table 1). Notably, Vegfa is the only hub gene identified with both of the network inference methods.”

4) The author's conclusion that network analysis can be used to identify genes more likely associated with specific placental cell types is very likely true, but I think that the conclusion would be more impactful if the authors reported how the method compares to simply taking a list of differentially expressed genes and looking for cell type enrichments using their favorite enrichment software. For example, if a gene is highly connected in a particular network that has been identified as SCT-specific, but that gene isn't considered an SCT "marker" by the placental biology research community, it would be interesting to highlight that it is prevalent in a previously published scRNA-seq dataset or a dataset that has isolated that particular cell type to show the advantages of using networks to find placental cell type specific genes.

We completely agree with the reviewer’s point and have now added a randomization analysis to compare the enrichment using PlacentaCellEnrich (PCE) with genes in networks and random genes (Supplementary Figure S6). We randomly sampled 10,000 gene sets with the same sizes as the subnetworks from their corresponding hierarchical groups and carried out PCE analysis. These tests showed that the enrichments of cell type-specific genes were only significant with the subnetwork genes but not the random genes. The randomization tests added a valuable highlight that the network genes are highly relevant to cell type-specific genes in the human placenta, and therefore provided more confidence in the gene lists obtained from the network analyses.

We also further checked the expression of the hub genes in other independent data in order to identify hub genes that are potentially cell type specific markers. For example, we observed that Dvl3 (e8.5_2_GENIE3) and Olr1 (e9.5_3_STRING) have been shown to be differentially expressed in SCT compared to other TB subtypes (human trophoblast stem cells, EVT (Sheridan et al. 2021) or endovascular TB (Gormley et al. 2021)).

We added the following detail in the results, section 3:

“Importantly, randomization tests showed that the enrichment of cell type-specific genes were only significant in these subnetworks but not in random gene sets selected from corresponding timepoint hierarchical groups (Supplementary Figure S6), which highlights the biological relevance of the gene network modules.”

Added to the discussion section:

“Moreover, hub genes could be used to identify potential novel markers for the cell types corresponding to their subnetworks. For example, hub genes of subnetworks enriched for SCT-specific genes such as Dvl3 (e8.5_2_GENIE3) and Olr1 (e9.5_3_STRING) are not established SCT marker genes, but are in fact differentially expressed in SCT compared to human trophoblast stem cells, EVT (Sheridan et al. 2021) or endovascular TB (Gormley et al. 2021). In general, combining network analysis with existing gene expression data from single cell or pure cell populations will allow identification of novel cell-specific marker genes to help future studies focused on different TB populations.”

5) While the selection of genes for validation was limited by the model system available for testing, the authors should recognize that the genes/networks identified here should first and foremost be validated in a mouse model (by knockdown/overexpression studies using mouse trophoblast stem cells or by evaluation of placenta/embryo in a KO/transgenic mouse model). Whether or not the data are relevant to human placentation is (at least initially) irrelevant. While we recognize that these are difficult studies requiring significant time and resources, as is, the data and results will have significantly less impact than if even a limited amount of such validation could be performed.

We thank the reviewer for this valuable comment. Based on this comment and the suggestions from reviewer #1, we have added the following points to the manuscript to discuss the relevance of the genes in the mouse models, and further explain our gene choices:

To assess the possible role of hub genes in mouse development more comprehensively, we extended our search for gene functions on the Mouse Genome Informatics (MGI) database to include not only placenta related GO and MGI phenotype terms (defined as “genes with known roles”), but also embryo related GO and MGI phenotype terms (defined as “genes with possible roles”). We included embryo related terms as “genes with possible roles” because embryonic lethal mouse knockout lines frequently have placentation defects, and because defects in placental development can be associated with the development of other embryonic tissues (Brown and Hay 2016; Perez-Garcia et al. 2018; Woods, Perez-garcia, and Hemberger 2018). This change resulted in an increase in the number of genes with relevant functions in mouse, including several annotated as embryonic lethal or with abnormal embryonic growth (see Supplementary Table S6). With the additional annotations:

• 6 out of 17 hub genes of e7.5 networks have known/possible roles.
• 17 out of 28 hub genes of e8.5 networks have known/possible roles.
• 48 out of 127 hub genes of e9.5 networks have known/possible roles. We also carried out randomization tests to determine if the number of known/possible genes we identified were significant. Randomization tests were carried out with the following procedure: for each timepoint, from the respective timepoint-specific groups, we sampled 10,000 gene sets of the same number as the hub gene numbers. Then we counted the number of known/possible genes in each random set. A p-value is calculated as the number of times a random gene set has ≥ known/possible genes than the observed number, divided by 10,000. We found that the number of genes with known/possible roles at each time point are statistically significant (Supplementary Figure S3). This result indicates that the gene sets we identified are significantly associated with relevant phenotypes in mouse.

The remaining hub genes are unannotated as related to placental or embryonic functions in the MGI database. Based on that, it is difficult to determine if they lack a relevant phenotype, or if there has not been a detailed assessment of the placenta.

Added to section 2 of the result section:

“Briefly, genes annotated under any GO or MGI phenotype terms related to placenta, TB cells, TE and the chorion layer are considered as having a “known” role in the placenta. Genes annotated under terms related to embryo are considered as having a “possible” role in the placenta, because embryonic lethal mouse knockout lines frequently have placentation defects, and because defects in placental development can be associated with the development of other embryonic tissues (Brown and Hay 2016; Perez-Garcia et al. 2018; Woods, Perez-garcia, and Hemberger 2018). Hereafter, such genes are referred to as “known/possible genes”. In the e7.5 networks, there were 17 hub genes in which six genes were known/possible. The number of hub genes that are labelled as known/possible is statistically significant when comparing to random gene sets selected from the e7.5 timepoint-specific group (Supplementary Figure S3). In the e8.5 and e9.5 networks, 17 out of 28 and 48 out of 127 hub genes were known/possible, respectively. Similar to e7.5, the number of hub genes labelled as known/possible in e8.5 networks and e9.5 networks were both statistically significant when comparing to random gene sets selected from the corresponding timepoint-specific groups (Supplementary Figure S3). These results indicate that the gene sets we identified are significantly associated with relevant phenotypes in the mouse.”

For the four genes that we tested in HTR-8/SVneo cells, we also added more information about the current known role of the gene in mouse.

Added to the discussion section:

“We identified hub genes and their immediate neighboring genes which could regulate placental development and confirmed the roles of four novel genes (Mtdh, Siah2, Hnrnpk and Ncor2) in regulating cell migration in the HTR-8/SVneo cell line. These genes were selected primarily based on the network analyses, but also based on expression data from human cells to account for possible differences between mouse and human placental gene expression. Previous studies suggested these four candidates are functionally important in mouse. Mtdh has been suggested to regulate cell proliferation in mouse fetal development (Jeon et al. 2010). The Siah gene family is important for several functions (Qi et al. 2013). Of relevance to the placenta, Siah2 is an important regulator of HIF1α during hypoxia both in vitro and in vivo (Qi et al. 2008). Moreover, while Siah2 null mice exhibited normal phenotypes, combined knockouts of Siah2 and Siah1a showed enhanced lethality rates, suggesting the two genes have overlapping modulating roles (Frew et al. 2003). Hnrnpk-/- mice were embryonic lethal, and Hnrnpk+/- mice had dysfunctions in neonatal survival and development (Gallardo et al. 2015) . Ncor2-/- mice were embryonic lethal before e16.5 due to heart defects (Jepsen et al. 2007). According to the International Mouse Phenotyping Consortium database (Dickinson et al. 2016), Ncor2 null mice also showed abnormal placental morphology at e15.5. However, none of these genes have been studied in the context of TB migration.”

Minor comments:

1) In the GO analysis, why not use a combination of hypergeometric and binomial distribution for enrichment decisions?

We used hypergeometric tests as in the default setting of ClusterProfiler. GO enrichment with hypergeometric test for differentially expressed genes was also suggested in Rivals et al., 2007 (Rivals et al. 2007). Combination of hypergeometric and binomial tests will be of great use when carrying out enrichment for cis-regulatory domains where there is a higher chance of sampling a gene randomly (McLean et al. 2010).

We have added this detail in the method section to make the analysis clearer.

2) In Figure 2B, are there any genes that are both hub nodes (diamonds) and annotated as having placental functions (squares)? If so, it might be good to show that in some way.

We agree this is necessary and have altered the presentation in Figure 2. In the revised manuscript, we have added an additional list of hub genes as genes with possible roles. The figure now shows hub genes with known placental functions (diamonds), hub genes with possible functions (hexagons) and hub genes without related annotation (rounded squares). Non-hub genes are now not shown to avoid crowdedness.

3) It might improve the deconvolution analysis to employ more than one method and recent reports have shown that the cell-type signature data is the most important parameter with the main factors influencing performance being biological (such as where the sample was taken) rather than technical (https://doi.org/10.1038/s41467-022-28655-4).

We agree the conclusion would have been further confirmed if we could employ another deconvolution method. Upon literature search, we found another tool, CAM (N. Wang et al. 2016), that had similar approaches to LinSeed which aims to infer cell proportions without reference. However, the tool has been taken down from Bioconductor and is not currently maintained. As a result, to the best of our knowledge, LinSeed is the only deconvolution tool that is completely reference-free.

We also tried carrying out the deconvolution analysis with another method, DSA (Zhong et al. 2013), with a limited number of marker genes obtained through literature review. However, when the marker genes are highly correlated in multiple cell types, the models failed to infer meaningful proportions.

We acknowledge that we need additional single cell RNA-seq data or marker genes obtained from pure cell populations to make more concrete conclusions for the deconvolution analysis. We hope with future studies, there will be more evidence supporting our observations.

We have added this acknowledgement in the results section:

“The identification of these cell groups could have resulted from noise introduced by both biological and technical variation, which is challenging to overcome when using a small sample size or analyzing without prior knowledge in the deconvolution analysis.”

Added to the discussion section:

“Nevertheless, we acknowledge that our deconvolution analysis and cell type annotations were limited due to the absence of matching scRNA-seq data, data from pure cell populations, or extensive cell marker lists. As these types of information are available, deconvolution analysis can be used to identify species-specific cell types or correcting for confounding effects prior to DEA (Sutton et al. 2022).”

4) The above report also shows that there are ways to correct for cell-type composition differences in DEA which might be interesting to look when using bulk data from different timepoints in future studies when focusing on different biological processes and not timepoint-specific transcripts.

We agree correcting for cell proportion prior to differential expression analysis will be interesting for future studies. When single cell RNA-seq data or more extensive marker gene lists are available, deconvolution analysis will be of great use for this purpose.

We have added this in the discussion section (also mentioned in point #3):

“Nevertheless, we acknowledge that our deconvolution analysis and cell type annotations were limited due to the absence of matching scRNA-seq data, data from pure cells, or extensive cell marker lists. As these types of information become more available, deconvolution analysis can be used to identify species-specific cell types or correcting for confounding effects prior to DEA (Sutton et al. 2022).”

5) Could the authors speculate as to possible reason(s) that an siRNA knockdown would give variable results functionally, while the actual gene expression appears to be consistently and sufficiently downregulated? Did the authors evaluate protein levels following siRNA knockdown?

Following the reviewer’s comment, we have evaluated protein levels for each target gene and each siRNA. For the genes that gave variable results between siRNAs (MTDH and NCOR2), we did not observe a change in their ability to reduce protein levels (Supplementary Figure S7). It is therefore possible that there are off-target effects for one of the siRNAs. We considered this possibility in designing the project, which is why we tested two siRNAs per target gene. Although siRNA off-target effects may be present, visual inspection of the migration experiments indicate that transfection with each of the siRNAs reduces migration capacity. We have added the possibility of off-target effects in the discussion section:

“We observed that while all siRNAs were able to decrease cell migration capacity, there was variability in the amount of decrease, even when comparing two siRNAs targeting the same gene. This observation did not seem to be associated with differences in transcript or protein knockdown levels and could be due to different off-target effects for different siRNAs.”

6) As mentioned in the discussion, finding genes that have timepoint dependent isoforms would an interesting and novel addition to the manuscript.

Protein isoforms would be interesting to study. Here we focused on different mRNA transcripts. We carried out additional GO analysis on the genes unique to each timepoint and genes shared among timepoints. This was also done in response to major comment 2:

In the revised manuscript, we added additional analysis for genes that belong to multiple timepoint groups due to different transcripts of the same gene being annotated as timepoint-specific, and genes unique to each timepoint (Added to results section 1):

“It is possible that timepoint-specific groups share genes that have timepoint-specific transcripts. Indeed, we identified 37 genes shared between e7.5 and e8.5, 5 genes shared between e7.5 and e9.5, and 109 genes shared between e8.5 and e9.5 (Supplementary Table S3). We found that genes only present at one timepoint (timepoint-unique genes) were generally enriched for similar terms as the full group of timepoint-specific genes (Supplementary Table S3). However, terms related to the development of labyrinth layer like “labyrinthine layer morphogenesis” and “labyrinthine layer blood vessel development” were only enriched when using all e8.5-specific genes but not when using e8.5 timepoint-unique genes. Moreover, we found that, unlike genes shared between e9.5 and e7.5, genes shared between e9.5 and e8.5 were enriched for processes such as “blood vessel development” and “insulin receptor signaling pathway”. This observation may indicate that different transcripts of the same genes could be expressed at different timepoints for the continuation of certain biological processes.”

7) Although outside the scope of this manuscript, it might be interesting to look at the effects of knocking down network genes on the networks themselves and in combination with a phenotypic readout such as a migration assay. With numerous knockouts and migration assay readouts, one could possibly find a better method to rank the genes within the networks.

We agree with this comment. Upon literature search, we realized this approach has been used in previous studies on other biological contexts such as virus entry (A. Wang et al. 2010; A. Wang, Ren, and Li 2011) and cancer cell growth (Paul et al. 2021). Although these studies used different network inference strategies from ours, their in silico gene knockouts proved to be effective for the candidate selection. However, the knockout process (both computationally and experimentally) may not be trivial; therefore, we agree the approach will be useful for future studies.

CROSS-CONSULTATION COMMENTS

I mostly agree with the other two reviewers.

It is not clear to me that additional KD experiments (i.e. ones that might affect fusion, proliferation, apoptosis), as proposed by Reviewer #3, would be that much more informative. There are many differences between mouse and human placentation, and these model systems (HTR8 and BeWo) are not truly representative of either. The additional data mining/computational work would be more useful and enhance data interpretation.

Reviewer #2 (Significance (Required)):

The authors use RNA-seq of mouse placenta at e7.5, e8.5, and e9.5 to show that timepoint-specific expression patterns are highly correlated with certain biological processes and point to the existence of certain cell types in the sample. While focused on early post-implantation mouse placental development, the author's methods could be transferrable to other timepoints, species, and organs. Furthermore, with their method they uncover what appears to be several novel, early placental, developmentally important genes and their results might be of interest to those in the field studying placental development.

Reviewer #3:

Summary:

This paper is an analysis of RNA-seq data from the mouse human placenta at embryonic day from 7.5 to 9.5 days. Bioinformatics was used to pinpoint genes networks, and tentatively connect with human cell populations. Wet experiments were performed on the HTR8/SV neo trophoblast cell model.

The introduction clearly posits the reasons why mouse models were chosen, and presents some examples of genes that are conserved between human and mouse placentas, before presenting the major steps of mouse placental development at the crucial periods analyzed.

The results are divided into four parts:

1. Identification of genes that are specific of fetal tissues at the three days studied
2. A network analysis of the genes using classical bioinformatics tools (String, Genie3) to identify gene modules
3. A connection with the human placenta at the level of cell-specific expression profile is then analyzed
4. A in vitro validation on a trophoblast cell model using siRNA to Knockdown genes identified in the in silico part of the paper. Three clustering methods were used to classify the genes according to their profile (at which time point they have the highest level). The function associated are dispatched into three logical physiological events (7.5: proliferation and ectoplacental cone development, 8.5 attachment of the placenta -chorioallantoidian at this stage- , and 9.5: syncytiotrophoblast constitution and labyrinth development, structures essential for growth and exchange).

Mostly minor comments:

Quality of the transcriptomics data: 6 replicates per condition (some being pools at E7.5 and 8.5) is a lot, and I congratulate the authors to have make such effort. This says a lot about the technical quality of their results. Nevertheless, there is no comment on the exclusion of two samples in the further analysis based upon the PCA. Could the authors comment upon the reasons why these two samples behave so differently from the others?

We thank the reviewer for the comment. We reviewed the RNA concentration and quality prior to sequencing, and did not observe that the outliers were of lower quality. After sequencing, quality control metrics (obtained with FastQC), also did not indicate that the two outliers were of poor quality. Based on the PCA, it is also unlikely that two samples were swapped. One possibility is that the tissues obtained for these samples were diseased in some way. However, this is difficult to confirm, so we did not want to speculate about this in the manuscript. We did exclude the two samples to ensure the accuracy of our downstream analyses.

Rq: at this stage some statistics of the degree of enrichment in keyword should be provided (such as Enrichment Scores, normalized or not, and False Discovery Rates, to be able to evaluate the actual robustness of the genes network identified. In addition, it seems that the authors supervised the 'keywords' and 'ontologies' toward placental function. A more agnostic approach could be very relevant, such as identifying the ontologies associated to for instance the set of genes that are highest at 8.5 days, by comparing them with preliminary datasets accessible via the GSEA platform of the BROAD institute or similar sites such as Webgestalt. This does not mean that the placental-targeted approach is not useful, but to have a more global overview is in my opinion indispensable.

We agree and this is a good point. We have now added a stringent approach to determine if the placenta-targeted terms are truly relevant to the gene networks. We performed randomization tests using random gene sets sampled from hierarchical groups of the same time point. These tests showed that the selected terms are significant in the networks when compared to gene groups of the same size from the timepoint specific hierarchical groups (Supplementary Figure S3). Moreover, we have added the specific -log10(q-value) of some highlighted enriched terms in the main text, so together with Figure 2A, the degree of enrichment of these terms can be shown in a clearer way.

We have added this detail in the result section:

“Compared to e8.5 and e9.5 networks, e7.5 networks had a higher rank or fold change and were significantly enriched for the GO terms “inflammatory response” (e7.5_1_STRING: -log10(q-value) = 22.82 and e7.5_2_GENIE3: -log10(q-value) = 3.95) and “female pregnancy” (e7.5_2_GENIE3: -log10(q-value) = 4.1) (Figure 2A, Supplementary Table S5). The term “morphogenesis of a branching structure”, which can be expected following chorioallantoic attachment around e8.5, was not enriched at e7.5, but was enriched in multiple e8.5 and e9.5 networks (e8.5_1_STRING: -log10(q-value) = 1.73, e8.5_2_GENIE3: -log10(q-value) = 1.72, e9.5_1_STRING: -log10(q-value) = 4.01, e9.5_1_GENIE3: -log10(q-value) = 1.54, e9.5_2_STRING: -log10(q-value) = 14.33, and e9.5_2_GENIE3: -log10(q-value) = 2.2). After chorioallantoic attachment finishes, nutrient transport is being established. Accordingly, we observed the following enrichments: “endothelial cell proliferation” (highest ranked in e9.5_2_STRING: -log10(q-value) = 15.91), “lipid biosynthetic process” (only significant after e7.5, highest ranked in e9.5_3_STRING: -log10(q-value) = 17.63), “cholesterol metabolic process” (only significant after e7.5, highest ranked in e9.5_2_GENIE3: -log10(q-value) = 2.76 and e9.5_3_STRING: -log10(q-value) = 7.79), and “response to insulin” (only significant after e7.5, highest ranked in e9.5_1_GENIE3: -log10(q-value) = 1.67).”

“Using randomization tests, we observed the majority of these GO terms (10 out of 11 terms) were significantly enriched when using the network genes but not random gene sets (significance level of 0.05; the term “vasculature development” having p-value = 0.0549 and 0.0575 in with subnetwork e9.5_1_GENIE3 and e9.5_3_GENIE3, respectively) (see Materials and Methods, Supplementary Figure S3). This analysis demonstrates that the network genes were highly relevant to the biological functions of interest. Moreover, the observed GO terms strongly aligned with the processes enriched when using the full lists of timepoint-specific genes (Supplementary Table S3), indicating the representative characteristics of the network genes. While the current analysis focuses on the biological processes related to placental development, there are other terms significantly enriched, which can be found in Supplementary Table S5.”

This is partially done in the part 2 of the results, but it would be relevant to do it on the group of highly expressed genes and not only on the clusters found by the algorithm of sting and genie3.

We have added GO analysis for timepoint-specific genes and also observed highly relevant processes being enriched (Supplementary Table S3). This additional analysis has also helped strengthen the relevance of the network genes, as the observed terms with network genes aligned well with the terms enriched with the full lists of genes.

Rq: in the second part of the results, everything is descriptive but no hierarchy is given to facilitate the understanding and to try to generate a few 'take-home messages' for the reader.

We agree with the comment and have adjusted the writing accordingly. We have added the following statements in section 2 of the result section:

“In summary, we identified 18 subnetworks across three timepoints for downstream analyses, some of which were enriched, according to GO analysis and randomization tests, for specific terms relating to placental development (Figure 2A).”

“These results indicate that the gene sets we identified are functionally relevant in the mouse models.”

“In summary, we have identified hub genes in networks at each timepoint. Analyzing the annotations of hub genes using the MGI database demonstrated that the hub genes are biologically relevant to mouse development and will be strong candidates for future investigation.”

The network analysis is well presented in Figure 2. I wonder whether the author could add systematically besides the three examples that are given the network analysis for the other enrichment network that are described (the four at e7.5, the 6 at e8.5 and the 8 at e9.5).

We have added the additional figures in Supplementary Figure S3.

The deconvolution of the 3rd part of the results to try to connect the mouse results to the human cell situation is interesting. I suspect that given the terms of the mouse placentas used, it would be relevant to focus on 1st trimester human placental cells.

The reference dataset we used in the PlacentaCellEnrich analysis was from human 1st trimester placenta samples. For the Placenta Ontology analysis, we were limited to the provided database from (Naismith and Cox 2021); however, it will be interesting to revisit the analysis when the database is extended.

We have specified that the reference data in PlacentaCellEnrich analysis was from human 1st trimester placenta in the methods section:

“For PlacentaCellEnrich, cell-type specific groups were based on the single-cell transcriptome data of first trimester human maternal-fetal interface from Vento-Tormo et al.”

As previously mentioned, this is a highly descriptive paragraph, and two or three sentences at the end of each paragraph of the results would be in my opinion indispensable to present the most important observations of the results in an intelligible way. Overall, the data presented by the authors, are not obviously 'raw data', but an effort of interpretation should be done by the authors to underline the importance of their results, and to stress among these results which are the most important, and which are the most relevant for placental development and human health.

We agree with the comment and have adjusted the writing accordingly. We have added this summary paragraph at the end of section 3 of the result section:

“In summary, we have demonstrated that the identification of timepoint-specific gene groups and densely connected network modules can be used to infer the cellular composition of bulk RNA-seq samples. We used independent human datasets from different sources to annotate the cell types in each timepoint’s samples. As a result, from the bulk RNA-seq data we were able to observe that at e7.5 and e8.5, there was a high proportion of different TB populations, whereas at e9.5, the placental tissues consisted of multiple cell types such as TB, endothelial and fibroblast cells.”

In the last part, which is very important in this type of paper, four genes were selected. A choice of highly expressed genes was made (which can in fact be discussed, some transcriptional factors may have a crucial importance with relatively low levels of expression). The efficiency of the siRNA was overall excellent. The authors showed that each of these siRNA is efficient to inhibit cell migration in the HTR8/SVneo model.

The migration assays are quantified, but there is a inherent limit of the cell model: the authors analyzed only cell migration, but not other very important parameters. One of them is trophoblast fusion, an issue that can be studied in another trophoblast cell model, the BeWo cells, which are induced to fuse under forskolin. It would be highly relevant to test the siRNA identified in this respect, since fusion is a very conspicuous feature of trophoblast cells in mice as well as in humans. Other relevant endpoints such as proliferation markers, apoptosis markers, oxidative stress markers could be studied in the KD cell models. Alternatively, it would have been interesting to evaluate the overall effect of the siRNA by transcriptomics and check whether the modified gene expression leads to specific profiles characteristic of a certain moment of placental development in mice, or proportion of various cells in the human placentas. Without asking for further experiments the authors should mention these limits in their discussion.

We completely agree with this comment and are investigating each of our candidate genes in more detail in ongoing studies. As we have already learned that each gene is involved in different processes and pathways, we feel that these studies are out of the scope of the current paper. However, we have added this point to our discussion section:

“However, more detailed analysis and process specific assays are needed. For example, future studies assessing each gene’s role in cell adhesion, cell-cell fusion, cell proliferation and cell apoptosis can be done to better understand their roles in placental development.”

In sum, I feel that this paper provides an excellent dataset, but that the authors should make an additional effort of redaction to extract the most important conclusions of their paper. This would increase its impact for a wider public.

Thank you. We have attempted to do so in the revised version.

Reviewer #3 (Significance (Required)):

The context is well introduced, but explanatory and synthesis sentences are missing at the end of each paragraph. I am relatively competent in bioinformatics methods, including deconvolution, and rather expert in cell biology. Therefore I feel comfortable to evaluate this paper.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This paper is an analysis of RNA-seq data from the mouse human placenta at embryonic day from 7.5 to 9.5 days. Bioinformatics was used to pinpoint genes networks, and tentatively connect with human cell populations. Wet experiments were performed on the HTR8/SV neo trophoblast cell model.

The introduction clearly posits the reasons why mouse models were chosen, and presents some examples of genes that are conserved between human and mouse placentas, before presenting the major steps of mouse placental development at the crucial periods analyzed.

The results are divided into four parts:

1. Identification of genes that are specific of fetal tissues at the three days studied
2. A network analysis of the genes using classical bioinformatics tools (String, Genie3) to identify gene modules
3. A connection with the human placenta at the level of cell-specific expression profile is then analyzed
4. A in vitro validation on a trophoblast cell model using siRNA to Knockdown genes identified in the in silico part of the paper.

Three clustering methods were used to classify the genes according to their profile (at which time point they have the highest level). The function associated are dispatched into three logical physiological events (7.5: proliferation and ectoplacental cone development, 8.5 attachment of the placenta -chorioallantoidian at this stage- , and 9.5: syncytiotrophoblast constitution and labyrinth development, structures essential for growth and exchange).

Mostly minor comments:

Quality of the transcriptomics data: 6 replicates per condition (some being pools at E7.5 and 8.5) is a lot, and I congratulate the authors to have make such effort. This says a lot about the technical quality of their results. Nevertheless, there is no comment on the exclusion of two samples in the further analysis based upon the PCA. Could the authors comment upon the reasons why these two samples behave so differently from the others?

Rq: at this stage some statistics of the degree of enrichment in keyword should be provided (such as Enrichment Scores, normalized or not, and False Discovery Rates, to be able to evaluate the actual robustness of the genes network identified. In addition, it seems that the authors supervised the 'keywords' and 'ontologies' toward placental function. A more agnostic approach could be very relevant, such as identifying the ontologies associated to for instance the set of genes that are highest at 8.5 days, by comparing them with preliminary datasets accessible via the GSEA platform of the BROAD institute or similar sites such as Webgestalt. This does not mean that the placental-targeted approach is not useful, but to have a more global overview is in my opinion indispensable.

This is partially done in the part 2 of the results, but it would be relevant to do it on the group of highly expressed genes and not only on the clusters found by the algorithm of sting and genie3. Rq: in the second part of the results, everything is descriptive but no hierarchy is given to facilitate the understanding and to try to generate a few 'take-home messages' for the reader.

The network analysis is well presented in Figure 2. I wonder whether the author could add systematically besides the three examples that are given the network analysis for the other enrichment network that are described (the four at e7.5, the 6 at e8.5 and the 8 at e9.5).

The deconvolution of the 3rd part of the results to try to connect the mouse results to the human cell situation is interesting. I suspect that given the terms of the mouse placentas used, it would be relevant to focus on 1st trimester human placental cells.

As previously mentioned, this is a highly descriptive paragraph, and two or three sentences at the end of each paragraph of the results would be in my opinion indispensable to present the most important observations of the results in an intelligible way. Overall, the data presented by the authors, are not obviously 'raw data', but an effort of interpretation should be done by the authors to underline the importance of their results, and to stress among these results which are the most important, and which are the most relevant for placental development and human health.

In the last part, which is very important in this type of paper, four genes were selected. A choice of highly expressed genes was made (which can in fact be discussed, some transcriptional factors may have a crucial importance with relatively low levels of expression). The efficiency of the siRNA was overall excellent. The authors showed that each of these siRNA is efficient to inhibit cell migration in the HTR8/SVneo model.

The migration assays are quantified, but there is a inherent limit of the cell model: the authors analyzed only cell migration, but not other very important parameters. One of them is trophoblast fusion, an issue that can be studied in another trophoblast cell model, the BeWo cells, which are induced to fuse under forskolin. It would be highly relevant to test the siRNA identified in this respect, since fusion is a very conspicuous feature of trophoblast cells in mice as well as in humans. Other relevant endpoints such as proliferation markers, apoptosis markers, oxidative stress markers could be studied in the KD cell models. Alternatively, it would have been interesting to evaluate the overall effect of the siRNA by transcriptomics and check whether the modified gene expression leads to specific profiles characteristic of a certain moment of placental development in mice, or proportion of various cells in the human placentas. Without asking for further experiments the authors should mention these limits in their discussion.

In sum, I feel that this paper provides an excellent dataset, but that the authors should make an additional effort of redaction to extract the most important conclusions of their paper. This would increase its impact for a wider public.

Significance

The context is well introduced, but explanatory and synthesis sentences are missing at the end of each paragraph. I am relatively competent in bioinformatics methods, including deconvolution, and rather expert in cell biology. Therefore I feel comfortable to evaluate this paper.

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Referee #2

Evidence, reproducibility and clarity

The authors used RNA-seq data from mouse fetal placenta at e7.5, e8.5, and e9.5 to create timepoint-specific gene expression interaction networks to find genes that they predicted would regulate placental development. They confirmed four novel candidate genes and showed that in the transfected human trophoblast HTR-8/SVneo cell line, these four candidates reduced cell migration capacity. Additionally, the authors show that bulk RNA-seq data can be used to infer cell-type composition and when used with single-cell RNA-seq, can be a powerful tool to study the biological processes that involve multiple cell-types.

Overall, the authors are rigorous in their analyses, their conclusions appear sound, and the work could be an asset to the broader placental biology field. However, although the authors present an approach that future studies might find useful to replicate and their work has produced numerous novel transcripts/genes that warrant further investigation, the approach is not entirely novel, and could be expanded/improved (as suggested by the authors in the discussion), particularly with regard to validation of the genes/networks identified. Major and minor comments are listed below.

Major comments:

1) The authors used clustering and differential expression analysis to define sets of timepoint-specific genes. However, it was not clear to me the benefits of this approach. Why would using this approach be better than differential expression analysis alone such as in a typical ANOVA?

2) Related to number 1 above, although the authors are interested in timepoint-specific transcripts, the author's methods would filter out possibly interesting transcripts that turn on and off during development. The authors might want to check to see if there are transcripts that are up in e7.5 and then down in e8.5 but then up again in e9.5. Also, the author's methods seem to include transcripts that are not exclusive to one timepoint (i.e. are up in e7.5 and e8.5 but not e9.5). It might be interesting to differentiate transcripts that are exclusive to one timepoint from those that are in more than one timepoint.

3) In the network analysis it would be interesting and helpful to the reader to highlight, if any, nodes or terms that were found to be significant (i.e. hubs or genes that have a high centrality metric etc.) in both the STRING and GENIE3 networks or overlap the networks created by the two different algorithms to compare them. This might help readers better rank genes when using these data to decide what genes are most important at each timepoint.

4) The author's conclusion that network analysis can be used to identify genes more likely associated with specific placental cell types is very likely true, but I think that the conclusion would be more impactful if the authors reported how the method compares to simply taking a list of differentially expressed genes and looking for cell type enrichments using their favorite enrichment software. For example, if a gene is highly connected in a particular network that has been identified as SCT-specific, but that gene isn't considered an SCT "marker" by the placental biology research community, it would be interesting to highlight that it is prevalent in a previously published scRNA-seq dataset or a dataset that has isolated that particular cell type to show the advantages of using networks to find placental cell type specific genes.

5) While the selection of genes for validation was limited by the model system available for testing, the authors should recognize that the genes/networks identified here should first and foremost be validated in a mouse model (by knockdown/overexpression studies using mouse trophoblast stem cells or by evaluation of placenta/embryo in a KO/transgenic mouse model). Whether or not the data are relevant to human placentation is (at least initially) irrelevant. While we recognize that these are difficult studies requiring significant time and resources, as is, the data and results will have significantly less impact than if even a limited amount of such validation could be performed.

Minor comments:

1) In the GO analysis, why not use a combination of hypergeometric and binomial distribution for enrichment decisions?

2) In Figure 2B, are there any genes that are both hub nodes (diamonds) and annotated as having placental functions (squares)? If so, it might be good to show that in some way.

3) It might improve the deconvolution analysis to employ more than one method and recent reports have shown that the cell-type signature data is the most important parameter with the main factors influencing performance being biological (such as where the sample was taken) rather than technical (https://doi.org/10.1038/s41467-022-28655-4).

4) The above report also shows that there are ways to correct for cell-type composition differences in DEA which might be interesting to look when using bulk data from different timepoints in future studies when focusing on different biological processes and not timepoint-specific transcripts.

5) Could the authors speculate as to possible reason(s) that an siRNA knockdown would give variable results functionally, while the actual gene expression appears to be consistently and sufficiently downregulated? Did the authors evaluate protein levels following siRNA knockdown?

6) As mentioned in the discussion, finding genes that have timepoint dependent isoforms would an interesting and novel addition to the manuscript.

7) Although outside the scope of this manuscript, it might be interesting to look at the effects of knocking down network genes on the networks themselves and in combination with a phenotypic readout such as a migration assay. With numerous knockouts and migration assay readouts, one could possibly find a better method to rank the genes within the networks.

CROSS-CONSULTATION COMMENTS

I mostly agree with the other two reviewers. It is not clear to me that additional KD experiments (i.e. ones that might affect fusion, proliferation, apoptosis), as proposed by Reviewer #3, would be that much more informative. There are many differences between mouse and human placentation, and these model systems (HTR8 and BeWo) are not truly representative of either. The additional data mining/computational work would be more useful and enhance data interpretation.

Significance

The authors use RNA-seq of mouse placenta at e7.5, e8.5, and e9.5 to show that timepoint-specific expression patterns are highly correlated with certain biological processes and point to the existence of certain cell types in the sample. While focused on early post-implantation mouse placental development, the author's methods could be transferrable to other timepoints, species, and organs. Furthermore, with their method they uncover what appears to be several novel, early placental, developmentally important genes and their results might be of interest to those in the field studying placental development.

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Referee #1

Evidence, reproducibility and clarity

Review of "Identifying novel regulators of placental development using time series transcriptomic data and network analyses."

The authors present a detailed bioinformatic assessment of mouse developmental time series of the placenta. They apply current data mining and analysis methods to identify protein-centred networks that are likely enriched to specific cell types of the placenta. They then translate these findings to humans using statistical comparisons of human single-cell sequencing data of the placenta. Lastly, they use knock-down experiments to validate the conserved functional importance of the hub genes in the mouse protein networks in human cells. The strengths of this paper are the rigorous data mining methods and the functional translation to humans from mice. There are no critical weaknesses to the article. There is a blend of statistical analysis with anecdotal or hand curation from databases and the literature, but it is unclear if these curated finings are circumstantial or statistically meaningful. In the end, the hypothesis seems to hold in that 4/4 gene knocked down in the human cells gave a migration phenotype.

Comments, questions, critique

1. Given the translational aims of the paper, more introduction/discussion material on the comparative aspects of mice and humans are needed. Are giant cells and EVT the same? What are the cell equivalents that you are discovering? The Soncin et al. paper is cited, but I think underused. This publication contains time series data on mice and humans and could be used as external validation of clusters, networks, and other analyses. Other publications to consider for context are

a) Cox B, et al. Mol Syst Biol 5: 279.

b) Silva JF, Serakides R. 2016. Cell Adhes Migr 10: 88-110. (specifically discusses migration difference between the species placenta)

1. Clustering represented in Figure 1B, was this a supervised model? Why only three clusters?) Did you specify that there would be three models and force each gene profile into one of the categories? How robust are the fits? A fitted model might be a better approach as you can specify the ideal models (early high, late high and mid-high), then determine each gene profile that fits each model and only assess those genes with a significant fit to the model. Forcing clustering to the three-model fit likely gives many poorly fitting profiles. While in the end, this works out, it may be due to applying other post hoc methods for gene enrichment, where noise distributes randomly.

2. Several statements are made about the conservation of importance between mouse and human hub genes. For example, "We predict these highly expressed genes to be generally important for TB function and processes such as cell migration, a term associated with multiple timepoint specific networks (Figure 2A)." While your knock-down assay of migration results shows these hub genes to be necessary to humans, what do they mean to the mouse? You did not use mouse TSC to assess functional importance concurrently. You note a small number of genes as of known importance, "127 hub genes of which 16 have been annotated as having a role in placental development". Were the others knocked out but lack a developmental phenotype or not assessed? Are these functionally redundant in the mouse or not involved in the same processes between the species?

3. In determining conservation between mouse and human networks, were only 1:1 orthologs examined or did you consider more complex 1:many mapping conditions between the two species?

4. Should the migration assay be normalized to survival/adhesion? If 70,000 cells were seeded but had 50% cell death (or reduced adhesion), then it may appear to be poor migration. Should the migration be evaluated as a ratio of top to bottom cell densities to control for poor adhesion or survival?

Significance

This significantly advances previous publications on this topic by functionally testing the discovered genes.

This highlights an excellent data mining strategy for a developmental disease using mice and translating to humans.

The audience is likely developmental biologists and reproductive specialists.

My expertise is bioinformatics and developmental biology.

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Reply to the reviewers

In this study we reveal that, in both mice and humans, the metabolic benefits of caloric restriction (CR) are sex- and age-dependent. Through a systematic review of the literature, we show that sex differences have been largely overlooked by previous CR research, a finding that Reviewer 1 highlights as “an important point”. Our results have critical implications for understanding the fundamental biology linking diet and health outcomes, as well as translational strategies to leverage the therapeutic benefits of CR in humans.

We thank the reviewers for their helpful appraisal of our manuscript, which Reviewer 2 highlights as “a very well written paper”. Reviewer 1 emphasised the translational relevance of our findings and commented on the “systematic” nature of our study. They noted that it “was well performed”, ”is a valuable and important contribution to the field”, and “will elicit great interest in the scientific and public readership.” Indeed, the importance of sex as a biological variable is the focus of a September 2022 news feature in Nature (https://www.nature.com/articles/d41586-022-02919-x), underscoring the timeliness and relevance of our findings. Our response to the reviewers comments is outlined below, including the changes we have incorporated in a revised version of our manuscript.

Reviewer 1 – Major Comments:

__A) The clinical part is definitely the weak spot in the study. I don't think that the data should be omitted, but the authors should be very careful in interpreting the data. Obvious limitations apply to this part, which need to be more directly addressed in the abstract and discussion. It feels like the data from the small-scale clinical trial is exaggerated. __The clinical study was conducted by Prof Alex Johnstone’s group at the Rowett Institute of Nutrition and Health, University of Aberdeen. Her group are experts in the study of dietary interventions for weight loss. The study was conducted to a high standard and therefore we have the utmost confidence in the conclusions drawn from our analysis of this data.

As we discuss in response to the reviewer’s other points below, the clinical study was primarily designed to address other outcomes and we analysed the data retrospectively to investigate if sex and age affect CR-induced weight and fat loss. This explains some of the limitations that the reviewer mentions, e.g. the relatively low numbers of younger males, and the focus on overweight and obese subjects. As requested, we have now addressed these limitations as follows:

1. Updated the abstract to clarify that the data are from overweight and obese subjects.
2. Updated the results to emphasise that we did a retrospective analysis of CR in overweight and obese subjects (lines 396-398).
3. Performed an additional ANCOVA analysis to test if baseline adiposity or BMI contribute to the sex differences in body mass, fat mass or fat-free mass (new Supplementary Figure 11); see Reviewer 1 Major Point D below.
4. Updated the ‘Limitations’ section of the Discussion to highlight the retrospective nature of the human study (lines 746-748).
5. Updated the Methods to again clarify the retrospective nature of the analysis (lines 884-885). __B) It is important to mention in the abstract and the discussion that the human data came from obese participants. This might well influence the findings from human data. __The human subjects were overweight or obese; this was previously stated in the methods section (line 885) and in the discussion (lines 509-511). To further clarify this, we now also mention it in the Abstract (lines 52-53) and have reiterated it in the Discussion (line 744). Importantly, the fact that humans still show age-dependent sex differences in fat loss, even when overweight and obese, supports our conclusion that this age effect in mice is not simply a consequence of aged mice being fatter than younger mice. We refer to this as the ‘baseline adiposity’ hypothesis (lines 500-518 of the Discussion). In response to point D below, we have also analysed if the loss of fat mass or fat-free mass is influenced by adiposity or BMI at baseline (pre-CR). Our analyses show that neither of these parameters explain the sex differences in loss of fat mass or fat-free mass (see new Supplementary Figure 11).

__C) It is very important to calculate the % calorie restriction of the human participants achieved throughout the CR study. This is crucial information to compare it to other studies. __We have updated the Methods (lines 906-909) to explain the basis for the weight loss diet, as follows: “Participants had their basal energy requirements determined and each participant was then fed an individualised diet with a caloric content equivalent to 100% of their resting metabolic rate (Table 3). This approach was taken to standardise the diet to account for individual energy requirements and energy restriction.” We have also updated Table 3 to show the caloric intake for males and females. Note that RMR accounts for ~60-70% of total daily energy expenditure (TDEE) in adults (Martin et al., 2022), so the diet in our study would give a daily caloric deficit of around 30-40% from baseline TDEE.

__D) Since there is quite a wide range in the BMIs of the participants, can the authors also stratify against BMI? __We have done this against both baseline BMI and against baseline fat mass (the latter to further test the ‘baseline adiposity’ hypothesis). We present this data in an updated Supplementary Figure 11. We find that, in males but not in females, baseline BMI or fat mass are significantly associated with the changes in fat mass or fat-free mass: surprisingly, individuals with higher baseline fat mass or BMI show less fat loss and a greater loss of fat-free mass during CR. Importantly, males and females do not significantly differ in the relationships between baseline fat mass (or BMI) and loss of fat mass or fat-free mass. This further supports our conclusion that the sex differences in fat loss are unrelated to differences in baseline adiposity. We report this in lines 409-411 of the Results and lines 513-515 of the Discussion.

__E) There is no mention of any pre-study registration online of the clinical part (e.g. _gov_). Was this done? __This study was done before pre-registration was a requirement for clinical trials. We retrospectively analysed the study data to investigate if sex and/or age influence the outcomes. In the updated manuscript we now state this on lines 884-885 of the Methods, as well as in the Results (line 396) and Discussion (lines 746-748).

__F) In the methods section the authors write "Participants were informed that the study was funded by an external commercial sponsor...". This is important information, and this is not mentioned anywhere else in the paper. Can the authors clarify this point? A commercial sponsor would, in my view, qualify for a conflict of interest that needs to be mentioned. __We have updated the Declaration of Interests section to clarify this as follows: “The human weight loss study was funded by a food retailer; however, the company had no role in the data analysis, interpretation or conclusions presented in this paper.”

__G) How did the authors determine the group sizes for the clinical part? I have some doubts about the sub-group sizes. It would be valuable information if the authors had a statistical analysis plan prior conducting the study. It appears a bit, like the sub-groups were chosen at random, to match findings of the mouse data. Otherwise, there should have been a better allocation within the sub-groups (especially age). __We agree that larger group sizes would have been preferable. This limitation reflects that the study was not originally designed to test age and sex effects on CR outcomes, but instead was analysed retrospectively to investigate the impact of these variables. As mentioned above, we have updated the text of the manuscript to highlight the retrospective nature of the analyses. In the Discussion, under ‘Limitations’, we also highlight the fact that relatively few younger subjects are included in the human study (lines 744-745).

__H) *There's a big problem with the age stratification of the male participants in the clinical data. If I'm correct there are only 5 males 45 groupings.

__I) The applied protocol for CR in mice is known to provoke long fasting phases and probably elicits some effects through fasting alone, rather than the caloric deficit. There are some papers out addressing this (e.g. by deCabo, Lamming). The authors should not dismiss this fact and at least address it in their discussion. Also, given this fact, it would be thoughtful to include a database-search - not only regarding CR - but also regarding various types of intermittent fasting protocols in humans and animal studies (similar to what the authors did in the supplemental figure). __We agree on the importance of highlighting recent studies demonstrating that prolonged daily fasting contributes to the outcomes of typical ‘single-ration’ CR protocols. We have added a new paragraph to the Discussion to address this (Lines 710-719).

Regarding the second point, we feel that including a new literature search that addresses not only CR, but also intermittent fasting, is beyond the scope of the current manuscript. However, this is a very good idea and would be worth addressing in a future standalone review article. We have also updated our source data to include all data from our literature reviews, to help if other researchers wish to analyse according to fasting duration or other variables.

__J) Did the authors monitor the eating time of the mice? __We have since done this in new cohorts of mice fed using the same CR protocol. We find that the mice consume their food within 2-3 hours, consistent with other CR studies. We have now mentioned this in the Methods section (lines 867-868).

__K) While CR certainly has a lot of health benefits in rodents and humans, it should be advised to raise the cautious note that it may not be beneficial for everyone in the general population. For some groups of people and in some cases (e.g. infectious diseases, pregnancy) even CR with adequate nutritional intake of micro/macronutrients might be disadvantageous. This should be mentioned clearly, as the topic gets more and more "hyped" in public media and online. __We now highlight this important point in the opening paragraph of the introduction (lines 65-67).

__L) There is no indication of how the authors dealt with missing data. Statistically this can be very important, especially in cases with a low number of data points. __In the Methods section we previously explained (lines 846-848) that “Mice were excluded from the final analysis only if there were confounding technical issues or pathologies discovered at necropsy.” No data had to be excluded from our human study and we have now stated this in the Methods (lines 897-898). For analyses involving paired or repeated-measures data (e.g. time courses of body mass or blood glucose), if data points were missing or had to be excluded for some mice then we used mixed models for the statistical analysis. We have now updated this information in the ‘Statistical analysis’ section of the Methods (lines 1047-1048). Because of the large numbers of mice used in our studies, analyses remain sufficiently well powered even if some data points were missing or had to be excluded.

__M) Key data from qPCR should be followed up by western blots or other means. If this was done and there was no effect, the authors should report this. Also, is there any evidence or the possibility to support these findings regarding pck1 and ppara in human samples? __As requested, we will next use Western Blotting to assess the expression of proteins encoded by the transcripts that show sex and/or diet differences within the liver (Fig. 6A). These data will be reported in our fully revised manuscript.

Regarding effects of CR on PCK1 and PPARA expression in human liver samples, no human CR studies have taken liver biopsies for downstream molecular analysis. Recent studies of the GTEx database confirm that hepatic gene expression in humans is highly sexually dimorphic (Oliva et al., 2020). We checked PCK1 and PPARA in the GTEx database and found that, in the liver, each of these transcripts is expressed more highly in females than in males (https://www.gtexportal.org/home/gene/PCK1 & https://www.gtexportal.org/home/gene/PPARA). While this is the opposite to what we observe in our ad libitum mice (Fig. 6A), it demonstrates that sex differences in these genes’ hepatic expression do occur in humans. The effect of CR on their hepatic expression, and whether this differs between males and females, remains to be addressed.

N): I think it would be very valuable to analyse the sex-differences in lipolysis directly in fat tissues. The authors concentrated on differences in hepatic mRNA profiles, but there's an obvious possibility and gap in their story. ____We agree that this would be informative. In the Discussion we cite previous research identifying sex differences in adipose lipolysis and lipogenesis and explain how this fits with our findings (lines 567-574). Since submitting our manuscript, we have begun experiments to investigate sex differences in the effects of CR on lipid metabolism and molecular pathways in adipose tissue. However, these analyses are extensive and ongoing, so we feel strongly that attempting to include them in our present paper would not only substantially delay publication, but also overload what is already a very extensive paper. Therefore, we plan to report our findings in future publications.

__O) Given the relatively low n and sometimes small effect sizes I fear that some of their findings won't be reproduced by other labs. Were the (mouse) data collected all at once in one cohort or did the authors pool data from different cohorts/repeats? __We presume the reviewer means ‘relatively high n’, as most of our mouse analyses used large group sizes. The mouse data were pooled from across multiple cohorts, with ANOVA confirming that the same sex-dependent CR effects were observed within each cohort. This reproducibility across multiple cohorts is a clear strength of our study because it demonstrates the robustness of our findings. Importantly, the sex differences in fat loss, weight loss and glucose homeostasis were still observed in our much-smaller cohort of evening-fed mice (Fig. S5-S6) (n = 5-6), demonstrating that large sample sizes are not needed for other researchers to detect these effects.

Reviewer 1 – Minor comments:

__a) The discussion is very extensive, and I suggest compressing the information presented there to make it more easily readable. __We have removed some text that was more speculative, such as the paragraph discussing a possible role for ERalpha. We have also revised wording elsewhere to state things more succinctly. However, given the scope of our study we feel we cannot substantially cut down the Discussion without compromising the interpretation of our findings. We note the Reviewer two’s comment that “This is a very well written paper” and feel that attempting to compress the extensive information in the Discussion would compromise, rather than help, the readability.

__b) There is some confusion present in the literature regarding the nomenclature of CR/fasting interventions. Recently some reviews have summarized the different forms (e.g. Longo Nature Aging, Hofer Embo Mol Med, ...) and the authors should address this briefly. Especially the applied CR intervention in ____mice overlaps with intermittent fasting. __We have updated the Discussion (lines 710-719) to explain how our single-ration CR protocol also incurs a prolonged intermittent fast, and how this fast per se may contribute to metabolic effects.

c): The order of the subpanels in Figure 9 (and other figures where B is below A and so on) is confusing. Please rearrange or indicate in a visual way which panels belong to each other.

We disagree that the order of subpanels is confusing: the panels are clearly labelled, and we find it most logical to have the absolute values shown in the top row (panels A, C and E), with the corresponding graphs of fold changes shown beneath each of these (panels B, D and F). This allows the reader to quickly compare the absolute vs fold-change data for each readout. If we had panels A-C on the top row and D-F on the second row, then the connection between graphs 9C and 9D would be less clear and comparable.

d): Did the authors also measure cardiovascular (e.g. blood pressure) parameters? There is some evidence out there that there is an age/sex dependency during fasting/CR. This would be a nice add-on to the rather small clinical data here.

We did measure various cardiovascular parameters for our mice but find, unlike for the metabolic outcomes, these generally don’t show sex or age differences. In our human study we measured blood pressure and heart rate before starting CR and at weeks 3 and 4 post-CR. For this response to reviewers we have summarized these human data in Figure R1. The data show that CR decreases blood pressure and heart rate in males and females (Figs. R1A-E). In the younger age group (We have decided to not include these data in the current study because we feel it is already extensive and is focused on metabolic outcomes. We instead plan to report the cardiovascular outcomes (from both humans and mice) in a separate paper.

__e) What was the decision basis for stratifying the human data into 45 years? __We used 45 years as the cutoff point because this is the age when, in women, oestrogen levels begin to decline (this point was stated in lines 491-492 of the Discussion, and we now reiterate it in lines 414-415 of the Results).

__f) The part on aging starting in Figure 7 comes quite surprising and it is not clearly linked to the data before. A suggestion here would be to smooth the transition in the text and the authors could again perform a literature search regarding age-of-onset for CR/fasting interventions in mice and humans. __We have added a sentence to smooth the transition to these studies (lines 363-364). We had previously done a literature search to identify the age of onset of CR interventions in mice and humans. We summarise the findings of this search in lines 452-470 and 484-495 of the Discussion. We have also updated the source data so that it includes the our review of the CR literature, allowing other researchers to interrogate this data.

g) At the first mention of HOMA and Matsuda indices, the effect direction should be put into physiological context.

We now mention this in lines 231-232 of the Results.

h) There is no mention of how the PCA analyses were conducted.

We have updated the Methods to explain that the PCA analyses were done using R. We have updated the source data to include the outputs from these analyses, as well as the underlying code. These data and code are now available here https://doi.org/10.7488/ds/3758.

i) Were the mice aged in-house in the authors' facility or bought pre-aged from a vendor? Is it known how they were raised? If bought pre-aged, were female and male animals comparable?

We bred and aged all mice in house. Males and females were littermates from across several cohorts. Therefore, there are no concerns about lack of comparability resulting from environmental differences.

j) Very minor note: I think that "focussed" has become very rarely used, even in British English. I don't know about the journal's language standards, but I would switch to the much more common "focused".

We have updated to ‘focused’ as requested.

k) Figure 6B/F (PCAs) should indicate the % difference of each dimension.

We have updated the figures to show the % variance accounted for by each principal component. We have also updated the figure legend to specify this.

l) Limitations section: Maybe tone down on "world-leading mass spec facility". This sounds like an excuse and this statement is unsupported and doesn't add anything valuable to the section. Other limitations would include the low n, as mentioned above and the mono-centric fashion of the mouse and human experiments.

We have addressed these points as follows:

• Toned down the description of our mass spec facility (they are renowned for expertise in steroid hormone analysis, so we our original text was intended to highlight that our facility are not novices for this).
• Regarding the low n for some of the human groups, we now highlight this on lines 744-745 of the Discussion.
• We have added a new paragraph to the Discussion (lines 710-719) explaining the limitations of our CR protocol, i.e. that includes elements of both CR and intermittent fasting. Reviewer 2:

__Point 1: This is a very well written paper. __We thank the reviewer for this kind comment.

__Point 2: Since the authors fed the animals in the morning, this is likely the reason for energy expenditure to be different in the CR vs ad lib groups. Although the authors do study the effects of night v day feeding and saw no change in the outcomes regarding weight, this fact I think should be mentioned somewhere. Also, figure 4A is expressed a W while all the other graphs are in kJ. I think it would be nice to see it all consistent. __Regarding the first point, we agree that time of feeding can influence when energy expenditure is altered, but most studies show that CR decreases overall energy expenditure regardless of time of feeding. For example, Dionne et al studied the effects of CR on energy expenditure, administering the CR diet during the night phase (Dionne et al., 2016). They found that CR mice have lower energy expenditure in the day but not in the night (Figure 3C in their paper), which is the opposite to our findings (Figure 4C). However, total energy expenditure in their study remains decreased with CR. This goes against the reviewer’s suggestion that feeding the animals in the morning “is likely the reason for energy expenditure to be different in the CR vs ad lib groups”. We have updated our manuscript (Lines 576-581) to clarify this.

Regarding the second point, we have updated Figure 4A to express the data in kJ (showing the average kJ, per hour, at each time point). The figure legend has been updated to reflect this.

__Point 3: For all the graphs, can you make the CR groups bold and not filled as it is hard to see the lighter colours. __We have updated the graphs so that the CR groups are represented by solid lines, rather than dashed lines.

__Point 4: I know many investigators use them, but I am not sure how relevant HOMA-IR and the Matsuda index are in mice since they were specifically designed for humans. __The issue of whether it is ‘correct’ to use HOMA-IR and/or Matsuda index in mice is often debated in the metabolism field. Importantly, we are not using the absolute values for HOMA-IR or Matsuda in the same way that they are used in humans; instead, we are comparing the relative values between groups because these are still physiologically meaningful. We discussed this with Dr Sam Virtue, an expert in mouse metabolic phenotyping (Virtue and Vidal-Puig, 2021), who agrees on their usefulness in this way.

__Point 5: Something also to note is the fact that all the glucose uptake data is under basal conditions. Just because there are no differences in the basal state does not mean that there are no differences after a meal/during an insulin stimulation. I think that this needs to be discussed and the muscle and fat not completely discounted as a player in the differences seen. __We agree that CR can enhance insulin-stimulated glucose uptake but our OGTT data suggest that it is effects on fasting glucose, rather than insulin-stimulated glucose uptake, that contribute to the sex differences we observe. We have now updated the Discussion (lines 608-613) as follows, “CR enhances insulin-stimulated glucose uptake (82) and it is possible that this effect differs between the sexes. However, our second relevant finding is that, during an OGTT, CR decreases the tAUC but not the iAUC, highlighting decreases in fasting glucose, rather than insulin-stimulated glucose disposal, as the main driver of the improvements in glucose tolerance.”

References cited in Response to Reviewers:

Dionne, D.A., Skovso, S., Templeman, N.M., Clee, S.M., and Johnson, J.D. (2016). Caloric Restriction Paradoxically Increases Adiposity in Mice With Genetically Reduced Insulin. Endocrinology 157, 2724-2734. 10.1210/en.2016-1102.

Martin, A., Fox, D., Murphy, C.A., Hofmann, H., and Koehler, K. (2022). Tissue losses and metabolic adaptations both contribute to the reduction in resting metabolic rate following weight loss. Int. J. Obes. 46, 1168-1175. 10.1038/s41366-022-01090-7.

Oliva, M., Muñoz-Aguirre, M., Kim-Hellmuth, S., Wucher, V., Gewirtz, A.D.H., Cotter, D.J., Parsana, P., Kasela, S., Balliu, B., Viñuela, A., et al. (2020). The impact of sex on gene expression across human tissues. Science 369, eaba3066. 10.1126/science.aba3066.

Virtue, S., and Vidal-Puig, A. (2021). GTTs and ITTs in mice: simple tests, complex answers. Nat Metab 3, 883-886. 10.1038/s42255-021-00414-7.

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Referee #2

Evidence, reproducibility and clarity

Summary

This study was investigating sex and age in calorie restriction. In part 1 the authors reviewed the literature to see the percentage of papers that still only use males as their primary animal model, of which it is still the predominant sex being investigated although there are countries that have stipulated the importance of both sexes being involved and responses compared. In human studies, both sexes are often used, but not analysed separately to give sex differences.

In the second section, which was experimental, the authors report that sex does play an important role in the effects of 30% calorie restriction in mice with differences in both metabolic outcomes as well as in adipose tissue - with males responding and females not. Interestingly, this sex effect in mice was not found if the calorie restriction was started later in life, with both sexes responding, suggesting female sex hormones play and important role early in life in the resistance to calorie restriction. This finding was replicated in human studies, with females seemingly resistant to the weight loss effects or CR, especially in the younger age group.

Comments

1. This is a very well written paper
2. Since the authors fed the animals in the morning, this is likely the reason for energy expenditure to be different in the CR vs ad lib groups. Although the authors do study the effects of night v day feeding and saw no change in the outcomes regarding weight, this fact I think should be mentioned somewhere. Also, figure 4A is expressed a W while all the other graphs are in kJ. I think it would be nice to see it all consistent.
3. For all the graphs, can you make the CR groups bold and not filled as it is hard to see the lighter colours.
4. I know many investigators use them, but I am not sure how relevant HOMA-IR and the matsuda index are in mice since they were specifically designed for humans.
5. Something also to note is the fact that all the glucose uptake data is under basal conditions. Just because there are no differences in the basal state does not mean that there are no differences after a meal/during an insulin stimulation. I think that this needs to be discussed and the muscle and fat not completely discounted as a player in the differences seen.

Significance

Due to the lack of studies directly investigating sex and calorie restriction, I believe this is a very important manuscript.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In „The effects of caloric restriction on adipose tissue and metabolic health are sex- and age-dependent" the authors systematically studied the effects of sex and age on the response to sustained caloric restriction in mice and humans. The study was well performed and is a valuable addition to the literature. They found overlapping differences between the species when CR-data from mouse experiments and a small-scale clinical trial were stratified for sex and age. It appears that differences in the response to CR in young age in females compared to males depends on the hormonal status and is equalized in aged mice and humans. Since sex has played an underrated role so far in most studies on CR (especially in rodents), as the authors have laid out in their literature search, they make an important point.

Major comments:

• The clinical part is definitely the weak spot in the study. I don't think that the data should be omitted, but the authors should be very careful in interpreting the data. Obvious limitations apply to this part, which need to be more directly addressed in the abstract and discussion. It feels like the data from the small-scale clinical trial is exaggerated.
• It is important to mention in the abstract and the discussion that the human data came from obese participants. This might well influence the findings from human data.
• It is very important to calculate the % calorie restriction of the human participants achieved throughout the CR study. This is crucial information to compare it to other studies.
• Since there is quite a wide range in the BMIs of the participants, can the authors also stratify against BMI?
• There is no mention of any pre-study registration online of the clinical part (e.g. clinicaltrials.gov). Was this done?
• In the methods section the authors write "Participants were informed that the study was funded by an external commercial sponsor...". This is important information, and this is not mentioned anywhere else in the paper. Can the authors clarify this point? A commercial sponsor would, in my view, qualify for a conflict of interest that needs to be mentioned.
• How did the authors determine the group sizes for the clinical part? I have some doubts about the sub-group sizes. It would be valuable information if the authors had a statistical analysis plan prior conducting the study. It appears a bit, like the sub-groups were chosen at random, to match findings of the mouse data. Otherwise, there should have been a better allocation within the sub-groups (especially age).
• There's a big problem with the age stratification of the male participants in the clinical data. If I'm correct there are only 5 males <45 years. Although this looks intriguing, this can easily be a sampling problem.
• The applied protocol for CR in mice is known to provoke long fasting phases and probably elicits some effects through fasting alone, rather than the caloric deficit. There are some papers out addressing this (e.g. by deCabo, Lamming). The authors should not dismiss this fact and at least address it in their discussion. Also, given this fact, it would be thoughtful to include a database-search - not only regarding CR - but also regarding various types of intermittent fasting protocols in humans and animal studies (similar to what the authors did in the supplemental figure).
• Did the authors monitor the eating time of the mice?
• While CR certainly has a lot of health benefits in rodents and humans, it should be advised to raise the cautious note that it may not be beneficial for everyone in the general population. For some groups of people and in some cases (e.g. infectious diseases, pregnancy) even CR with adequate nutritional intake of micro/macronutrients might be disadvanteguous. This should be mentioned clearly, as the topic gets more and more "hyped" in public media and online.
• There is no indication of how the authors dealt with missing data. Statistically this can be very important, especially in cases with a low number of data points.
• Key data from qPCR should be followed up by western blots or other means. If this was done and there was no effect, the authors should report this. Also, is there any evidence or the possibility to support these findings regarding pck1 and ppara in human samples?
• I think it would be very valuable to analyse the sex-differences in lipolysis directly in fat tissues. The authors concentrated on differences in hepatic mRNA profiles, but there's an obvious possibility and gap in their story.
• Given the relatively low n and sometimes small effect sizes I fear that some of their findings won't be reproduced by other labs. Were the (mouse) data collected all at once in one cohort or did the authors pool data from different cohorts/repeats?

Minor comments:

• The discussion is very extensive, and I suggest compressing the information presented there to make it more easily readable.
• There is some confusion present in the literature regarding the nomenclature of CR/fasting interventions. Recently some reviews have summarized the different forms (e.g. Longo Nature Aging, Hofer Embo Mol Med, ...) and the authors should address this briefly. Especially the applied CR intervention in mice overlaps with intermittent fasting.
• The order of the subpanels in Figure 9 (and other figures where B is below A and so on) is confusing. Please rearrange or indicate in a visual way which panels belong to each other.
• Did the authors also measure cardiovascular (e.g. blood pressure) parameters? There is some evidence out there that there is an age/sex dependency during fasting/CR. This would be a nice add-on to the rather small clinical data here.
• What was the decision basis for stratifying the human data into < and >45 years?
• The part on aging starting in Figure 7 comes quite surprising and it is not clearly linked to the data before. A suggestion here would be to smooth the transition in the text and the authors could again perform a literature search regarding age-of-onset for CR/fasting interventions in mice and humans.
• At the first mention of HOMA and Matsuda indices, the effect direction should be put into physiological context.
• There is no mention of how the PCA analyses were conducted.
• Were the mice aged in-house in the authors' facility or bought pre-aged from a vendor? Is it known how they were raised? If bought pre-aged, were female and male animals comparable?
• Very minor note: I think that "focussed" has become very rarely used, even in British English. I don't know about the journal's language standards, but I would switch to the much more common "focused".
• Figure 6B/F (PCAs) should indicate the % difference of each dimension.
• Limitations section: Maybe tone down on "world-leading mass spec facility". This sounds like an excuse and this statement is unsupported and doesn't add anything valuable to the section. Other limitations would include the low n, as mentioned above and the mono-centric fashion of the mouse and human experiments.

Significance

The authors have analysed in great depth the importance of age and sex on the outcomes of CR on fat tissue, body weight and glucose homeostasis. It is a valuable and important contribution to the field. However, some points need to be clarified and some additional analyses/experiments should be performed. The piece will elicit great interest in the scientific and public readership. The authors have collected important evidence that the majority of CR studies in the literature have a drastic sex-bias in both mice and humans. This may be one reason why translational and mechanistic findings from mice to human application have been haltered in the field of nutritional healthy-aging-promoting interventions.

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Referee #3

Evidence, reproducibility and clarity

The Drosophila oocyte is a classical model to study establishment of cell polarity, and it is known for decades how Bicoid and Oskar define the anterior-posterior axis of the embryo. However, Bicoid and Oskar are not conserved so that these findings cannot be generalized. The situation is different for the Par proteins, which have been identified in C. elegans. They are not only conserved but also their mode of of action seems to be preserved. 20 years ago it was a very surprising finding that the Par proteins contribute to establishment of polarity in the Drosophila oocyte. A fascinating and simple mutual inhibition model emerged over the years, in which the same molecular mechanisms establish cell polarity in the C. elegans one-cell embryo and in the Drosophila oocyte: Anteriorly localised Par-3/Bazooka recruits aPKC kinase, which excludes Par-1 by phosphorylation, whereas posteriorly localised Par-1 kinase excludes Par-3/Bazooka by phosphorylation. The manuscript by Milas et al. challenges this model by closely analysing Par localisation in living Drosophila oocytes. The authors provide strong evidence that the kinetics of Par-1 and Bazooka localisation are not consistent with the model.

Milas et al. first describe a morphological difference between the anterior-lateral and posterior cortex of the oocyte by showing that only the posterior cortex is tightly connected to the overlaying epithelium. This morphological difference correlates with the localisation of Par-1, which is restricted to the posterior, while Bazooka localises only to those regions of the cortex, where there is a gap between the oocyte and the epithelium. This gap expands towards the posterior cortex during stage 10A and encloses it at stage 11. Unexpectedly, Par-1 and Bazooka localisations overlap at the posterior cortex when the gap expands, which contradicts the mutual inhibition model. The authors hypothesised that the close contact of epithelium with the oocyte might influence Par-1/Bazooka localisation. To test this they mechanically detached the epithelium from the oocyte and also ablated groups of epithelial cells. These manipulations resulted in posterior spreading of Bazooka protein within 30-60 minutes. Interestingly, the authors found that in those regions of the posterior cortex, where cells have been ablated, Par-1 and Bazooka colocalise for 30 minutes, which is difficult to reconcile with a model in which Par-1 excludes Bazooka by phosphorylation. The authors also show that Par-1 finally disappeared form the regions where epithelial cells have been ablated. However, aPKC, the kinase that is supposed the exclude Par-1 by phosphorylation, appeared only after Par-1, which argues against the idea that aPKC prevents Par-1 localisation. In summary, the described localisation kinetics are in conflict with the current model, in which direct phosphorylation activities of Par-1 and aPKC orchestrate the mutual exclusive Par domains in the Drosophila oocyte. The data suggest that the mechanisms underlying mutual inhibition are more complex than thought and involve contact with posterior epithelial cells.

The microscopy used by the authors is state of the art, the data are of high quality and the quantitative analysis is convincing. The results are surprising but conclusive since the experiments were performed and presented in a professional way. This combination makes the manuscript very interesting.

Major points:

1. The finding that the posterior cortex is in close contact to the epithelium, while there is a gap between the remaining oocyte cortex and the epithelium is very interesting, and should be quantified and characterised more precisely. When does the gap form and how exactly does it spread posteriorly? Is it possible to distinguish the gap from the attachment zone by using markers for the ECM (e.g. viking-GFP) or adhesion proteins (e.g. Integrin)?
2. The authors suggest that direct contact between the epithelium and the oocyte is required to exclude Bazooka from the posterior oocyte cortex. The polar cells of the follicular epithelium have almost no contact to the oocyte. One would expect that if only the polar cells are ablated, this would not lead to posterior spreading of Bazooka. Such a control experiment could support the author´s model.

Minor points:

1. There are repeatedly double negations which make the text difficult to understand (e.g. "Bazooka exclusion was lost...." (line 104) or "Par-1 does not delocalise from the posterior pole prior to accumulation of Bazooka" (line 163). I see that this follows the logic of the published molecular mechanisms but for the sake of comprehensibility, the authors should try to formulate the results in a positive way (at least in a repeating sentence).
2. Based on the kinetics of Par-1 localisation the authors the conclude that Par-1 binds to diffusible binding sites at the oocyte cortex, which are modulated by posterior epithelial cells. This is one possible explanation for their results but other interpretations are equally possible. Since the authors provide no further evidence for the existence of Par-1 binding sites their interpretation should be formulated more carefully.
3. The authors should mention that they use the Par-1 isoform (N1S) which fully rescues the par-1 mutant phenotype (see Doerflinger et. al, Curr Biol, 2006). What is known about the rescuing activity of the Bazooka transgenes that were used in the manuscript?
4. In principle it is possible that the posterior spreading of Bazooka (after follicle cell detachment or ablation) is caused by premature ooplasmic steaming. However, the movies show that this is not the case. This should be stated in the text.

Significance

The Drosophila oocyte is a classical model to address the fundamental biological question of how cell polarity is established. The current model of mutual Par protein inhibition is a critical part of our understanding of cell polarisation, and was proposed to be conserved between flies and worms. In the case of Drosophila this model mainly relies on a combination of genetic and biochemical data. Milas et al. tested this model by using in vivo imaging, and found that the kinetics of Par localisation do not correspond to the existing model. This suggests that central aspects of the proposed mechanisms controlling mutual Par inhibition in the Drosophila oocyte are not conserved or not fully understood. The work makes therefore a surprising and important contribution to the understanding of cell polarity.

I work for many years on Drosophila oogenesis and my main interest switched from cell polarity to membrane trafficking.

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Referee #2

Evidence, reproducibility and clarity

This manuscript examines an important and unsolved question concerning the establishment of the polarity axis in the Drosophila oocyte, namely how the follicle cells located at the posterior of the egg chamber trigger a signal to the oocyte for its subsequent polarization. To address this question the authors, center their studies on the localization of PAR proteins which are distributed along the antero-posterior axis. They more specifically focus on the mutual exclusion of Par1 and Bazooka/Par3 (Baz)at the posterior of the oocyte. The signaling event from the posterior follicle cells toward the oocyte is an essential process however it remains unsolved despite numerous screening and genetic manipulation approaches, leaving open the possibility that classical signaling involving a diffusible ligand emitted by follicular cells with its receptor located at the plasma membrane of the oocyte, would not be applied here.

Here the authors are using original biophysical approaches to address whether signaling between the follicular cells and the oocyte would involve mechanical features.

The authors focus at the dual exclusion between Baz and Par1 between the stages 10 and 11. To specifically follow these two proteins in the oocyte without being disrupted by their expression in the follicle cells, they used the Gal4/UASp system to express Baz and Par1. They found that Baz accumulate again at the posterior of the oocyte at stage 10B following the loss of contact between the posterior follicle cells (PFCs) and the oocyte whereas Par1 is gradually lost at that position. By using a glass micropipette to aspirate and pull on the PFCs they observed a premature Baz accumulation at the oocyte posterior. Then, to spatially improve the targeted area in the PFCs, the authors use a pulsed UV lazer, and show that PFCs are required to locally maintain posterior exclusion of Baz. Using a similar setup, they show that similarly Par1 is eliminated at the oocyte cell cortex region that had been in contact with ablated PFCs. However, Par1, with a kinetic slower to the one of Baz, is never disappearing before Baz appearance. Although difficult to distinguish, the authors report that the disappearance of Par1 is locally connected by an increase in microtubules (see major points). Finally, upon PFCs ablation, the authors show that the posterior reappearance of Baz is followed by the appearance of aPKC. However, the reappearance of PKC is slower than the removal of Par1, suggesting that in this case Par1 is not removed by PKC.

The particularly interesting results of this work show that cellular contacts between PFCs and the oocyte are necessary to maintain Baz exclusion and Par1 localization. Furthermore, the ablation results suggest that individual PFCs are required to maintain local posterior exclusion of Baz. Overall it is an interesting observation, and most of the data are presented in a clean organized manner.

Major comments

1. The authors concentrate their studies on the distribution of Par3 and Par1 at the posterior part of the oocyte, mainly at stage 10 according to the images in the figures and movies. The involvement of Par3 and Par1 on polarized transport to the posterior pole of the oocyte has been well characterized previously between stages 7 and 9. The results of the authors are very interesting but they do not show that beyond the return of Baz and the disappearance of Par1 at the developmental stage they are looking at, the antero-posterior polarization and more particularly the localization of oskar in the posterior is affected. This is an important point as the authors propose that follicle cell contact maintains main body axis polarity. This would be possible by monitoring the impact of PFC ablation on the maintenance of oskar localization by tracking osk RNA with the MCP-MS2 system, or also by visualizing the staufen protein with a stau-GFP transgene.
2. The authors use the Jupiter protein fused to the cherry protein to track MTs. This is perfectly fine to highlight the cytoplasm in the oocyte and to outline the cell-cell contacts between the PFCs and the oocyte. However, with Jupiter-cherry the microtubules are not clearly detected in the oocyte in the data presented.This is a problem because the authors want to make an important point with the potential reappearance of microtubules in the oocyte while Par1 has disappeared in the vicinity of the destroyed PFCs. (Fig5). The authors should use another microtubule reporter that allows better detection of microtubules in the oocyte, Jupiter-GFP, EB1-GFP, Ensconsin MT binding domain (EMTB)-RFP.

Minor comments:

1. The stage of the oocyte is not always indicated, this is particularly the case with the Fig2 with the pulling experiment with a glass micropipette.
2. With the Fig 3E, to highlight the fact that the intensity of Baz increases very quickly after the removal of PFCs (1 mn) the authors should include an insert with a shorter time scale. The authors could also comment on the difference in velocity in baz reappearance when the ablation of PFCs includes or not polar cells.
3. In the discussion line 240, this is not myosin II but myosin V which anchored oskar mRNA at the posterior.
4. For the suppl figure 5, the n is not mentioned in the legend

Significance

Nature and significance of the advance and work in the context of existing literature

This manuscript examines an important and unsolved question concerning the establishment of the polarity axis in the Drosophila oocyte, namely how the follicle cells located at the posterior of the egg chamber trigger a signal to the oocyte for its subsequent polarization (Gonzalez-Reyes et al ; Nature 1995 ;doi: 10.1038/375654a0) and (Roth et al; 1995; Cell; doi: 10.1016/0092-8674(95)90016-0). To address this question the authors, center their studies on the localization of PAR proteins which are distributed along the antero-posterior axis. They more specifically focus on the mutual exclusion of Par1 and Bazooka/Par3 (Baz) at the posterior of the oocyte. The signaling event from the posterior follicle cells toward the oocyte is an essential process however it remains unsolved despite numerous screening and genetic manipulation approaches, leaving open the possibility that classical signaling involving a diffusible ligand emitted by follicular cells with its receptor located at the plasma membrane of the oocyte, would not be applied here. We still know little about the modalities of this signaling between the follicular cells and the oocyte necessary for the polarization of the latter. We know that the first sign of anteroposterior polarization in the oocyte is posteriorly the recruitment of Par1 and subsequently the elimination of Baz. However, we do not know the nature of this signaling. Furthermore, we do not know whether this signaling must be maintained in order to maintain the polarization of the oocyte and more particularly to maintain the localization of oskar RNA, the posterior determinant of the oocyte, Here the authors are using original biophysical approaches to address whether signaling between the follicular cells and the oocyte would involve mechanical features. Important results of this work show that cell contacts between PFCs and the oocyte are necessary to maintain baz exclusion and Par1 localisation. Furthermore, the ablation results suggest that individual PFCs are required to maintain local posterior exclusion of Bazooka.

Audience: These results will be of interest to those interested in the relationship between cell signaling and polarization in particular in a developmental context.

Reviewer's area of expertise: Cell polarity, microtubule-associated transport, oocyte development in Drosophila.

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Referee #1

Evidence, reproducibility and clarity

Summary

The formation of mutually exclusive domains of Partition defective (Par) proteins works as a foundation for establishment of cell polarity in a variety of cells. The Drosophila oocyte is a well-known model system to study mechanisms of the asymmetric distribution Par proteins. At stage 6/7 of oogenesis, an unknown signal the posterior follicle cells (PFC) induces the recruitment of the Par-1 kinase to the posterior cortex of the oocyte and the concomitant exclusion of aPKC/Par-6 from this region. By contrast, Bazooka (Par-3) remains at the posterior with Par-1 and only disappears from the posterior at early stage 9. Millas et al. investigate the nature of the PFC signal and whether PFC continue to play a role in keeping Bazooka away from the posterior after the original signal is received by the oocyte. They do so by following the distribution of Bazooka and other Par proteins in living oocytes after pulling away or ablating the PFC at various stages of oogenesis.

Major comments

1. Quality of live imaging Judging from the appearance of the polar follicle cells and the size of the follicle cells, the authors constantly have an issue with maintaining a steady focal plane during live imaging in most movies (Figure 2 and video1; Figure 3 and video 2; Figure 4 and video 4; Figure 5 and video 5, FigureS5 and video 6). The conclusions of the paper are based on measuring changes in fluorescence intensity at the oocyte posterior over time, and this will be undermined by a varying focal plane. Considering the bullet shape of the oocyte, imaging the posterior at different focal planes could also cause artefacts. Supplementary Fig 3D-E and video 3 (a control experiment) are examples where the focal plane did not drift.
2. Mechanical contact of PFC with the oocyte cortex causes the posterior exclusion of Bazooka and maintains oocyte polarity By physically pulling PFC away from the oocyte at stage 10b (Figures 1-2) the authors observed that in some oocytes Bazooka re-localises to posterior and concluded that it is a mechanical contact between PFC and the oocyte cortex that keeps Bazooka away from the posterior. Although this is an interesting observation per se, this is after the polarity of the oocyte has been defined (stages 6-9) and the posterior determinant, oskar mRNA has been localised. Could the authors do the same experiment at stages 6-9 to directly address whether the distance between the PFC and the oocyte cortex actually matters, considering that Bazooka remains at the posterior up to early 9 when the PFC and the oocyte are still at close contact?

The conclusion that the signal between PFC and the oocyte could be mechanical is only one of potential interpretations of the experiment. It still could be a short range/ non-diffusible biochemical signal that is sensitive to the distance between the PFC and the oocyte membrane. The authors do not provide any evidence for or against either interpretation. 3. Figure 5B is supposed to demonstrate that local loss of Par-1 at the posterior causes the re-growth of microtubules from this region. However, the data provided are not convincing. The accumulation of red vesicles at the posterior cortex 150 min post ablation does not look like a specific signal for Jupiter-mCherry-marked microtubules. Similar vesicles start to be visible in the neighbouring follicle cells at the same time.

Minor comments

1. In Figure 4A-C, it is not clear what area has been ablated
2. The authors should provide a simple 1-6 numbering for Video files

Significance

The observation that the PFC are required to maintain oocyte polarity at stage 9 is significant, but not very surprising, given the recent observation by Doerflinger et al that the posterior localisation of Par-1 requires continuous myosin activation, demonstrating that the antagonism between anterior and posterior Par proteins is not sufficient to maintain polarity once established. The authors must improve the quality of the live imaging to support this conclusion.

The conclusion that phosphorylation of Bazooka by Par-1 is not sufficient to exclude Bazooka from the posterior cortex is not novel (see Doerflinger et al 2010, 2022).

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Referee #3

Evidence, reproducibility and clarity

Comments for Butt et al This study examines the potential role of SHARPIN phosphorylation on cell migration. The role of the phosphorylation sites of SHARPIN, especially S146, is clearly shown by the expression of the mutant in various cell lines. However, the argument of the interaction with the Arp2/3 complex is relatively weak; only the FRET analysis in cells is shown. It would be good if the authors could include more mechanistic insights into the role of the phosphorylation of SHARPIN.

Table 1. the reason for the selection of S131 and S156 is not clear. Why the S165 and T170 were not studied?

The phosphorylation would be better confirmed by the antibody for the phosphorylation peptides. The possible phospho-mimic mutants, with the substitution to the acidic amino acid residues, would be better to be examined.

Significance

The potential role of SHAEPIN in the context of the current understanding of the cell migration machinery would be better to be described. Now the study only contains the mutant expression phenotype.

Referees cross-commenting

I agree with other reviewers and do not have other opinions. The three reviews appear to be reasonable.

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Referee #2

Evidence, reproducibility and clarity

In this paper, Butt and co-workers examine the role of SHARPIN phosphorylation in Ser146 as it controls diverse readouts related to cell motility. The main findings of the study are: SHARPIN is robustly phosphorylated by PKCalpha in vitro. Mass spectrometry and in silico approaches indicate that some of these sites may be genuinely phosphorylated in cells. Ser146 phosphorylation seems uninvolved in SHARPIN-mediated integrin inactivation but imitation of the non-phosphorylated state using a Ser to Ala mutant impairs SHARPIN interaction with Arp2/3. S146A and V240A/L242A mutations impair lamellipodia formation. S146E mutation has a much less pronounced effect on SHARPIN-Arp2/3 interaction and lamellipodia formation, being close to the effect of the wild type. The authors conclude, based on this, that the active form of SHARPIN is likely phosphorylated in Ser146. In 3D matrix invasion assay, CRISPR-mediated SHARPIN deletion decreased invasiveness in several tumor cell lines. Perhaps the most striking experiment is that the authors use SHARPIN-KO MDA-MB-231 cells reconstituted with GFP-SHARPIN, WT or 146A, in a xenograft model in zebrafish, and they see that only WT-expressing cells form distal clusters of tumor cells. This is an interesting paper that merits publication, but several issues need to be addressed.

1. Whereas the data are consistent and interesting, some points could be strengthened quantitatively. An example is the quantification of the invasion assays (Fig. 4), which is relatively crude (this reviewer has firsthand experience with these assays).
2. Does SHARPIN control actin polymerization in response to stimulation? For example, growth factors in the cells used, or PMA.
3. PKCalpha has been involved in the control of protrusion dynamics through its local effect on myosin II regulatory light chain (Asokan et al, 2014). Is PKCalpha actually phosphorylating SHARPIN in live cells? Are other kinases involved in vitro? This needs to be clearly and explicitly demonstrated.
4. SHARPIN phosphorylated in Ser146 locally at lamellipodia? This is a hard experiment that requires a phospho-specific antibody, but the subcellular localization of the effect may be critical towards explaining the relative importance and generality of this mechanism.
5. In the same vein, does SHARPIN S146E localize more readily to protrusions that Ser146A?
6. The inference that active SHARPIN is phosphorylated in Ser146 needs to be demonstrated formally for the story to be substantiated. One possible manner could be to immunoprecipitate the Arp2/3 complex and show that most of the associated SHARPIN is phosphorylated in this residue by mass spectrometry. Alternatively, the authors could pull down integrins and show that SHARPIN is not phosphorylated in this case, which is also suggested by their data.
7. The last piece of data is striking, but the xenograft nature of the experiment casts some doubt as to its significance. B16F10 cells similarly treated could be implanted in C57BL/6 mice to make a much stronger case.

Significance

The data presented here, if substantiated as indicated in the previous section, would constitute a significant addition to the state of the art. My enthusiasm for the story is curbed by the technical flaws (relatively minor) and conceptual gaps (more significant) stated above. My expertise is cell and molecular biology with focus on cytoskeletal-related cell motility.

Referees cross-commenting

I mostly concur with the revisions suggested by the other two reviewers. Reviewer #1 raises a significant point that needs to be addressed, which pertains to the overall levels of overexpression. Other than that, I stand by my review, which has many connection points with those of reviewers 1 and 3. I think this paper has been judged fairly and the experiments requested are not overly complicated. I understand if the authors cannot do the in vivo experiment in mice, and this alone should not be grounds for rejection. However, they need to address the rest of our points.

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Referee #1

Evidence, reproducibility and clarity

The SHARPIN protein is involved in multiple cellular pathways, and a number of studies demonstrated that it can interact with many key proteins regulating cellular proliferation, adhesion, motility and other functions that are important in normal cell physiology, but are particularly relevant for cancer metastasis. This study addresses post-translational phosphorylation of SHARPIN in human cells, and identifies two functionally important sites that are specifically involved in the interaction with ARP2/3, as well as in lamellipodia formation and cell motility (invasion). The function of one of these phosphorylation sites, the S146, is further explored in KD, KO and rescue experiments, in several human cancer cell lines, and in zebrafish model, using the directed mutagenesis approach to abolish or mimic the phosphorylation of S146. The authors conclude that Ph-S146 modification of SHARPIN is specifically responsible for interaction with ARP2/3, lamellipodia formation, and cancer cell invasion.

Major comments:

• Are the key conclusions convincing?

Overall, the conclusions are convincing, though the question of wild-type and mutated SHARPIN in rescue experiments should be addressed, given the functional importance of SHARPIN overexpression in cancer. Indeed, throughout the paper, the authors monitor the expression levels of their ectopically expressed SHARPIN, and systematically refer to these molecules as being "overexpressed", without showing their relative levels with regard to normal endogenous levels of SHARPIN in these cell lines, prior to its KD/KO. However, as the typical cancer-related functions of SHARPIN are linked to its expression levels, it is important to understand whether the observed phenomena can be regarded as physiologically relevant, or are the authors operating out of the physiological scale. Given the capacity of HeLa and 293 cell lines to produce very high levels of ectopic proteins, this issue should be systematically controlled. Therefore, in all the experiments with ectopic expression of SHARPIN and its mutants, a western blot should be added to show the relative expression, compared to the endogenous protein.

There are also some major problems with the statistical analysis (please see below). - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

I would modify the text of the article referring to Fig.2A, where the authors qualify a 20-25% reduction of integrin activity as "significant". It is not clear whether they refer to statistical or functional significance, and the statement is generally misleading. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

As mentioned previously, I believe that the expression levels of ectopic SHARPIN have to be systematically monitored in all assays, and compared to the normal, endogenous levels. - 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.

These experiments are fully realistic and should not involve additional costs. - Are the data and the methods presented in such a way that they can be reproduced?

There is some ambivalence about the "n" values in most of the experiments, where it is not clear at all what "n" means (the number of cells? Experimental points?) For example, in Fig.S1D, the legend states that n=1, whereas the panel shows three experimental points per condition, as well as error bars. I would suggest that the authors correct these obvious mistakes and explain more clearly what exactly "n" means, in each case. - Are the experiments adequately replicated and statistical analysis adequate?

I cannot comment on that because I do not understand what exactly "n" means (please see above). For example, if in Fig.3, "n=4" means that only four cells were analyzed per experimental condition, this is clearly not enough. The statistical analysis is not sufficiently described in the Materials and Methods section, and the reasons for attributing one, two or three stars to the results are not stated, either (normally, this information should be equally present in Legends to Figures). The choice of applying the t-test does not appear evident to me, in experiments that clearly require multiple statistical comparisons, and in general, the statistical analysis does not appear adequate.

Minor comments:

• Specific experimental issues that are easily addressable.

Please provide a clear gel for Fig.1A, especially the right-hand panel. The current results look as one big black spot, with two red frames added for no clear reason. - Are prior studies referenced appropriately?

I have no problem with the list of references. - Are the text and figures clear and accurate?

It will be a good idea to proof-read the text. For example, I have noticed a frequent use of the word "lamellApodia" instead of "lamellipodia", as well as other typing errors. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Molecular weight markers should be added to all western blots, and scale bars to all immunofluorescent images.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Given the functional importance of SHARPIN in cancer, and the fact that it interacts with multiple major regulatory networks, it is important to pinpoint the exact post-translational modification of this protein that is specifically responsible for interaction with ARP2/3, and for the invasion potential of cancer cells. - Place the work in the context of the existing literature (provide references, where appropriate).

I agree with the description of the field and the place of the current study that is provided in the manuscript, and do not have anything significant to add. - State what audience might be interested in and influenced by the reported findings.

The study will undoubtedly be interesting to scientists working with cell motility, ARP2/3-dependent lamellipodia formation, and eventually metastasis growth in cancer. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I study the RAC1-WAVE-ARP2/3 regulatory pathway in normal and cancer cells. I did not have any problems with evaluating this work, either academically, or with regard to methodology.

Referees cross-commenting

I am very pleased to see that the three reviews have a very similar evaluation of this article, and hope that the raised questions will help the authors to improve the manuscript and successfully publish their work. I do not have any additional comments.

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Reply to the reviewers

1. General Statements

We thank the reviewer for stating that “The detailed analysis uses many state of the art techniques to address the role of ROR1 and is of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic” and we appreciate the reviewer’s constructive suggestions. We have substantially revised our manuscript and plan to perform new experiments based on these valuable comments.

1. Description of the planned revisions

Three main points: (1) The importance of AURKB as a downstream effector of ROR1 [Reviewer #1: major #2] Based on these suggestions, we plan to perform a colony formation assay using AURKB-overexpressing cells with ROR1-knockdown. We will clarify this point in the revised manuscript.

(2) The link between ROR1 expression and YAP/BRD4 [Reviewer #1: major #5 and Reviewer #3: major #1] Based on the suggestion, we plan to perform the luciferase reporter assay. We will clearly describe this experiment in the revised manuscript.

(3) Single-cell analysis using other models to validate tumor heterogeneity [Reviewer #2: major #1 and Reviewer #3: major #2] Based on your suggestion, we plan to analyze primary human tumors (public data: for example, GSE155698, CRA001160) and examine PDO#1 xenografts (in-house data). We will clearly state this information in the revised manuscript.

For the two minor points suggested by Reviewer #2, we plan to (1) reanalyze TCGA data. (2) perform the organoid or colony formation assay to validate that the siRNA model functionally recapitulates the ROR1low vs. ROR1high phenotype.

Please see the “Authors’ responses to the reviewers' comments” for more details.

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

As suggested by the reviewer, we have substantially revised our manuscript, and the changes are shown in red. • Reviewer #1: major comments #2, #3, #4, and #5; minor comments #1 and #2 • Reviewer #2: major comments #2, #3, and #4; minor comments #2, #3, #4, #8, and #10 • Reviewer #3: minor comments #1 and #2

Please see the “Authors’ responses to the reviewers' comments” for more details.

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

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Authors’ responses to the reviewers' comments

Reviewer #1

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

In this manuscript the authors analyzed the role of ROR1 in pancreatic cancer progression and metastasis. They found that ROR1 expression is specifically increased in an partial EMT cell cluster upon scRNA-Seq of tumor cells derived from an orthotopic mouse PDAC model. Moreover, the ROR1 high population in tumors specifies cells with high proliferation and tumor initiation capacities, increased metastatic propensity and chemoresistance, since knockdown of ROR1 shows reduction of these features in vivo. By comparing transcriptomes from several in vivo models the authors identified that ROR1 acts through AURKB and that its expression is regulated by an upstream enhancer that is bound by YAP/TAZ and BRD4 complexes. With this study the authors identified a new targetable pathway that promotes tumor progression and metastasis in PDAC. The detailed analysis uses many state of the art techniques to address the role of ROR1 and is of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic. However, some of the findings are a bit preliminary and the drawn conclusions are not sufficiently supported by the experimental data. Moreover, some findings seem a bit out of context and do not really help to bring the story forward. At other instances experimental details are missing to mechanistically demonstrate the role of ROR1. In particular it remains elusive how ROR1 is regulated, i.e. which signaling events are crucial to generate ROR1 high vs. low cells. I listed my specific comments below.

[Response] We thank the reviewer for stating that “The detailed analysis uses many state of the art techniques to address the role of ROR1 and is of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic” and we appreciate the reviewer’s constructive suggestions. We have substantially revised our manuscript and plan to perform new experiments based on these valuable comments.

1. The authors' initial finding is that in the partial EMT cluster ROR1, but also other RTKs (out of 56) are specifically increased. What about the other RTKs? Why was ROR1 chosen to analyze more thoroughly?

[Response 1] We are thankful for the reviewer’s suggestion to clarify why ROR1 was selected. (1) Seven candidate genes (EPHA4, EPHA7, ERBB4, FGFR1, JAK3, LYN, and ROR1) were chosen as surface markers in the partial EMT cluster. (2) The genes were sorted in order of high expression. (3) ROR1 is reported to promote metastasis in breast cancer (Cui et al, 2013). The induction of metastasis is one of the functions of tumor-initiating cells. FGFR1 is already known to enhance the CSC-like phenotype in non-small cell lung cancer (Ji et al, 2016). (4) The antibody against ROR1 was marketed as available for cell sorting using FACS. Therefore, we focused on ROR1 as a potential new marker for tumor-initiating cells with a partial EMT signature.

References Cui B, Zhang S, Chen L, Yu J, Widhopf GF 2nd, Fecteau JF, Rassenti LZ, Kipps TJ. Targeting ROR1 inhibits epithelial-mesenchymal transition and metastasis. Cancer Res. 2013 Jun 15;73(12):3649-60. doi: 10.1158/0008-5472.CAN-12-3832. PMID: 23771907; PMCID: PMC3832210. Ji W, Yu Y, Li Z, Wang G, Li F, Xia W, Lu S. FGFR1 promotes the stem cell-like phenotype of FGFR1-amplified non-small cell lung cancer cells through the Hedgehog pathway. Oncotarget. 2016 Mar 22;7(12):15118-34. doi: 10.18632/oncotarget.7701. PMID: 26936993; PMCID: PMC4924774.

1. The finding of AURKB as crucial target of ROR1 is very weak and needs more in-depth analyses. It is not clear why AURKB was chosen over the other candidates. Is AURKB expression directly regulated by ROR1? Are the two genes directly linked? Can ROR1 deficiency be compensated by AURKB overexpression? Especially the decrease in AURKB protein level in Fig. 4K is not very convincing to account for the different phenotypes in ROR1 high and low cells. Is AURKB and ROR1 expression correlated in TCGA samples (like Fig. 8B)? In Fig. 4L the readout was changed from colony numbers to colony diameter. If AURKB is the crucial player downstream of ROR1, then colony formation efficiency should be affected at first. This needs to be shown. The statement in lines 223,224 that AURKB is a direct downstream target of ROR1 was not shown!

[Response 2-1: changed] We thank the reviewer for noting this issue. We have performed additional experiments to assess the hypothesis that AURKB is a crucial downstream target of ROR1. ROR1-knockdown not only suppressed AKT phosphorylation (Supplemental Figure 9A) but also decreased c-Myc protein levels and the expression of c-Myc target genes (CDK4, CCND1, CDK2, and CCNE1), leading to a reduction in RB phosphorylation (new Supplemental Figure 9B and 9C). Based on these results, ROR1 regulates c-Myc expression through AKT signaling, leading to the activation of the E2F network (new Supplemental Figure 9D). We added some figures and descriptions to the preliminary revision manuscript (new Supplemental Figure 9B–9D, lines 357–363, lines 649–651).

[Response 2-2: the planned revisions] We also plan to perform new experiments with a colony formation assay to determine whether ROR1 deficiency is compensated by AURKB overexpression. We agree that this experiment will confirm that AURKB is an important downstream target of ROR1 in PDAC proliferation.

[Response 2-3] In TCGA-PAAD dataset, AURKB expression was not correlated with ROR1 expression. Since the ROR1high cluster is a minor population in the tumor, a downstream analysis of specific clusters with results from a bulk study such as this TCGA dataset is difficult to perform.

[Response 2-4: changed] We have added a new graph of organoid formation efficiency (new Figure 4L) and changed some descriptions in the preliminary revision manuscript (line 227).

1. Fig. 4 A-E: The ROR1 KD was induced in vitro but not continued in vitro. The transient KD has a strong impact on tumor forming capacity, even though recovery of expression is likely within the first days in vivo. This is very interesting and underscores the role of ROR1 in tumor initiation and presumably independent of differences in proliferation. Would the results be different, if the DOX treatment would start with injection of the cells and continued in vivo? Is then tumor initiation not affected and maybe only tumor growth?

[Response 3: changed] We apologize for the confusing description in the original manuscript. In Fig. 4A–E, we used PDAC cells with stable expression of doxycycline-inducible shROR1. ROR1-knockdown was maintained in vivo by adding doxycycline to the drinking water. Continuous ROR1-knockdown suppressed tumor growth (Fig. 4C–E). Several statements we made were more ambiguous than intended, and we have adjusted the text and the figures for clarity in the preliminary revision manuscript (new Figure 4A and B, lines 203–204).

1. In Fig. 5 the authors show that ROR1 is highly expressed in tumors after gemcitabine treatment and conclude that the ROR1 high cells are a resistant population. However, this statement is too strong, since gemcitabine treatment could also lead to an upregulation of ROR1 in "low" cells during acquisition of chemoresistence. Together with our knowledge on the role of EMT in driving therapy resistance and therapy-mediated induction of EMT, such a scenario is equally likely. Similarly, the statement in lines 370-372 is not supported by experimental evidence.

[Response 4: changed] We appreciate the reviewer’s critical comments. As suggested, we have not clearly determined whether (1) the ROR1high cells survived gemcitabine treatment and/or (2) the ROR1low cells increased ROR1 expression upon exposure to this treatment. We have carefully changed some descriptions in the preliminary revision manuscript (lines 241–242, 382–383).

1. In order to understand how ROR1 is regulated, the authors use ATAC-Seq and cut and run and identified a putative upstream enhancer element (Fig. 7). Although this element increases the activity of the promoter fragment in a reporter construct, the experiments do not help to understand how ROR1 activity is increased specifically in the "high" cells. Are peaks of YAP1 and BRD4 also changed between hi/lo cells? Is YAP OE and KD (BRD4 OE and KD) or the use of the inhibotor JQ1 altering the activity of the reporter constructs (i.e. only of the enhancer-promoter combination but not of the promoter only construct)? This would help to strengthen a direct link between ROR1, YAP and BRD4. Is YAP activity different in ROR1 high vs. low cells?

[Response 5-1: changed] We thank the reviewer for this important comment. We have shown differences in chromatin accessibility and histone modification of the ROR1 enhancer between ROR1high and ROR1low cells using ATAC-seq and CUT&RUN assays (Fig. 7B). Very few ROR1high/low cells are present in xenograft. We were not successful in experiments examining the binding of YAP and BRD4 to enhancers in ROR1high/low cells because of the technical limitations in the ChIP and CUT&RUN assays. Instead, we used public data to examine YAP and BRD4 occupancy at the ROR1 enhancer region of cell lines with low ROR1 expression. In T-47D and MCF7 cells (breast cancer cells, low ROR1 expression), YAP and BRD4 did not bind to the ROR1 enhancer region (new Figure 8D and 8I). We have added figures and some descriptions to the preliminary revision manuscript (new Figure 8D and 8I, lines 304–309, line 768).

[Response 5-2: the planned revisions] We plan to perform new experiments with the reporter assay you suggested. We agree that this experiment will help strengthen the direct link between ROR1, YAP and BRD4.

[Response 5-3] As shown in Figure 8C, GSEA revealed that ROR1high cells in both S2-VP10 xenografts and PDO#1 xenografts expressed higher levels of YAP-regulated genes than ROR1low cells in these xenografts. We have added a description of this result as follows: “Thus, ROR1high cells have higher YAP activity than ROR1low cells.” (lines 304–305).

1. In Fig. 8A the authors identified 202 antigens that match the H3 monomethylation / acetylation pattern. How was YAP etc. chosen?

[Response 6] We apologize for the poor description in the original manuscript. We chose YAP and BRD4 based on the following criteria: (1) these antigens are expressed in S2-VP10 cells and PDO#1 and (2) bind to the ROR1 enhancer region (based on an analysis of public data).

Minor: 1. Fig. 2D,E: What is actually shown here? Is there an overlap between the genes that define ROR1 high vs. low cells in both approaches? The gene list should be provided.

[Response: changed] We apologize for the poor description in the original manuscript. We have added this information to the preliminary revision manuscript (new Supplemental Table 3).

1. Fig. 3G: I suggest to include the images of the tumors from the ROR1 low cells in the main figure as well.

[Response: changed] We appreciate the reviewer’s suggestion. We have moved this information from the supplementary information to the main figure in the preliminary revision manuscript (new Figure 3G, lines 186–189).

Reviewer #1 (Significance (Required)):

PDAC is a very aggressive desease with very low 5-year survival rates. Understanding of the pathobiology is of keen interest. The findings of the authors are of high significance and extremely relevant as they provide a mechanism that can also be targeted by specific drug combinations, i.e. standard care gemcitabine with specific ROR1 inhibition. The findings are of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic.

[Response] We greatly appreciate the reviewer’s comments.

Reviewer #2

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

In this work Yamazaki and colleagues performed single cell RNA sequencing of one xenograft tumor formed by the S2-VP10 PDAC cell line to explore PDAC intratumor heterogeneity. Using this model they identified ROR1 as heterogeneously expressed in neoplastic cells. Using further in vivo and in vitro models they show that ROR1high cells have higher tumor initiation capacity than ROR1low. By histone and ATAC-seq analyses, they identify a ROR1 enhancer upstream the promoter and show that YAP and BRD4 bind to this genomic region and that BRD4 inhibition by JQ1 reduces ROR1 expression and organoid formation. The data, figures and methods are nicely and clearly presented.

[Response] We thank the reviewer for stating that “The data, figures and methods are nicely and clearly presented”, and we appreciate the reviewer’s constructive suggestions. We have substantially revised our manuscript and plan to perform new experiments based on these valuable comments.

Major comments

1. The authors use one xenograft tumor as starting model and all conclusions are derived from the data generated with this model. To support the existence of identifie heterogeneity in the PDAC neoplastic compartment, I would strongly suggest to validate the existence of the partial EMT population and the ROR1 heterogeneity in single cell data bases generated from primary human tumors.

[Response 1: the planned revisions] We thank the reviewer for the positive suggestion. We plan to perform a new analysis of available public single-cell data from human PDAC tumors. In addition, we also launched a single-cell analysis of PDO#1 xenografts.

1. In Fig. 3G, it is mentioned that tumors grown from ROR1high cells recapitulate the original PDOx histology thus suggesting that ROR1high cells in the tumor are the actual TICs. ROR1low cells could also grow tumors, just with lower incidence. Are these tumors any different to the ROR1high derived ones? Is it just a lower tumor initiation capacity (TIC) or they can not recapitulate the tumor as the ROR1high cell? Can they also give rise to differentiated progeny cells? This should appear in the main text and not only in the discussion. I would suggest to move panel 3G to supplementary figure.

[Response 2: changed] We thank the reviewer for noting this issue and apologize for the confusing description in the original manuscript. ROR1low cells generated tumors at a low frequency, and these tumors showed a hierarchical histology mimicking the original tumor. As suggested, we have added this information to the main text (new Figure 3G, lines 186–189).

1. In line 160 you mention that known CSC markers such as CD44, PROM1 and DCLK1 are not differentially expressed between ROR1 high and low populations. Then, in figure 3H,I you analyze the expression of CD44v6 together with ROR1. I would try to put this information together in the text, or at least in fig. 3 start with something like "we had seen that both ROR1high and low express CD44, however...". In any case, I feel that the experiment with CD44 could be obviated (or at least moved to supplementary), as it brings the question of weather this is also true for DCLK1 or CD133.

[Response 3: changed] We appreciate and agree with the reviewer's comment on this point. Accordingly, we have moved this figure to the supplementary information and changed the description (new Supplemental Figure 5C and 5D, lines 191–196).

1. JQ1 has been described to inhibit PDAC growth by downregulation of MYC. To unequivocally link the effect of JQ1 in the downregulation of ROR1 (Fig. 8M) as discussed in the text it would be important to exclude that other mechanisms such as MYC downregulation are taking place. For example, does JQ1 treatment of ROR1low cells also reduce their colony formation capacity (in an experiment such as the one in fig. 3C). Or does ROR1 re-expression in Fig. 8M rescue the JQ1 effect? These or other experiments could help to establish a stronger link between (BRD4/JQ1) and ROR1.

[Response 4: changed] We thank the reviewer for this important comment. As mentioned in the response to Reviewer #1-major comment #2, we newly found that ROR1 regulates c-Myc expression through AKT signaling, leading to the activation of the E2F network (new Supplemental Figures 9B–9D, lines 357–363).

Minor comments 1. The data are nicely presented (text and figures) and the conclusions are clear. My suggestion to make the story more "catchy" at the beginning would be, if possible, to start from the observation done in primary human data and then move to the PDX model to explore ROR1 as a TIC marker in PDAC. For this, you could use available public single cell data of human PDAC tumors. If this doesn't work (it is of course possible that by unsupervised analysis you don't get the same clusters as in the PDX with the partial EMT cluster popping up), it would be nice if some primary tumor data came early in the story (currently the first figure showing heterogeneity in primary samples is in supplem fig. 4A).

[Response: the planned revisions] We thank the reviewer for these excellent comments. As suggested, we plan to perform several new analyses (please see the previous comment for details: Reviewer #2-major comment #1).

1. It is not clear if the xenografts were subcutaneous or orthotopic. It would be good to include this information in the main text (line 102) and the methods so that the reader knows what is the exact model that has been used.

[Response: changed] We thank the reviewer for this comment and apologize for the poor description in the original manuscript. As suggested, we have added this information to the preliminary revision manuscript (line 101).

1. In Fig. 2F and 2G I would highlight the EMT pathway to help the reader.

[Response: changed] We thank the reviewer for this comment. As suggested, we have changed the relevant figures in the preliminary revision manuscript (new Figure 2F and 2G).

1. In Supp Fig 4B it would be nice to have an amplified view of the staining as in panel C of the same figure.

[Response: changed] We thank the reviewer for this comment. As suggested, we have added high-magnification images of the staining in the preliminary revision manuscript (new Supplemental Figure 4A and 4B).

1. In the same figure (Fig. 4A-D) ROR1 shows an apical staining pattern that doesn't seem to resemble the staining in patient samples. I am not an expert in pathology evaluation but I would recommend a pathologist to give her/his opinion. Possibly, during the PDX process, few cells from the original patient tumor are selected giving a different staining pattern.

[Response] We appreciate the reviewer's comment on this point. Dr. Ito, a coauthor of this paper, is a pathologist. We have changed some images of staining in patient samples (new Supplemental Figure 4A). We agree that ROR1 shows an apical staining pattern in PDX samples. However, some sites show similar apical staining patterns in patient samples (Patient #2 and Patient #4 in the new Supplemental Figure 4A). We propose that PDX mimics the original patient tissue because it has heterogeneity of ROR1 expression and morphological features indicative of a luminal structure.

1. In the analyses of TCGA data, be aware that only 150 from the original dataset are actual PDAC tumors. The dataset contains otherwise data from cell lines, PDX, normal tissue, etc that should be removed for a proper analysis (see DOI: 10.3390/cancers11010126)

[Response: the planned revisions] We thank the reviewer for the careful review of this issue. We are currently reconsidering with the pathologist whether the samples are appropriate based on TCGA data (diagnosis and pathology sections) and the paper you presented. The current data (Figures 3A, 4J, and 8B) were analyzed for samples excluding cell lines, PDX, and normal tissue in the TCGA-PAAD dataset.

1. Does ROR1 correlate with RFS? This would nicely fit with the concept of TIC and metastasis.

[Response] We thank the reviewer for noting this issue. Unfortunately, no correlation was observed between ROR1 expression and RFS.

1. Line 219: ROR1 is not "depleted" in the lines as it is a downregulation model. "ROR1-downregulated" would be more correct.

[Response: changed] We thank the reviewer for this suggestion and agree with your comment. We have corrected this term accordingly in the preliminary revision manuscript (line 223).

1. It would be good to have a supplem figure showing that siROR1 cells show reduction organoid formation, to validate that the siRNA model functionally recapitulates the ROR1low vs high phenotype.

[Response: the planned revisions] We thank the reviewer for this suggestion. We plan to perform a colony formation assay.

1. Some of the supplemental figures are only referred in the discussion although they appear earlier than other in the main text. This is a bit confusing when going through the figures.

[Response] We apologize for the poor description in the original manuscript. We have adjusted the order of the supplemental figures in the preliminary revision manuscript.

CROSS-CONSULTATION COMMENTS I agree with the importance of addressing points 2 (link to AURKB), 4 (selection vs acquisition), 5 (mechanism in high vs low cells) raised by Reviewer 1, and the comments from Reviewer 3. I think that the study of other RTKs (point 1 from Reviewer 1) is not the focus of the story. It would be nice if the authors can comment on why they chose ROR1 but the fact that are other differentially expressed genes does not exclude the validity of the current story. I fell that the in vivo sustained KD experiment (point 3 from Reviewer 1) although interesting, it is not mandatory for a revision of this manuscript in case the adaptation of the animal protocol represents a long process. The experiment provided already in the current version is the best approach to address the role of ROR1 at the early initiation phase.

[Response] We thank the reviewer for these positive comments. As suggested, we have substantially revised our manuscript.

Reviewer #2 (Significance (Required)):

Significance: This is a neat and interesting work with potential implications for the clinical field of pancreatic cancer as the authors identified a new subpopulation with enhanced tumor initiating cell capacity. However, the use of JQ1 for pancreatic cancer has been previously discussed mainly linked to MYC inhibition, but also to stromal reprogramming or DNA damage induction. I missed some discussion in this regard in the discussion section. What is adding the work to the field of JQ1 treatment in PDAC? IN a way, how do the authors foresee that the discovery of ROR1high cells and the regulation of ROR1 by BRD4 and YAP will be beneficial when considering JQ1 in the clinics? Maybe by stratifying patients? Or by following ROR1 upregulation upon initial chemotherapy? These questions are just suggestions. In general, some discussion to put the work into the context of previous works using JQ1 in PDAC would be nice.

[Response: changed] We thank the reviewer for this comment. As you suggested, we have added a description of the proposed use of JQ1 and BRD4 inhibitors in ROR1high PDAC treatment to the Discussion section (lines 412–416).

I believe that this work would be interesting not only to the pancreatic cancer community but also to a more general public working on cancer and/or stemmness as it touches several interesting points in that regard that can be applicable to other systems. My own work is focused on pancreatic cancer, patient heterogeneity and stromal interactions. I am not an expert on histone or ATACseq analyses.

[Response] We greatly appreciate the reviewer’s comments.

Reviewer #3

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

Summary Yamazaki et al investigate partial EMT in pancreatic cancer and provide data that ROR1 marks pancreatic tumor cells that are capable of initiating tumors. The authors exploit scRNAseq of pancreatic tumor xenografts to identify a cluster of cells showing a partial EMT phenotype. The found 7 RTKs expressed more highly in this partial EMT cluster and focus their attention on ROR1, an 'orphan' receptor that has been implicated in WNT signaling and EMT previously. Validation experiments using ROR1-high vs low cells support that ROR1 expression correlates with EMT, poor outcome in human PDA patients, tumor forming and colony forming capacity. They also show that ROR1 high cells form tumors that recapitulate parental tumor histology. The authors show that ROR1 expression is associated with EF2 transcription factor activity, elevated expression of multiple targets including AURKB. Pharmacologic inhibition of AURKB reduces colony formation and genetic loss of ROR1 combined with chemotherapy (gemcitabine) has potent anti-tumor activity in vivo. The authors show that ROR1 expression is elevated in metastatic lesions and identify a novel enhancer element that putatively drives ROR1 expression in tumor cells. They provide evidence that this element is engaged by YAP/BRD4 and show that BRD4 inhibition reduces tumor cell colony formation. The manuscript is a solid combination of techniques with adequate controls and statistics.

[Response] We thank the reviewer for stating that “The manuscript is a solid combination of techniques with adequate controls and statistics”, and we appreciate the reviewer’s constructive suggestions. We have substantially revised our manuscript and plan to perform new experiments based on these valuable comments.

Major Comments: The overall conclusion that ROR1 expression marks a subset of pancreatic cancer cells that have the ability to initiate tumors is supported by the data provided. The correlative data are strong and the demonstration that loss of ROR1 reduces colony formation, reduces metastatic lesions and enhances the efficacy of chemotherapy are compelling. Additionally, the demonstration that ROR1 expression is elevated in metastatic lesions is consistent with many other drivers/markers of EMT in pancreatic cancer.

The conclusion that ROR1 expression is driven by YAP/BRD4 is interesting and provides important mechanistic depth to the study. However, this conclusion could be strengthened by use of a suitable rescue experiment. For instance does overexpression of ROR1 rescue the effect of BRD4 inhibition or loss of YAP?

[Response 1: the planned revisions] We thank the reviewer for this comment. We completely agree with the reviewer’s suggestion. However, the suggested examination to determine whether overexpression of ROR1 rescues the effect of BRD4 inhibition or loss of YAP may not be suitable because BRD4 and YAP act as transcriptional coregulators of various target genes. Instead, as mentioned in response to Reviewer #1-major comments 5-2, we plan to perform new experiments using a reporter assay.

A challenge with the data presented in Figure 1, the scRNA-seq data that lead them to ROR1, is that it is not stated how many tumors are used to generate the scRNA-seq data and the overall number of tumor cells analyzed is relatively low (993). The authors should provide the number of tumors used for the initial scRNA-seq. A general concern with any scRNA-seq data is batch effect, this is mitigated to a degree by the follow on studies that provide functional validation of ROR1 in multiple cell lines.

[Response 2: changed and the planned revisions] We appreciate the reviewer’s comments. As suggested, we have added this information to the preliminary revision manuscript (line 104). In addition, as mentioned in response to Reviewer #2 major comment #1, we plan to perform a new single-cell analysis of PDO xenografts (in-house data) and human PDAC tumors (available public data).

The data and methods are provided in an adequate manner. Reproduction of the experiments is likely. The authors use multiple cell lines and tools that are generally available. The authors note a limitation of the study is that only human tumor xenografts were exploited.

[Response] We thank the reviewer for the positive comment.

Minor comments: Figure 1E and text page 9. The text identifies MERB3 as a gene that marks the partial EMT cluster, I believe this is a type and the gene should actually be MSRB3.

[Response: changed] We apologize for the typo. We have corrected this error accordingly (line 114).

Please provide the dose of gemcitabine in the legend for figure 5

[Response: changed] We apologize for the poor description in the original manuscript. We have added this information.

CROSS-CONSULTATION COMMENTS I think the comments from Referee #2 are pretty reasonable - have no additions

Reviewer #3 (Significance (Required)):

Intratumor heterogeneity is a major challenge for the treatment of many cancers, including pancreatic cancer. The data provided support that ROR1 marks a subset of cancer cells in pancreatic tumors that have the capacity to drive intratumor heterogeneity. If supported these data have the potential to drive significant impact. Identification of a marker and a targetable pathway that supports tumor initiation in pancreatic cancer has the potential to nominate companion therapies that enhance the efficacy of standard of care approaches. Further, identification of a pathway that drives partial EMT in pancreatic cancer provides a substantial increase in baseline knowledge of intratumor heterogeneity.

These data would be broadly interesting to scientists interested in the tumor microenvironment, metastasis, therapy resistance and tumor progression. In addition, oncologists focused on drug development and combinatorial therapy will find this manuscript of interest.

[Response] We greatly appreciate the reviewer’s comments.

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

Learn more at Review Commons

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Referee #3

Evidence, reproducibility and clarity

Summary

Yamazaki et al investigate partial EMT in pancreatic cancer and provide data that ROR1 marks pancreatic tumor cells that are capable of initiating tumors. The authors exploit scRNAseq of pancreatic tumor xenografts to identify a cluster of cells showing a partial EMT phenotype. The found 7 RTKs expressed more highly in this partial EMT cluster and focus their attention on ROR1, an 'orphan' receptor that has been implicated in WNT signaling and EMT previously. Validation experiments using ROR1-high vs low cells support that ROR1 expression correlates with EMT, poor outcome in human PDA patients, tumor forming and colony forming capacity. They also show that ROR1 high cells form tumors that recapitulate parental tumor histology. The authors show that ROR1 expression is associated with EF2 transcription factor activity, elevated expression of multiple targets including AURKB. Pharmacologic inhibition of AURKB reduces colony formation and genetic loss of ROR1 combined with chemotherapy (gemcitabine) has potent anti-tumor activity in vivo. The authors show that ROR1 expression is elevated in metastatic lesions and identify a novel enhancer element that putatively drives ROR1 expression in tumor cells. They provide evidence that this element is engaged by YAP/BRD4 and show that BRD4 inhibition reduces tumor cell colony formation. The manuscript is a solid combination of techniques with adequate controls and statistics.

Major Comments:

The overall conclusion that ROR1 expression marks a subset of pancreatic cancer cells that have the ability to initiate tumors is supported by the data provided. The correlative data are strong and the demonstration that loss of ROR1 reduces colony formation, reduces metastatic lesions and enhances the efficacy of chemotherapy are compelling. Additionally, the demonstration that ROR1 expression is elevated in metastatic lesions is consistent with many other drivers/markers of EMT in pancreatic cancer.

The conclusion that ROR1 expression is driven by YAP/BRD4 is interesting and provides important mechanistic depth to the study. However, this conclusion could be strengthened by use of a suitable rescue experiment. For instance does overexpression of ROR1 rescue the effect of BRD4 inhibition or loss of YAP?

A challenge with the data presented in Figure 1, the scRNA-seq data that lead them to ROR1, is that it is not stated how many tumors are used to generate the scRNA-seq data and the overall number of tumor cells analyzed is relatively low (993). The authors should provide the number of tumors used for the initial scRNA-seq. A general concern with any scRNA-seq data is batch effect, this is mitigated to a degree by the follow on studies that provide functional validation of ROR1 in multiple cell lines.

The data and methods are provided in an adequate manner. Reproduction of the experiments is likely. The authors use multiple cell lines and tools that are generally available.

The authors note a limitation of the study is that only human tumor xenografts were exploited.

Minor comments:

Figure 1E and text page 9. The text identifies MERB3 as a gene that marks the partial EMT cluster, I believe this is a type and the gene should actually be MSRB3.

Please provide the dose of gemcitabine in the legend for figure 5

Referees cross-commenting

I think the comments from Referee #2 are pretty reasonable - have no additions

Significance

Intratumor heterogeneity is a major challenge for the treatment of many cancers, including pancreatic cancer. The data provided support that ROR1 marks a subset of cancer cells in pancreatic tumors that have the capacity to drive intratumor heterogeneity. If supported these data have the potential to drive significant impact. Identification of a marker and a targetable pathway that supports tumor initiation in pancreatic cancer has the potential to nominate companion therapies that enhance the efficacy of standard of care approaches. Further, identification of a pathway that drives partial EMT in pancreatic cancer provides a substantial increase in baseline knowledge of intratumor heterogeneity.

These data would be broadly interesting to scientists interested in the tumor microenvironment, metastasis, therapy resistance and tumor progression. In addition, oncologists focused on drug development and combinatorial therapy will find this manuscript of interest.

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

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

In this work Yamazaki and colleagues performed single cell RNA sequencing of one xenograft tumor formed by the S2-VP10 PDAC cell line to explore PDAC intratumor heterogeneity. Using this model they identified ROR1 as heterogeneously expressed in neoplastic cells. Using further in vivo and in vitro models they show that ROR1high cells have higher tumor initiation capacity than ROR1low. By histone and ATAC-seq analyses, they identify a ROR1 enhancer upstream the promoter and show that YAP and BRD4 bind to this genomic region and that BRD4 inhibition by JQ1 reduces ROR1 expression and organoid formation. The data, figures and methods are nicely and clearly presented.

Major comments

1. The authors use one xenograft tumor as starting model and all conclusions are derived from the data generated with this model. To support the existence of identifie heterogeneity in the PDAC neoplastic compartment, I would strongly suggest to validate the existence of the partial EMT population and the ROR1 heterogeneity in single cell data bases generated from primary human tumors.
2. In Fig. 3G, it is mentioned that tumors grown from ROR1high cells recapitulate the original PDOx histology thus suggesting that ROR1high cells in the tumor are the actual TICs. ROR1low cells could also grow tumors, just with lower incidence. Are these tumors any different to the ROR1high derived ones? Is it just a lower tumor initiation capacity (TIC) or they can not recapitulate the tumor as the ROR1high cell? Can they also give rise to differentiated progeny cells? This should appear in the main text and not only in the discussion. I would suggest to move panel 3G to supplementary figure.
3. In line 160 you mention that known CSC markers such as CD44, PROM1 and DCLK1 are not differentially expressed between ROR1 high and low populations. Then, in figure 3H,I you analyze the expression of CD44v6 together with ROR1. I would try to put this information together in the text, or at least in fig. 3 start with something like "we had seen that both ROR1high and low express CD44, however...". In any case, I feel that the experiment with CD44 could be obviated (or at least moved to supplementary), as it brings the question of weather this is also true for DCLK1 or CD133.
4. JQ1 has been described to inhibit PDAC growth by downregulation of MYC. To unequivocally link the effect of JQ1 in the downregulation of ROR1 (Fig. 8M) as discussed in the text it would be important to exclude that other mechanisms such as MYC downregulation are taking place. For example, does JQ1 treatment of ROR1low cells also reduce their colony formation capacity (in an experiment such as the one in fig. 3C). Or does ROR1 re-expression in Fig. 8M rescue the JQ1 effect? These or other experiments could help to establish a stronger link between (BRD4/JQ1) and ROR1.

Minor comments

1. The data are nicely presented (text and figures) and the conclusions are clear. My suggestion to make the story more "catchy" at the beginning would be, if possible, to start from the observation done in primary human data and then move to the PDX model to explore ROR1 as a TIC marker in PDAC. For this, you could use available public single cell data of human PDAC tumors. If this doesn't work (it is of course possible that by unsupervised analysis you don't get the same clusters as in the PDX with the partial EMT cluster popping up), it would be nice if some primary tumor data came early in the story (currently the first figure showing heterogeneity in primary samples is in supplem fig. 4A).
2. It is not clear if the xenografts were subcutaneous or orthotopic. It would be good to include this information in the main text (line 102) and the methods so that the reader knows what is the exact model that has been used.
3. In Fig. 2F and 2G I would highlight the EMT pathway to help the reader.
4. In Supp Fig 4B it would be nice to have an amplified view of the staining as in panel C of the same figure.
5. In the same figure (Fig. 4A-D) ROR1 shows an apical staining pattern that doesn't seem to resemble the staining in patient samples. I am not an expert in pathology evaluation but I would recommend a pathologist to give her/his opinion. Possibly, during the PDX process, few cells from the original patient tumor are selected giving a different staining pattern.
6. In the analyses of TCGA data, be aware that only 150 from the original dataset are actual PDAC tumors. The dataset contains otherwise data from cell lines, PDX, normal tissue, etc that should be removed for a proper analysis (see DOI: 10.3390/cancers11010126)
7. Does ROR1 correlate with RFS? This would nicely fit with the concept of TIC and metastasis.
8. Line 219: ROR1 is not "depleted" in the lines as it is a downregulation model. "ROR1-downregulated" would be more correct.
9. It would be good to have a supplem figure showing that siROR1 cells show reduction organoid formation, to validate that the siRNA model functionally recapitulates the ROR1low vs high phenotype.
10. Some of the supplemental figures are only referred in the discussion although they appear earlier than other in the main text. This is a bit confusing when going through the figures.

Referees cross-commenting

I agree with the importance of addressing points 2 (link to AURKB), 4 (selection vs acquisition), 5 (mechanism in high vs low cells) raised by Reviewer 1, and the comments from Reviewer 3. I think that the study of other RTKs (point 1 from Reviewer 1) is not the focus of the story. It would be nice if the authors can comment on why they chose ROR1 but the fact that are other differentially expressed genes does not exclude the validity of the current story. I fell that the in vivo sustained KD experiment (point 3 from Reviewer 1) although interesting, it is not mandatory for a revision of this manuscript in case the adaptation of the animal protocol represents a long process. The experiment provided already in the current version is the best approach to address the role of ROR1 at the early initiation phase.

Significance

This is a neat and interesting work with potential implications for the clinical field of pancreatic cancer as the authors identified a new subpopulation with enhanced tumor initiating cell capacity. However, the use of JQ1 for pancreatic cancer has been previously discussed mainly linked to MYC inhibition, but also to stromal reprogramming or DNA damage induction. I missed some discussion in this regard in the discussion section. What is adding the work to the field of JQ1 treatment in PDAC? IN a way, how do the authors foresee that the discovery of ROR1high cells and the regulation of ROR1 by BRD4 and YAP will be beneficial when considering JQ1 in the clinics? Maybe by stratifying patients? Or by following ROR1 upregulation upon initial chemotherapy? These questions are just suggestions. In general, some discussion to put the work into the context of previous works using JQ1 in PDAC would be nice.

I believe that this work would be interesting not only to the pancreatic cancer community but also to a more general public working on cancer and/or stemmness as it touches several interesting points in that regard that can be applicable to other systems.

My own work is focused on pancreatic cancer, patient heterogeneity and stromal interactions. I am not an expert on histone or ATACseq analyses.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript the authors analyzed the role of ROR1 in pancreatic cancer progression and metastasis. They found that ROR1 expression is specifically increased in an partial EMT cell cluster upon scRNA-Seq of tumor cells derived from an orthotopic mouse PDAC model. Moreover, the ROR1 high population in tumors specifies cells with high proliferation and tumor initiation capacities, increased metastatic propensity and chemoresistance, since knockdown of ROR1 shows reduction of these features in vivo. By comparing transcriptomes from several in vivo models the authors identified that ROR1 acts through AURKB and that its expression is regulated by an upstream enhancer that is bound by YAP/TAZ and BRD4 complexes. With this study the authors identified a new targetable pathway that promotes tumor progression and metastasis in PDAC. The detailed analysis uses many state of the art techniques to address the role of ROR1 and is of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic. However, some of the findings are a bit preliminary and the drawn conclusions are not sufficiently supported by the experimental data. Moreover, some findings seem a bit out of context and do not really help to bring the story forward. At other instances experimental details are missing to mechanistically demonstrate the role of ROR1. In particular it remains elusive how ROR1 is regulated, i.e. which signaling events are crucial to generate ROR1 high vs. low cells. I listed my specific comments below.

1. The authors' initial finding is that in the partial EMT cluster ROR1, but also other RTKs (out of 56) are specifically increased. What about the other RTKs? Why was ROR1 chosen to analyze more thoroughly?
2. The finding of AURKB as crucial target of ROR1 is very weak and needs more in-depth analyses. It is not clear why AURKB was chosen over the other candidates. Is AURKB expression directly regulated by ROR1? Are the two genes directly linked? Can ROR1 deficiency be compensated by AURKB overexpression? Especially the decrease in AURKB protein level in Fig. 4K is not very convincing to account for the different phenotypes in ROR1 high and low cells. Is AURKB and ROR1 expression correlated in TCGA samples (like Fig. 8B)? In Fig. 4L the readout was changed from colony numbers to colony diameter. If AURKB is the crucial player downstream of ROR1, then colony formation efficiency should be affected at first. This needs to be shown. The statement in lines 223,224 that AURKB is a direct downstream target of ROR1 was not shown!
3. Fig. 4 A-E: The ROR1 KD was induced in vitro but not continued in vitro. The transient KD has a strong impact on tumor forming capacity, even though recovery of expression is likely within the first days in vivo. This is very interesting and underscores the role of ROR1 in tumor initiation and presumably independent of differences in proliferation. Would the results be different, if the DOX treatment would start with injection of the cells and continued in vivo? Is then tumor initiation not affected and maybe only tumor growth?
4. In Fig. 5 the authors show that ROR1 is highly expressed in tumors after gemcitabine treatment and conclude that the ROR1 high cells are a resistant population. However, this statement is too strong, since gemcitabine treatment could also lead to an upregulation of ROR1 in "low" cells during acquisition of chemoresistence. Together with our knowledge on the role of EMT in driving therapy resistance and therapy-mediated induction of EMT, such a scenario is equally likely. Similarly, the statement in lines 370-372 is not supported by experimental evidence.
5. In order to understand how ROR1 is regulated, the authors use ATAC-Seq and cut and run and identified a putative upstream enhancer element (Fig. 7). Although this element increases the activity of the promoter fragment in a reporter construct, the experiments do not help to understand how ROR1 activity is increased specifically in the "high" cells. Are peaks of YAP1 and BRD4 also changed between hi/lo cells? Is YAP OE and KD (BRD4 OE and KD) or the use of the inhibotor JQ1 altering the activity of the reporter constructs (i.e. only of the enhancer-promoter combination but not of the promoter only construct)? This would help to strengthen a direct link between ROR1, YAP and BRD4. Is YAP activity different in ROR1 high vs. low cells?
6. In Fig. 8A the authors identified 202 antigens that match the H3 monomethylation/acetylation pattern. How was YAP etc. chosen?

Minor:

1. Fig. 2D,E: What is actually shown here? Is there an overlap between the genes that define ROR1 high vs. low cells in both approaches? The gene list should be provided.
2. Fig. 3G: I suggest to include the images of the tumors from the ROR1 low cells in the main figure as well

Significance

PDAC is a very aggressive desease with very low 5-year survival rates. Understanding of the pathobiology is of keen interest. The findings of the authors are of high significance and extremely relevant as they provide a mechanism that can also be targeted by specific drug combinations, i.e. standard care gemcitabine with specific ROR1 inhibition. The findings are of great interest to a large audience including basic researchers in the field of cancer biology and oncologists in the clinic.