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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors show in this study that Lithium and other GSK3-beta inhibitors induce cilia elongation in Chlamydomonas. They further demonstrate that inhibition of endocytosis by Dynasore prevents the induced elongation of cilia. They speculate that a Dynamin-related protein might be involved in this process, and determine 9 Dynamin related proteins (DRPs) in Chlamydomonas of which DRP3 shows the highest sequence similarity. Lithium-induced ciliary elongation is prevented in DRP3 mutants supporting the author's hypothesis and indicating that DRP3 might be a GSK3-beta target, similar to some animal Dynamins. Since Dynamins interact with the F-actin regulator ARP3/3-complex, and because F-actin reorganization is observed in cells after GSK3-beta inhibition, they test the induction of ciliary elongation in arpc4 mutants and after blocking the ARP-complex by CK-666. Indeed, F-actin remodeling and cilia elongation were prevented after loss of ARP-complex function. The induction of ciliary elongation and F-actin remodeling also correlates with the emergence of strong F-actin punctae in cells, and the authors interpret that as induction of Dynamin-dependent endocytosis (also addressed in a current preprint from the group). From that, the conclude that endocytosis is required for delivering membrane to the growing cilium and that this is required for the observed effects. While this claim is somewhat supported by a lack of cilia elongation inhibition after treatment to prevent protein synthesis or Golgi function, direct evidence for membrane delivery to the cilium, the need for membrane delivery for ciliary elongation, and presence of bona fide endocytotic vesicles is sadly missing. Therefore, this study sheds new light on an important process in ciliary functional regulation and also furthers our understanding on why GSK3-beta inhibition induces elongated cilia in many cell systems, but I am not convinced that the conclusions are actually supported by the data, as the two key points in question were not experimentally addressed at this point.

Main points:

1. The authors need to demonstrate that new membrane is delivered in the process to the growing cilium. E.g. this could be done by membrane stains (pulse) and static or live-cell imaging analysis in untreated, GSK3-beta inhibitor treated and in mutants.
2. Along the same line, the authors need to demonstrate that the punctae are truly endocytotic vesicles. For that uptake assays/stains could be used and additional markers. Furthermore, there are multiple modes of endocytosis (e.g. Clathrin) besides Dynamin. The authors should determine if blocking other modes of endocytosis has similar or divergent effects on cilia elongation.
3. No cilia are actually shown in the study. I personally, would like to see how these cilia look like, especially in relation to the sites of F-actin remodeling and punctae formation. What comes first? Please also provide a axoneme staining to confirm elongation of the ciliary core and what happens to the tubulin pool when cilia cannot elongate any more? Is it accumulating at the ciliary base?
4. The authors also claim that the method of GSK3 inhibition is not important. It would be more correct to say that the mode/drug of GSK3 inhibition is not important, but discuss how some of the minor variance between treatments could be explained (incl. the timeline and temporal dynamics of the diverging effects; and the dose-dependency as low concentrations of BIO seem to induce shortening but high doses induce elongation of cilia).
5. They propose here a positive effect of F-actin build up in cilia length regulation, while most studies to date report ciliary shortening to correlate with increased F-actin at the ciliary base. I believe that this is not highlighted and discussed enough, which I find reduces the overall quality of the paper (but is easy to improve). It might be also interesting to test if other F-actin inducers/stabiliziers have the same effect?

Minor points:

1. In many Figures, the x-axis is labeled "Number of values", but I think that maybe number of observations might be more appropriate.
2. The author often use the word "normally" elongating, but in all cases the elongation is induced = abnormal situation. Maybe the authors could use a different term.
3. It is puzzling as to why DRP3 was chosen, while DRP2 actually is most similar in terms of domain composition. Maybe they could discuss that. They also could explain a bit better how the mutats were generated in which a "cassette was inserted early in the gene". What kind of disruption is expected?
4. The representative images in Figure 4A do not really seem to match the quantifications.
5. line 109: "of-targets" should be off-targets
6. line 141: "delivery form the Golgi" should be FROM the Golgi
7. line 160: "was DRPs" should be was DRP3
8. line 204/205: the sentence starting "Thus, we phalloidin..." should be rephrased. It sounds not quite correct
9. line 209: Figure 4A should refer to Figure 4B
10. line 211: "times or rapid ciliary" should be of rapid ciliary...
11. line 257: "in lithium." Should be in lithium treated cells

Significance

This study sheds new light on an important process in ciliary functional regulation and also furthers our understanding on why GSK3-beta inhibition induces elongated cilia in many cell systems, but I am not convinced that the conclusions are actually supported by the data, as the two key points in question were not experimentally addressed at this point.

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Referee #1

Evidence, reproducibility and clarity

The current manuscript by Bigge et al. demonstrated that the chemical inhibition of GSk3 causes ciliary elongation in Chlamydomonas reinhardtii. They show that lithium induced ciliary lengthening is majorly due to GSK3 inhibition. Consistent with earlier reports, they show that new protein synthesis is not required for lithium induced ciliary elongation. The authors report that targeting endocytosis either by using chemical inhibitors (dynasore and CK-666) or genetic mutants (dpr3 and Arpc4) does not cause lithium induced ciliary elongation. They further reveal enhanced actin dynamics in lithium treated cells and such activity is lost in Arpc4 mutants. Based on these results, the authors concluded that endocytic pathways may be involved in lithium induced ciliary lengthening. The results are interesting, and this work is important in understanding more about ciliary length regulation. However, more experimental evidence addressing the current interpretation that endocytic pathways may be involved in lithium induced ciliary lengthening is required.

Major comments:

1. The authors use chemical inhibitors as major tools for their study. However, the specificity of these inhibitors is a concern. How specific are these GSK3 inhibitors such as LiCl? Can authors show that LiCl mediated ciliary lengthening is due to inhibition of GSK3? Authors used BFA and Dynasore to show that not the Golgi, but the endocytosis derived membrane is required for ciliary lengthening. Again, here the specificity of these inhibitors is a concern. Especially as Dynasore has been shown to have non-specific effects.
2. Does inducing/enhancing endocytosis independent of GSK3 by other means has any effect on ciliary length regulation?
3. The major claim of this paper is that LiCl mediated ciliary lengthening is due to enhanced endocytosis. Although authors showed that inhibition of endocytosis results in reduced ciliary length, it is important to show if GSK3 inhibition by LiCl (or any other inhibitor) causes any increased cellular endocytosis? Similarly, what is the effect of GSK3 mutants on endocytosis?
4. Are these endocytic processes enhanced specifically at/or around the cilium during the ciliary lengthening process?
5. Authors claim that drp3 is a target of GSK3 and, similar to the canonical dynamin, functions in endocytosis. While, it is an important observation, experiments are required to show the role of drp3 in endocytosis and also to show that it is indeed a target of GSK3.
6. Mechanistic insights into how endocytosis/actin dynamics regulate ciliary lengthening would be interesting to see. Further, it is interesting to see if the ciliary signaling defects caused by abnormal ciliary length can be rescued by inhibition of endocytosis.

Minor comments:

1. The paper needs a thorough proof reading as it harbors many spelling mistakes, grammatical errors, and poor sentence formation in multiple instances.
2. Supplemental Figure S2A and S2B should be quoted separately from S2C and S2D.
3. In Page 6 paragraph 2 - "authors wrote "To determine if GSK3 could be a potential kinase for this protein, we employed ScanSite4.0, which confirmed that of the 9 DRPs of Chlamydomonas, the only one with a traditional GSK3 target sequence was DRPs (Supplemental Figure 2)." No data is shown in S2 with regard to this. Either data needs to be shown or change the text in a way to avoid confusion.
4. It would be nice to see if GSK3 can actually phosphorylate DRP3.
5. The authors observe that arpc4 mutants do not form actin puncta upon LiCl treatment. Could this phenotype be rescued by complementing with WT ARPC4.
6. The concentration of inhibitors is described differently in the text and figure legends (for example Fig. 4A)
7. The p values are not significant in some of the figures. (Fig. 4D &Fig. 5C)

Significance

The current manuscript by Bigge et al. demonstrates that endocytosis is required for GSK3 inhibition mediated ciliary lengthening. Maintenance of proper length of cilia is crucial and its dysregulation results in pathogenesis. This work takes the field forward and helps in our understanding of how ciliary length is regulated. This work is of interest to researchers working in the field of ciliary biology as well as to those working on endocytosis.

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Reply to the reviewers

Point-by-point response

We thank the reviewers for their constructive comments. We have addressed all of them to the best of our knowledge. Our responses are shown below in bold and all changes in the text are highlighted in yellow.

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

This study of Rizk, Bekiaris and colleagues is well written, carefully edited, and nicely placed into the trending context of the juvenile immune system development.

They suggest that cIAP ubiquitin ligases cIAP1 and cIAP2 sustain type 3 γδ T after 4-5 weeks of age in mice. As a mechanism they show that these ubiquitin ligases are required in a cell-intrinsic manner to maintain cMAF and RORγt levels, and that this depends likely on overt activation of the non-canonical NF-κB pathway.

Extrinsic factors such as microbiota did not seem to play a major role in this context.

**Major comments:**

It is absolutely crucial to directly and stringently control the efficiency of cIAP depletion via RORgt-cre, which may take some time and thus perhaps only reaches relevant (exponential) penetrance at early adulthood?

Fig 4C is nice, however the Birc2 loxP sites may be far less efficient than those in the ROSA26-LSL-RFP system.

- We thank the reviewer for this comment. In this regard, we sorted day 1 old γδT17 cells from the thymus of Cre+ and Cre- mice and screened for Birc2 mRNA (cIAP1) expression. We additionally compared expression to CD27+ γδ T cells, from the same thymi as RORγt-neg controls. Please see new Fig S5A and text line 208-209.

However, the pre-puberty timing aspect is surprising, but without this aspect the conclusions would be similarly exciting.

- The fact that Birc2 is indeed deleted in newborn thymocytes, supports our conclusions that its impact is seen progressively while mice are aging

**Minor comments:**

• To understand the general impact of cIAP on gdT17 homeostasis, the authors should consider investigating them in additional organs, as these gdT17 are quite tissue-resident and differentially adapt to their environment, where they use specific anti-apoptotic strategies to persist, including expression of Bcl2a1 family proteins.

- We have investigated lung from adult ΔIAP1/2 and found significantly reduced γδT17 cells, in accordance with our data in the LN, gut and skin. Please see new Fig S1E and text lines 134-136.

• Fig. 3: Has the presence of gdT17 in the graft been analyzed or enumerated? Experiments shown in Fig 3 AB and FG might collectively suggest that co-transferred gdT17 from the 45.1 BM graft could have reconstituted the regenerated gdT17 compartment in competition with the radioresistant 45.1/2 host gdT17 cells. This would actually not compromise the results, as the cIAP deficient cells did not persist.

- We are not entirely sure what the reviewer means with this comment. We believe that the data in Fig 3 clearly shows that ΔIAP1/2 cells cannot compete with WT cells. This is also reinforced in Fig S3 where the host is ΔIAP1/2.

Reviewer #1 (Significance (Required)):

**Significance**

This work is very original and might be of pharmacological interest for approaches targeting cIAP, e.g. in order to enhance anti-viral therapies.

**Referee Cross-commenting**

No further comments.

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

The authors studied the effect of the inactivation of cIAP1 and 2 on the development and evolution of γδ T cells and in type 3 innate lymphoid cells (ILC3) using RORc-Cre induced inatiction of cIAP1 in combination or not with cIAP2 whole body KO. The authors showed that these two E3 ubiquitin ligases that regulate the NF-κB pathway, are important to maintain a population of IL-17 producers γδ T and ILC3 in adult animals. This lack of maintenance is correlated with a loss of c-MAF and RORγt expression in the two cell types and may be related to a deficiency in entering cell cycle in response to various cytokines. The authors also established that the mechanism is independent of the TNFR1 pathway. The article is well written, clear and most of the conclusions are well supported by the data showed. The results presented are novel and interesting for the field. However, I would suggest some major changes to make the story suitable for publication.

1- The study of 2 different cell types brings some confusion to the story, even if I understand it makes some sense to pool these two parts in the same article. The γδ T cell part is more complete than the ILC3 part, which brings some frustration for the reader, as nothing indicates that the mechanisms leading to the loss of maintenance are similar in the 2 cell types. I would suggest to simply remove the ILC3 part and keep it for another article. If the authors wish to keep it in this article, they must perform a similar set of experiments already done for the γδ T cell part, especially the lineage tracing performed in figure 5 as c-Maf is known to be important in ILC plasticity for ILC3 and ILC1. They would also need to confirm the mechanisms involved in the process leading to ILC3 decrease.

- We thank the reviewer for this comment. We do realize that the ILC3 part of the story may seem incomplete. For this reason, we have taken into consideration the reviewer’s advice and performed lineage tracing in ILC3 cells. In adult ΔIAP1/2 mice that were reporting RFP in RORγt+ cells, we found that within the ILC population, there was 10-fold reduction in RFP+ cells, suggesting that it is unlikely they convert to a non-ILC3 population. Please see new Fig S9C and text lines 297-302. In accordance KLRG1+ ILC2 numbers were not affected (Fig S9C).

Next, we isolated sLP lymphocytes from 4-week old mice and treated them with cytokines that are known to induce ILC3 proliferation including IL-7, IL-1β and IL-23. We also chose these cytokines to concur with our γδT17 findings. However, we could not induce cell cycle in either WT or ΔIAP1/2 cells. We contacted experts in the field, namely Dr David Withers at the University of Birmingham, who contacted further experts (Dr Matt Hepworth), in order to ask for advice of how to induce gut ILC3 proliferation. We quote David Withers “we have never had any joy making ILC3 proliferate much in vitro”, and Matt Hepworth “have been looking at this and have struggled to make them proliferate in vivo or in vitro”. So, unfortunately, we cannot test ILC3 proliferation in the same way we did for γδT17 cells.

2- Although the authors nicely excluded the TNFR1 pathway from the mechanisms leading to γδ T cell loss in adult, the overt activation of the cRel pathway is not enough established as far as I am concerned. It would at least require a more thorough quantification of the immunofluorescent staining done. Showing only one cell is not enough. If possible, using another approach to confirm these data would also be needed.

- We have now quantified RelB nuclear translocation over 4 experiments and found a significant increase in ΔIAP1/2 cells. Please see new panel in Fig 5F and text lines 244-250. Furthermore, there was a significant increase in Relb mRNA in ΔIAP1/2 newborn thymic γδT17 cells, which is consistent with activation of the non-canonical NF-kB pathway. Please see new Fig S6C and text lines 244-246.

3- The expression level/quantity of protein of cIAP1/2 in γδ T cells from WT animal at the various stages of development has not been analyzed. Does it remain constant? Does it vary throughout development of γδ T cells? This information is important to further enforce and understand the role of these protein in the development of γδ T cells.

- Unfortunately, we cannot quantify cIAP1/2 protein levels in these cells for technical reasons. There is no Ab for flow and only a cIAP1 Ab for western blots, which is of course impossible when dealing with such low cell numbers.____ However, we have contacted Dr Dominic Grün who had done a single-cell RNA-seq profiling of γδ T cells throughout different developmental stages, and asked to analyze expression levels of Birc2 and Birc3. We found that both Birc2 and Birc3 were expressed across all subsets of fetal and adult thymic γδ T cells with no specific enrichment and no apparent up- or down-regulation between the two time points. Please see attached Figure 1.

Attached Figure 1: expression patterns of Birc2 and Birc3 at a single cell level in the different populations of fetal and adult thymic γδ T cells.

4- In Figure 4D-E, the authors showed that in vitro, γδ T cells fail to progress through cell cycle in response to IL-7 or IL1b+ IL-23. Is a similar block detectable directly ex-vivo? Furthermore, it appears that Imiquimod treatment restore at least partially the deficiency in γδ T cells in the double KO mice. It would mean other cytokines or TCR triggering is rescuing this phenotype. Could the author test in vitro other stimuli and test whether γδ T cells are reactive to some stimuli but not others? It would bring some lights on the signaling regulated by cIAP1/2.

- There is little if any detectable active cell cycling of these cells directly ex vivo, as shown by near absence of Ki67+7AAD+ cells (see below). We can still pick up small differences in Ki67+ cells but this is not sufficient to conclude whether there is more or less cell division. Please see attached figure 2.

Attached Figure 2: ex-vivo cell cycle analysis of γδT17 cells form 4 week old- ΔIAP2 or ΔIAP1/2 mice.

- We have now tested how 4-week old γδT17 cells from ____Δ____IAP1/2 mice respond to IL-2 and TCR stimulation. We found that similar to IL-7, IL-1b and IL-23, cells lacking IAPs proliferate less under both conditions. See new Fig S5C and lines 227-228.

**Minor point:**

although the authors cite a reference in the result section, could they show a dot plot confirming that the CD44hi CCR6+ or CCR6+ are the only population producing IL-17 among, γδ T cells?

- We now show this in Fig S1D and lines 129-130

Reviewer #2 (Significance (Required)):

This article describes a new role for the cIAP1 and 2 in the maintenance of γδ T cells and ILC3s. In line with their previous work (Rizk, 2019), they show that this effect is correlated with a loss in c-MAF expression, which is a major transcription factor for these 2 cell types. These discoveries are of interest for specialists in the field, including myself. I am an expert in T cells and ILCs, with an interest in c-MAF function in these cell types.

**Referee Cross-commenting**

No further comments.

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Referee #2

Evidence, reproducibility and clarity

The authors studied the effect of the inactivation of cIAP1 and 2 on the development and evolution of T cells and in type 3 innate lymphoid cells (ILC3) using RORc-Cre induced inatiction of cIAP1 in combination or not with cIAP2 whole body KO. The authors showed that these two E3 ubiquitin ligases that regulate the NF-B pathway, are important to maintain a population of IL-17 producers T and ILC3 in adult animals. This lack of maintenance is correlated with a loss of c-MAF and RORγt expression in the two cell types and may be related to a deficiency in entering cell cycle in response to various cytokines. The authors also established that the mechanism is independent of the TNFR1 pathway. The article is well written, clear and most of the conclusions are well supported by the data showed. The results presented are novel and interesting for the field. However, I would suggest some major changes to make the story suitable for publication.

1- The study of 2 different cell types brings some confusion to the story, even if I understand it makes some sense to pool these two parts in the same article. The T cell part is more complete than the ILC3 part, which brings some frustration for the reader, as nothing indicates that the mechanisms leading to the loss of maintenance are similar in the 2 cell types. I would suggest to simply remove the ILC3 part and keep it for another article. If the authors wish to keep it in this article, they must perform a similar set of experiments already done for the T cell part, especially the lineage tracing performed in figure 5 as c-Maf is known to be important in ILC plasticity for ILC3 and ILC1. They would also need to confirm the mechanisms involved in the process leading to ILC3 decrease.

2- Although the authors nicely excluded the TNFR1 pathway from the mechanisms leading to T cell loss in adult, the overt activation of the cRel pathway is not enough established as far as I am concerned. It would at least require a more thorough quantification of the immunofluorescent staining done. Showing only one cell is not enough. If possible, using another approach to confirm these data would also be needed.

3- The expression level/quantity of protein of cIAP1/2 in T cells from WT animal at the various stages of development has not been analyzed. Does it remain constant? Does it vary throughout development of T cells? This information is important to further enforce and understand the role of these protein in the development of T cells.

4- In Figure 4D-E, the authors showed that in vitro, T cells fail to progress through cell cycle in response to IL-7 or IL1b+ IL-23. Is a similar block detectable directly ex-vivo? Furthermore, it appears that Imiquimod treatment restore at least partially the deficiency in T cells in the double KO mice. It would mean other cytokines or TCR triggering is rescuing this phenotype. Could the author test in vitro other stimuli and test whether T cells are reactive to some stimuli but not others? It would bring some lights on the signaling regulated by cIAP1/2.

Minor point:

although the authors cite a reference in the result section, could they show a dot plot confirming that the CD44hi CCR6+ or CCR6+ are the only population producing IL-17 among , T cells?

Significance

This article describes a new role for the cIAP1 and 2 in the maintenance of T cells and ILC3s. In line with their previous work (Rizk, 2019), they show that this effect is correlated with a loss in c-MAF expression, which is a major transcription factor for these 2 cell types. These discoveries are of interest for specialists in the field, including myself. I am an expert in T cells and ILCs, with an interest in c-MAF function in these cell types.

Referee Cross-commenting

No further 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

---

Referee #1

Evidence, reproducibility and clarity

This study of Rizk, Bekiaris and colleagues is well written, carefully edited, and nicely placed into the trending context of the juvenile immune system development.

They suggest that cIAP ubiquitin ligases cIAP1 and cIAP2 sustain type 3 γδ T after 4-5 weeks of age in mice. As a mechanism they show that these ubiquitin ligases are required in a cell-intrinsic manner to maintain cMAF and RORγt levels, and that this depends likely on overt activation of the non-canonical NF-κB pathway. Extrinsic factors such as microbiota did not seem to play a major role in this context.

Major comments:

It is absolutely crucial to directly and stringently control the efficiency of cIAP depletion via RORgt-cre, which may take some time and thus perhaps only reaches relevant (exponential) penetrance at early adulthood? Fig 4C is nice, however the Birc2 loxP sites may be far less efficient than those in the ROSA26-LSL-RFP system.

However, the pre-puberty timing aspect is surprising, but without this aspect the conclusions would be similarly exciting.

Minor comments:

• To understand the general impact of cIAP on gdT17 homeostasis, the authors should consider investigating them in additional organs, as these gdT17 are quite tissue-resident and differentially adapt to their environment, where they use specific anti-apoptotic strategies to persist, including expression of Bcl2a1 family proteins.
• Fig. 3: Has the presence of gdT17 in the graft been analyzed or enumerated? Experiments shown in Fig 3 AB and FG might collectively suggest that co-transferred gdT17 from the 45.1 BM graft could have reconstituted the regenerated gdT17 compartment in competition with the radioresistant 45.1/2 host gdT17 cells. This would actually not compromise the results, as the cIAP deficient cells did not persist.

Significance

Significance

This work is very original and might be of pharmacological interest for approaches targeting cIAP, e.g. in order to enhance anti-viral therapies.

Referee Cross-commenting

No further comments.

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Reply to the reviewers

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

The manuscript by Sasaki et al titled "Conditional GWAS of non-CG transposon methylation in Arabidopsis thaliana reveals major polymorphisms in five genes" employed conditional GWAS to identify trans-regulators of mCHG levels in Arabidopsis natural accessions, after controlling for mCHH. Using loss of function mutants for couple of these genes, the authors also tested their effects on mCHG levels.

Overall, this manuscript makes a nice contribution. I suggest the following improvements to enhance the quality of this manuscript.

Comments:

1. MSI1 has been shown to be copurified with TCX5, a component of DREAM Complex. The DREAM complex transcriptional regulates CMT3, MET1, DDM1 in a cell cycle dependent manner (ref: Yong-Qiang Ning, 2020 nature plants). Tcx5/6 double mutants have ectopic gain of TE and genic mCHG. It would be nice to refer this paper and add to the MSI1 part accordingly. Absolutely: thanks for suggesting this!

Multifaceted regulation of mCHG levels seems to be evident from this and previous studies. Why would such complex pathways evolv to regulate mCHG? Bewick et al 2016 and Wendte et al 2019 showed lack of CMT3 or ectopic expression of CMT3 can influence CG gene body methylation (gbM). One possibility is that these five factors regulate CHG to maintain it at a level that is just enough to target TE. Irrespective of the functional relevance of gbM, differences in the levels of these five factors might result in erroneous gbM. It would be interesting to look for the rates of gbM and number of gbM genes in the natural accession carrying 1 to 4 number of mCHG-decreasing alleles. Also, in the one line from Iberian peninsula carrying polymorphisms in all five genes.

Yes, the connection between CHG and gbM is very interesting and deserves more attention. We looked for the effect of cumulative mCHG-decreasing alleles on gbM, but there was no association with gbM — but this is really not expected given the stable epigenetic inheritance of gbM. The Iberian peninsula line carrying all decreasing alleles did slightly lower gbM levels, but it is impossible to exclude the effects of population structure. Since we have nothing to add beyond speculation, we prefer not to go into this topic.

The authors mentioned a significant peak for mCHG|mCHH on RdDM-targeted transposons was located 196 bp downstream of MIR823a and not on mature miRNA. Therefore, this cannot directly impair miR823 base pairing with CMT3 mRNA transcripts and its cleavage. Moreover, natural accessions carrying alternative MIRNA823 allele show reduced CMT3 and mCHG levels, meaning more miR823 levels? Does this 196 downstream region contain any regulatory feature that effects miR823 transcription? Or this region still falls in the primary miRNA hairpin region? A single nucleotide change in pri-miRNA can have a significant impact on its secondary structure that can impede DICER processivity and effectively levels of mature miR823 molecules? It will be beyond the scope of this paper to pin down the exact mechanism. But a simple stem loop RT-PCR for miR823 levels in reference and alternative accessions would be informative (on accessions that grow at the same speed). Perhaps, the authors can at least model SNP induced pri-miRNA secondary structure variations using Vienna RNAFold (http://rna.tbi.univie.ac.at/cgi-bin/RNAWebSuite/RNAfold.cgi) and present MEF values (maximum free energy) for representative accessions.

Stem-loop qRT-PCR for MIR823a expression would indeed be helpful to confirm allelic effects. However, comparing lines with wildly different genetic backgrounds is fraught with difficulty due to trans-effects. Furthermore, MIR823a is expressed specifically during embryogenesis, and the expression quickly decreases after the early heart stage (Papareddy et al., 2021). Thus, we would need to extract microRNA from embryos at exactly the same developmental stage, from lines that may develop at different speeds.. Most likely, time-series data would be required, and generating such data is a massive undertaking. As noted in the paper, we did measure MIR823a expression by stem-loop qRT-PCR for several lines carrying reference and alternative alleles but the results were inconclusive. A proper study of this is beyond the scope of this paper.

Testing predicted effects on RNA secondary structure, on the other hand, is eminently feasible. As suggested, we used Vienna RNAFold for the region, including the GWAS peak. Since the SNP is linked to a 35 bp deletion (shown in S4A), it is closer to the MIR823A coding region than 196 bp. However, the results indicate that the SNP (Chr3:4496626) is not within the stem-loop. It remains possible that this SNP tags multiple SNPs in the annotated stem regions. This is now mentioned.

Figure 1A can be made more reader friendly. Perhaps this can be broken down into correlation plots for individual conditions or tissue types. In addition, it might be good to add individual r-square values for each of them instead of compound r-square.

We respectfully disagree, since the main point of the figure is the overall correlation and heterogeneity, rather than the correlation within sub-sets. Instead of splitting the plot, we changed color contrasts to make it easier to read.

Page 3, Paragraph 1 from line 3 to end of paragraph. The authors wrote "Much of this variation is due to differences in the environment (including tissue, which can be viewed as a cellular environment)". A possible explanation is these two tissues have different mitotic indices (fraction of cells diving and non-diving; flowers have more dividing cell, leaves have more non dividing and endoreduplicated cells) that explains non-CG variation. I would suggest authors to change the text to this and refer to Filipe Borges et al 2021 Current biology paper.

This is certainly a possibility, although higher mCHG levels in flower buds presumably also reflect higher CMT3 expression during embryogenesis (Feng et al. 2020; Gutzat et al. 2020; Papareddy et al. 2021). We now mention both explanations and cite Borges et al. (2021).

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

Summary:

Sasaki et al. carried out a conditional GWAS analysis of TE-CHG methylation in Arabidopsis thaliana natural accessions. They revealed multiple associations with SNPs in known DNA methylation genes. A new finding is the association found proximal to JMJ26, which had no previously described role in the maintenance/establishment of RdDM-targeted transposons. The authors validate the JMJ26 association using a loss-of-function mutant of JMJ26, which essentially recapitulates the GWAS effect, suggesting that JMJ26 is likely causal. An important point of the study is that the associations detected with conditional GWAS have not been seen in previous univariate (i.e. unconditional) GWAS, probably due to to a lack of power. At the sub-genome-wide threshold the authors discovered further, albeit weaker, associations that were also highly enriched for known DNA methylation genes.

Overall impression:

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs. What I personally found very distracting throughout the manuscript was the strong emphasis on the methodological aspect; that is, the conditional GWAS, which is really not new. Furthermore, the conceptual/philosophical discussion about what is a complex trait or what can be called polygenic was slightly pedantic and distracted from the biological message.

There are three points here. First, we disagree that the GWAS results are confirmatory. Sure, only one of our associations is connected with a novel gene, but the fact that the four other genes apparently harbor major polymorphism is a new finding that contributes to our understanding of the function of this trait (and, possibly, these genes). Second, while it is possible that we emphasize statistical methodology too much, we do this for clarity, not to claim that what we are doing is novel. Third, we are similarly not interested in defining what is polygenic and what isn’t, but rather put the results in the context of other studies. We have changed the writing in various places to make it clearer (and hopefully less distracting/pedantic).

A conceptual comment:

• The conditional GWAS presented here is conceptually very similar to conditional QTL mapping approaches where candidate loci are included, a priori, as covariates in the model, and a scan is performed to search for additional modifiers. It is known that this approach increases power because the scan is performed on the residual trait variation (having accounting for effect of candidate loci). This is also the idea behind MQM mapping, although in the latter the inclusion is not restricted to candidate loci. Instead of including candidate SNPs as covariate the authors include TE-CHH methylation levels as a covariate as it is highly correlated with TE-CHG methylation. By doing this, the authors essentially "control" for any SNP affecting the covariance between CHG and CHH, even if these SNPs (and their genetic architecture) remain unknown. Hence, the conditional scan is mainly on the residual variation in TE-CHG methylation that is unique to this context (i.e. independent of CHH). That additional TE-CHG associated loci pop up in this scan is perhaps not so surprising.

We agree, and have even written papers on this very subject. We were surprised by this comment as we felt we had included lengthy sections (see also comment above) about methodology, emphasizing that multi-trait analysis is a good idea in principle. One of our purposes here is to provide a beautiful example demonstrating this. We have tried to make these points clearer.

The finding that this conditional GWAS yields again a handful of loci of that explain a considerable part of the trait (now residual trait) variation leads the authors to suggest that the genetic architecture underlying non-CG methylation of TEs is not "polygenic". I think this is semantics. All the authors have done is relegate any causal SNPs underlying the covariance between TE-CHG and TE-CHH to the right hand side of the equation of their GWAS model, and subsumed it under the predictor "TE-CHH methylation levels". That is, the genetic architecture underlying this covariance is still unknown, difficult to identify and probably highly polygenic.

Again we agree, and fail to see why the reviewer thinks we do not. Nowhere do we claim that the overall covariance has a simple basis, and we explicitly state that it is the conditional mCHG variation that has an oligogenic basis. We did write that “univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic”, which was imprecise, and arguably erroneous. The word “erroneously” has been removed in the revision.

The authors essentially decompose a complex traits into parts and map genetic architectures for each part. Although each part seems less complex and more oligogenic than polygenic, when putting all the parts back together, I would argue we are getting close to a complex trait with a polygenic architecture. The study by Hüther et al, which the authors also cite, is another example of how a complex trait can be decomposed into parts. In reference to one of the authors' GWAS associations, they say "...this association was also recently found by Hüther et al. (2022) using GWAS for unconditional mCHG levels of individual transposons. The MIR823A polymorphism appears to almost exclusively affect mCHG (Figs. S2, S3), primarily targeting the same transposons as a CMT3 knock-out...". In the case of Hüther et al., the complex TE-CHG methylation trait is simplified by selecting specific TEs, a priori, that are differential methylated in CMT3 knock-out lines. One could go on like this, and continue to peel away this complex trait. But, again, this does not mean that the overall TE-CHG methylation trait is not complex nor polygenic. It spirals down into a discussion of what is actually meant by "complex" or "polygenic", which is an interesting discussion, but - in the case - of this manuscript takes away from the biological message. My point is perhaps best reflected in the following statement from the discussion section: "Despite high heritability, univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic (Kawakatsu et al., 2016)." But a few lines below the authors seem to realize what they have actually done "We believe that, by controlling for mCHH, we have effectively simplified the trait, revealing genetic factors affecting mCHG only, perhaps by affecting the maintenance of this type of DNA methylation."

The phrase “seem to realize” is unwarranted and unnecessary sarcasm. Given that we cite the two century-old papers that first demonstrated that it was possible to decompose complex traits into Mendelian ones, it should be obvious that we understand what we have done. That our writing could have been better is another matter. As noted above, the word “erroneously” has been dropped, and we have also changed the second sentence to make it obvious that this is obvious. We suspect that whether one finds this part of the Discussion “distracting” or not depends on training and background — our objective was to explain our results to readers who (unlike us and the reviewer) are not well-versed in quantitative genetics.

Specific comments

1. A large part of the manuscript focuses on SNPs that enriched for a priori genes that fall below the genome-wide significance threshold. While I see the reasons for doing this in this particular manuscript, I do not see how this is useful in general (again this approach is partly "sold" on methodological grounds). The approach can obviously not be extended to study traits where a priori gene sets are unavailable or incomplete. Moreover, the "FDR" approach based on the a priori gene set labels GWAS hits that are not within the a priori set "false discoveries", which may or may not be true. Moreover, there is no "natural" stopping point for going below GWAS thresholds. An alternative, to this would be to perform a targeted GWAS for a priori genes (+ a LD window around them). Since this alleviates the multiple testing burden, I would be curious to see what this yields both in terms of conditional and unconditional analysis. Candidates that show a signal could be included as covariates and a conditional scan for unknown genes could then be performed.

The FDR analysis using a set of a priori genes should be explained in detail in this ms. It is cumbersome to go to another manuscript to see what was done exactly, especially since this information is also difficult to dig up in the Atwell 2010 study. Although I understand the idea behind this approach, I would be concerned that this type of "FDR" analysis assumes that that all methylation genes are known. A novel candidate that was perhaps never identified in mutants screens before would be classified as a false discovery. Similarly, known candidates that carry no functional polymorphisms in nature, perhaps because they are highly constraint, will never become a discovery.

Comments 1 and 9 largely overlap, and so we moved 9 here for clarity and respond to both at the same time. We agree that the enrichment analysis should be explained in this article as well, so as to save the reader from finding the supplement to an old paper. A new section has been added to Methods. In this section, we also try to preempt some of the misunderstandings in the reviewer's comments.

First, our approach is indeed generally applicable. Whether it is useful depends on what you want to do, and yes, the utility will depend on the quality of the independent data, but note that the a priori gene set does not have to be genes: you could use this approach to compare coding vs non-coding regions of the genome, for example.

Second, we are not trying to “sell” our approach (or anything else for that matter).

Third, the approach does not label GWAS hits that are not within the a priori set as false discoveries: it says nothing about these hits.

Fourth, we are not sure what is meant by a ‘“natural” stopping point for going below GWAS thresholds’, but our approach does provide a simple way to explore how FDR (in the a priori set!) depends on the threshold used.

Fifth, the proposed alternative of “targeted GWAS” (non-genomewide association, as it were) is not equivalent, because our approach was not designed to increase power by alleviating the multiple testing burden, but rather to rigorously demonstrate that there is a signal in the data when faced with uncalibrated p-values. That it can also be used to explore sub-significant associations is a nice side-effect that we exploit here.

Sixth, we do not assume that all methylation genes are known, nor is our goal to find them all.

With regards to the CMT2 signals (particularly section "Further evidence for allelic heterogeneity at CMT2") it would have been useful/clearer to break down CHH into CWA and non-CWA.

While this is a sensible suggestion, the focus of this paper is on mCHG, and refining the mCHH measurement would essentially amount to re-doing all analyses.

I understand that the authors set out to do this conditional analysis because previously no hits could be found for CHG TE methylation. However, have the authors considered going the other way around and performing a CHH|CHG analysis to find additional QTL affecting CHH methylation, partly indepedently of CHG?

Yes, this was in the paper, but we only mention it in the Discussion (and Fig S13) as the results were only of methodological interest (as expected, they were very similar).

The authors write: "While both mCHG and mCG showed high heritability, GWAS yielded little in terms of significant associations. This might be because these "traits" are highly polygenic, or because they are at least partly transgenerationally inherited, and hence do not behave like standard phenotypes." Please clarify what they mean by "not behave like standard phenotypes".

Done.

The authors write: "Our starting point is the observation that mCHG and mCHH levels on transposons are strongly correlated in the 1001 Epigenomes data set (Kawakatsu et al., 2016), especially for RdDM- targeted transposons (Fig. 1A; see Methods). Much of this variation ....". What is mean by "this variation"?

The sentence has been changed to make this clearer.

A few lines below, they write "...huge". Please rephrase.

Done.

The authors write: "sample data set ("Leaf SALK ambient temperature"; n=846). Interestingly, the covariance between mCHH and mCHG showed the same pattern in data generated by knocking out known or potential DNA methylation regulators in the same genetic background (Fig. 1B) (Stroud et al., 2013). This demonstrates strong co-regulation of these types of methylation, in particular for RdDM-targeted transposons." It is noticeable that many double mutants are off the diagonal. To me this indicates that they affect one context more than the other (i.e. they break covariance). Second, it suggests that they are probably interacting non-additively. It would be great if the authors could comment on this observation; perhaps also later in the ms, where they make a case for additivity.

We are not convinced that the double- or triple-mutant show non-additivity. Adding up effects in Figure 1 works pretty well. As for our GWAS results, it is clear that small effects (like the ones in our GWAS) will always tend to look additive for simple mathematical reasons. This does not mean that no interactions exist, and we emphasize this in the paper. We also have an example of non-linearity when it comes to TE activity. This is now also emphasized.

The authors write: " it is difficult to say what fraction of these factors is genetic and what is environmental, but, regardless of this, we hypothesized that the substantial covariance could reduce power of GWAS for either mCHH or mCHG (when using a standard univariate model), and that an analysis accounting for this covariance might perform better...". The arguments given thus far are not sufficient to understand why a "substantial covariance" between traits would reduce the power to map individual traits. I think more needs to be done here to motivate this.

The sentence following the one quoted is “In essence, we sought to simplify a complex trait by breaking it into constituent parts”, which is very much part of the motivation. As the reviewer noted above, it is not surprising that a conditional analysis turns out to be more powerful. The comment may have arisen from the statement “This insight is the basis for this paper”, which is misleading — there is no insight here, just a very obvious hypothesis, which turned to be correct. We have changed the writing to make this clearer.

The authors write" "However, MSI1 is required to control DNA methylation via repression of MET1, and a loss of FAS2 in CAF-1 induces mCHG hypermethylation (Fig 1B) (Stroud et al., 2013; Jullien et al., 2008)...", where is the "FAS2 in CAT-1" result visible in Fig. 1B?

fas2 induces mCHG hypermethylation in CMT2-targeted TEs, presumably via a complex that also involves MSI1. It is marked in Fig. 1B. We have rephrased the sentence to make this clearer.

The results presented in "A jmjC gene is a novel modifier of mCHG in RdDM-targeted transposons" could have been showcased better. Only after reading the methods part did I realize that the authors generated CRISPR mutants. It reads as if the authors just picked up some available loss of function mutants and profiled them. But, clearly, much more work was involved here and the authors could have brought that out more. Perhaps more generally, I think all the new functional analysis the authors perform is largely "under-sold" in this manuscript at the expense of unnecessary methodological/concpetual discussion (see point above).

We actually generated CRISPR/CAS9 mutants only for MIR823A (Table S5). For JMJ26, a t-DNA insertion line was available, and results based on this and rescue lines provided sufficient results. To clarify this, we corrected the subsection titles.

In section "The power and complexity of conditional GWAS", the authors write "The performance of GWAS relies on using the right model for the relation between genotype and phenotype. As with other statistical methods, using the wrong model may lead to unpredictable results." This seems like a too obvious of a statement.

Indeed: it is meant ironically. It is obvious, yet people do it.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Sasaki et al. carried out a conditional GWAS analysis of TE-CHG methylation in Arabidopsis thaliana natural accessions. They revealed multiple associations with SNPs in known DNA methylation genes. A new finding is the association found proximal to JMJ26, which had no previously described role in the maintenance/establishment of RdDM-targeted transposons. The authors validate the JMJ26 association using a loss-of-function mutant of JMJ26, which essentially recapitulates the GWAS effect, suggesting that JMJ26 is likely causal. An important point of the study is that the associations detected with conditional GWAS have not been seen in previous univariate (i.e. unconditional) GWAS, probably due to to a lack of power. At the sub-genome-wide threshold the authors discovered further, albeit weaker, associations that were also highly enriched for known DNA methylation genes.

Overall impression:

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs. What I personally found very distracting throughout the manuscript was the strong emphasis on the methodological aspect; that is, the conditional GWAS, which is really not new. Furthermore, the conceptual/philosophical discussion about what is a complex trait or what can be called polygenic was slightly pedantic and distracted from the biological message.

A conceptual comment:

• The conditional GWAS presented here is conceptually very similar to conditional QTL mapping approaches where candidate loci are included, a priori, as covariates in the model, and a scan is performed to search for additional modifiers. It is known that this approach increases power because the scan is performed on the residual trait variation (having accounting for effect of candidate loci). This is also the idea behind MQM mapping, although in the latter the inclusion is not restricted to candidate loci. Instead of including candidate SNPs as covariate the authors include TE-CHH methylation levels as a covariate as it is highly correlated with TE-CHG methylation. By doing this, the authors essentially "control" for any SNP affecting the covariance between CHG and CHH, even if these SNPs (and their genetic architecture) remain unknown. Hence, the conditional scan is mainly on the residual variation in TE-CHG methylation that is unique to this context (i.e. independent of CHH). That additional TE-CHG associated loci pop up in this scan is perhaps not so surprising.

The finding that this conditional GWAS yields again a handful of loci of that explain a considerable part of the trait (now residual trait) variation leads the authors to suggest that the genetic architecture underlying non-CG methylation of TEs is not "polygenic". I think this is semantics. All the authors have done is relegate any causal SNPs underlying the covariance between TE-CHG and TE-CHH to the right hand side of the equation of their GWAS model, and subsumed it under the predictor "TE-CHH methylation levels". That is, the genetic architecture underlying this covariance is still unknown, difficult to identify and probably highly polygenic.

The authors essentially decompose a complex traits into parts and map genetic architectures for each part. Although each part seems less complex and more oligogenic than polygenic, when putting all the parts back together, I would argue we are getting close to a complex trait with a polygenic architecture. The study by Hüther et al, which the authors also cite, is another example of how a complex trait can be decomposed into parts. In reference to one of the authors' GWAS associations, they say "...this association was also recently found by Hüther et al. (2022) using GWAS for unconditional mCHG levels of individual transposons. The MIR823A polymorphism appears to almost exclusively affect mCHG (Figs. S2, S3), primarily targeting the same transposons as a CMT3 knock-out...". In the case of Hüther et al., the complex TE-CHG methylation trait is simplified by selecting specific TEs, a priori, that are differential methylated in CMT3 knock-out lines. One could go on like this, and continue to peel away this complex trait. But, again, this does not mean that the overall TE-CHG methylation trait is not complex nor polygenic. It spirals down into a discussion of what is actually meant by "complex" or "polygenic", which is an interesting discussion, but - in the case - of this manuscript takes away from the biological message. My point is perhaps best reflected in the following statement from the discussion section: "Despite high heritability, univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic (Kawakatsu et al., 2016)." But a few lines below the authors seem to realize what they have actually done "We believe that, by controlling for mCHH, we have effectively simplified the trait, revealing genetic factors affecting mCHG only, perhaps by affecting the maintenance of this type of DNA methylation."

Specific comments

• A large part of the manuscript focuses on SNPs that enriched for a priori genes that fall below the genome-wide significance threshold. While I see the reasons for doing this in this particular manuscript, I do not see how this is useful in general (again this approach is partly "sold" on methodological grounds). The approach can obviously not be extended to study traits where a priori gene sets are unavailable or incomplete. Moreover, the "FDR" approach based on the a priori gene set labels GWAS hits that are not within the a priori set "false discoveries", which may or may not be true. Moreover, there is no "natural" stopping point for going below GWAS thresholds. An alternative, to this would be to perform a targeted GWAS for a priori genes (+ a LD window around them). Since this alleviates the multiple testing burden, I would be curious to see what this yields both in terms of conditional and unconditional analysis. Candidates that show a signal could be included as covariates and a conditional scan for unknown genes could then be performed.
• With regards to the CMT2 signals (particularly section "Further evidence for allelic heterogeneity at CMT2") it would have been useful/clearer to break down CHH into CWA and non-CWA.
• I understand that the authors set out to do this conditional analysis because previously no hits could be found for CHG TE methylation. However, have the authors considered going the other way around and performing a CHH|CHG analysis to find additional QTL affecting CHH methylation, partly indepedently of CHG?
• The authors write: "While both mCHG and mCG showed high heritability, GWAS yielded little in terms of significant associations. This might be because these "traits" are highly polygenic, or because they are at least partly transgenerationally inherited, and hence do not behave like standard phenotypes." Please clarify what they mean by "not behave like standard phenotypes".
• The authors write: "Our starting point is the observation that mCHG and mCHH levels on transposons are strongly correlated in the 1001 Epigenomes data set (Kawakatsu et al., 2016), especially for RdDM- targeted transposons (Fig. 1A; see Methods). Much of this variation ....". What is mean by "this variation"?
• A few lines below, they write "...huge". Please rephrase.
• The authors write: "sample data set ("Leaf SALK ambient temperature"; n=846). Interestingly, the covariance between mCHH and mCHG showed the same pattern in data generated by knocking out known or potential DNA methylation regulators in the same genetic background (Fig. 1B) (Stroud et al., 2013). This demonstrates strong co-regulation of these types of methylation, in particular for RdDM-targeted transposons." It is noticeable that many double mutants are off the diagonal. To me this indicates that they affect one context more than the other (i.e. they break covariance). Second, it suggests that they are probably interacting non-additively. It would be great if the authors could comment on this observation; perhaps also later in the ms, where they make a case for additivity.
• The authors write: " it is difficult to say what fraction of these factors is genetic and what is environmental, but, regardless of this, we hypothesized that the substantial covariance could reduce power of GWAS for either mCHH or mCHG (when using a standard univariate model), and that an analysis accounting for this covariance might perform better...". The arguments given thus far are not sufficient to understand why a "substantial covariance" between traits would reduce the power to map individual traits. I think more needs to be done here to motivate this.
• The FDR analysis using a set of a priori genes should be explained in detail in this ms. It is cumbersome to go to another manuscript to see what was done exactly, especially since this information is also difficult to dig up in the Atwell 2010 study. Although I understand the idea behind this approach, I would be concerned that this type of "FDR" analysis assumes that that all methylation genes are known. A novel candidate that was perhaps never identified in mutants screens before would be classified as a false discovery. Similarly, known candidates that carry no functional polymorphisms in nature, perhaps because they are highly constraint, will never become a discovery.
• The authors write" "However, MSI1 is required to control DNA methylation via repression of MET1, and a loss of FAS2 in CAF-1 induces mCHG hypermethylation (Fig 1B) (Stroud et al., 2013; Jullien et al., 2008)...", where is the "FAS2 in CAT-1" result visible in Fig. 1B?
• The results presented in "A jmjC gene is a novel modifier of mCHG in RdDM-targeted transposons" could have been showcased better. Only after reading the methods part did I realize that the authors generated CRISPR mutants. It reads as if the authors just picked up some available loss of function mutants and profiled them. But, clearly, much more work was involved here and the authors could have brought that out more. Perhaps more generally, I think all the new functional analysis the authors perform is largely "under-sold" in this manuscript at the expense of unnecessary methodological/concpetual discussion (see point above).
• In section "The power and complexity of conditional GWAS", the authors write "The performance of GWAS relies on using the right model for the relation between genotype and phenotype. As with other statistical methods, using the wrong model may lead to unpredictable results." This seems like a too obvious of a statement.

Significance

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Sasaki et al titled "Conditional GWAS of non-CG transposon methylation in Arabidopsis thaliana reveals major polymorphisms in five genes" employed conditional GWAS to identify trans-regulators of mCHG levels in Arabidopsis natural accessions, after controlling for mCHH. Using loss of function mutants for couple of these genes, the authors also tested their effects on mCHG levels. Overall, this manuscript makes a nice contribution. I suggest the following improvements to enhance the quality of this manuscript.

Comments:

1. MSI1 has been shown to be copurified with TCX5, a component of DREAM Complex. The DREAM complex transcriptional regulates CMT3, MET1, DDM1 in a cell cycle dependent manner (ref: Yong-Qiang Ning, 2020 nature plants). Tcx5/6 double mutants have ectopic gain of TE and genic mCHG. It would be nice to refer this paper and add to the MSI1 part accordingly.
2. Multifaceted regulation of mCHG levels seems to be evident from this and previous studies. Why would such complex pathways evolv to regulate mCHG? Bewick et al 2016 and Wendte et al 2019 showed lack of CMT3 or ectopic expression of CMT3 can influence CG gene body methylation (gbM). One possibility is that these five factors regulate CHG to maintain it at a level that is just enough to target TE. Irrespective of the functional relevance of gbM, differences in the levels of these five factors might result in erroneous gbM. It would be interesting to look for the rates of gbM and number of gbM genes in the natural accession carrying 1 to 4 number of mCHG-decreasing alleles. Also, in the one line from Iberian peninsula carrying polymorphisms in all five genes.
3. The authors mentioned a significant peak for mCHG|mCHH on RdDM-targeted transposons was located 196 bp downstream of MIR823a and not on mature miRNA. Therefore, this cannot directly impair miR823 base pairing with CMT3 mRNA transcripts and its cleavage. Moreover, natural accessions carrying alternative MIRNA823 allele show reduced CMT3 and mCHG levels, meaning more miR823 levels? Does this 196 downstream region contain any regulatory feature that effects miR823 transcription? Or this region still falls in the primary miRNA hairpin region? A single nucleotide change in pri-miRNA can have a significant impact on its secondary structure that can impede DICER processivity and effectively levels of mature miR823 molecules? It will be beyond the scope of this paper to pin down the exact mechanism. But a simple stem loop RT-PCR for miR823 levels in reference and alternative accessions would be informative (on accessions that grow at the same speed). Perhaps, the authors can at least model SNP induced pri-miRNA secondary structure variations using Vienna RNAFold (http://rna.tbi.univie.ac.at/cgi-bin/RNAWebSuite/RNAfold.cgi) and present MEF values (maximum free energy) for representative accessions.
4. Figure 1A can be made more reader friendly. Perhaps this can be broken down into correlation plots for individual conditions or tissue types. In addition, it might be good to add individual r-square values for each of them instead of compound r-square.
5. Page 3, Paragraph 1 from line 3 to end of paragraph. The authors wrote "Much of this variation is due to differences in the environment (including tissue, which can be viewed as a cellular environment)". A possible explanation is these two tissues have different mitotic indices (fraction of cells diving and non-diving; flowers have more dividing cell, leaves have more non dividing and endoreduplicated cells) that explains non-CG variation. I would suggest authors to change the text to this and refer to Filipe Borges et al 2021 Current biology paper.

Significance

The manuscript by Sasaki et al titled "Conditional GWAS of non-CG transposon methylation in Arabidopsis thaliana reveals major polymorphisms in five genes" employed conditional GWAS to identify trans-regulators of mCHG levels in Arabidopsis natural accessions, after controlling for mCHH. Using loss of function mutants for couple of these genes, the authors also tested their effects on mCHG levels. Overall, this manuscript makes a nice contribution. I suggest the following improvements to enhance the quality of this manuscript.

Comments:

1. MSI1 has been shown to be copurified with TCX5, a component of DREAM Complex. The DREAM complex transcriptional regulates CMT3, MET1, DDM1 in a cell cycle dependent manner (ref: Yong-Qiang Ning, 2020 nature plants). Tcx5/6 double mutants have ectopic gain of TE and genic mCHG. It would be nice to refer this paper and add to the MSI1 part accordingly.
2. Multifaceted regulation of mCHG levels seems to be evident from this and previous studies. Why would such complex pathways evolv to regulate mCHG? Bewick et al 2016 and Wendte et al 2019 showed lack of CMT3 or ectopic expression of CMT3 can influence CG gene body methylation (gbM). One possibility is that these five factors regulate CHG to maintain it at a level that is just enough to target TE. Irrespective of the functional relevance of gbM, differences in the levels of these five factors might result in erroneous gbM. It would be interesting to look for the rates of gbM and number of gbM genes in the natural accession carrying 1 to 4 number of mCHG-decreasing alleles. Also, in the one line from Iberian peninsula carrying polymorphisms in all five genes.
3. The authors mentioned a significant peak for mCHG|mCHH on RdDM-targeted transposons was located 196 bp downstream of MIR823a and not on mature miRNA. Therefore, this cannot directly impair miR823 base pairing with CMT3 mRNA transcripts and its cleavage. Moreover, natural accessions carrying alternative MIRNA823 allele show reduced CMT3 and mCHG levels, meaning more miR823 levels? Does this 196 downstream region contain any regulatory feature that effects miR823 transcription? Or this region still falls in the primary miRNA hairpin region? A single nucleotide change in pri-miRNA can have a significant impact on its secondary structure that can impede DICER processivity and effectively levels of mature miR823 molecules? It will be beyond the scope of this paper to pin down the exact mechanism. But a simple stem loop RT-PCR for miR823 levels in reference and alternative accessions would be informative (on accessions that grow at the same speed). Perhaps, the authors can at least model SNP induced pri-miRNA secondary structure variations using Vienna RNAFold (http://rna.tbi.univie.ac.at/cgi-bin/RNAWebSuite/RNAfold.cgi) and present MEF values (maximum free energy) for representative accessions.
4. Figure 1A can be made more reader friendly. Perhaps this can be broken down into correlation plots for individual conditions or tissue types. In addition, it might be good to add individual r-square values for each of them instead of compound r-square.
5. Page 3, Paragraph 1 from line 3 to end of paragraph. The authors wrote "Much of this variation is due to differences in the environment (including tissue, which can be viewed as a cellular environment)". A possible explanation is these two tissues have different mitotic indices (fraction of cells diving and non-diving; flowers have more dividing cell, leaves have more non dividing and endoreduplicated cells) that explains non-CG variation. I would suggest authors to change the text to this and refer to Filipe Borges et al 2021 Current biology paper.

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Reply to the reviewers

Manuscript number: RC-2022-01392R

Corresponding author(s): Ilan Davis

General Statements

We thank the reviewers for their constructive and helpful comments on our manuscript. We are delighted to find their consensus that the manuscript represents a useful resource for the Drosophila community in particular, and for the fields of neural development and post-transcriptional gene regulation. The following is our detailed responses and plan for how we will address all the major points raised by the reviewers. We also plan to address all minor points fully and have been through them in great detail one by one, so we are confident this is feasible within a reasonable and expected time frame.

Description of the planned revisions

Reviewer #1

Major 1: For the wildtype CS flies, there is no YFP mRNA signal in neuroblast region and how about YFP mRNA signal in MB, OL VNC and NMJ regions? What is the criterion of setting laser power and gain for the mRNA level of 200 genes? Is it difficult to distinguish background and true signal of the mRNA in different area?

This is a good point about background intensity levels (from non-specific binding of the YFP smFISH probe) across different tissue regions. We thank the review for raising it. Signal:background decreases with depth in all of the tissues, with superficial cells displaying similarly high signal:background in the CNS and NMJ, while signal:background in neuropil regions of the CNS are slightly lower. To address this point, we plan to include a supplementary figure to show background fluorescence of the smFISH probe across all regions of the CNS and NMJ.

To address the point about image acquisition settings, we will included the following additional information in the Methods section (Page 17):

“Consistent image acquisition settings (laser power, pixel dwell time or camera exposure, detector gain) were used for experimental and control experiments. Acquisition settings were optimized to achieve fast acquisition and high signal:background for each instrument.”

We will add a further explicit explanation to the manuscript referring to previous publications, that the nature of the smFISH method makes it relatively simple to distinguish background from true signal. True punctae have a relatively uniform size, symmetrical shape, and consistent intensity distribution. Whereas background punctae that are either larger than diffraction-limited punctae or have lower intensity can easily be separated from real signal.

Major 2: Would the insertion of YFP affect gene expression? Comparing to CS in Fig 1K, the dlg1 mRNA signals in dlg1::YFP line (Fig 1F) increases a lot. I do not know if this phenotype happens only in this area. So could you show some other regions for dlg1::YFP flies.

This is a good point raised by both Reviewer #1 and Reviewer #2 (Major point 1). We agree that a proper quantification of the effect of YFP-insertion will bolster our conclusion, highlighting the utility of protein-trap collections for systematic analysis of post-transcriptional regulations. To address this, we plan to: (i) provide quantifications of dlg1 transcript expression in the CNS and NMJ and compare the levels between dlg1::YFP and wild-type lines, and (ii) provide new figure visuals reflecting our quantification results.

Major 3: Is the dlg::YFP homozygous available? Among 200 gene trap lines, how many of them can be homozygous?

This is a good point raised by both Reviewer #1 and Reviewer #3 (Major point 1). The dlg1::YFP (CPTI-000207) line used for the control experiments is homozygous. However, it is a great point that not all of the YFP insertions are homozygous viable. Out of the 200 lines we screened, 131/200 (65.5%) insertions are homozygous viable, whereas 69/200 (34.5%) are homozygous lethal or are unknown. We have addressed this caveat in the Methods section (Page 16) with the following statement:

“The majority of YFP insertion lines are homozygous (65.5%, 131/200), those that are not homozygous viable were kept over balancer chromosomes.”

Our provisional analysis shows that the number of nervous system compartments expressing YFP-fused protein or mRNA are not affected by homozygous lethality. We plan to include this analysis in the revised manuscript.

Major 4: Have you tried to investigate the mRNA and protein localization in adult brains?

Yes, in a related study, we demonstrated that this approach also works in the adult brain (Mitchel et al., 2021, DOI:10.7554/eLife.62770). A systematic analysis of protein and mRNA expression patterns in the adult brain would be highly interesting and is certainly possible, however it is beyond the scope of the manuscript. To address this point, we will cite our related work and emphasise more clearly the wider applicability of our technique.

Major 5: In Fig 3C, the authors claimed in MB or OL soma regions, some genes are protein expression only but no mRNA present. I wonder how do you explain this phenotype in soma.

Our favoured explanation is that protein is more stable than mRNA. Therefore, after the mRNA is translated, it could get degraded while the protein is still present in the cell. We will add text in the relevant section to mention potential differential stability of protein/mRNA.

Major 6: Since sgg mRNA localize to both sides of NMJ, would KCl stimulus affect sgg mRNA amount and localization in muscle?

That is an interesting question. The data in Fig. 8I-J show that there is no additional Sgg::YFP protein accumulation at the muscle post synaptic density in response to KCl stimulus. It’s been shown elsewhere (Ataman et al., 2008, DOI:10.1016/j.neuron.2008.01.026) that Sgg protein translocates to the muscle nucleus in response to KCl stimulus. Determining whether that mechanism requires translation of new protein would require a complete new study with translational analysis and would distract from the message of the current study.

Reviewer #2

Major 1: Although the group is using an established and published set of gene traps, it would be good to confirm protein expression for same gene to increase confidence or provide more details on how is known that the YFP insertions do not affect mRNA stabilization or transcription or protein expression/localization. For example in Figure 1 F' versus K it is unclear why in the DlgYFP insertion there are more Dlg in situ signals than are observed in and around a neuroblast as compared to the wild type control. From the description provided these appear to the maximum intensity images. Is this due to background or an effect of the YFP insertion itself? Because of the increased level of expression is there a feedback loop of the protein regulating the mRNA expression? If had expression of Dlg protein in this figure would also confirm the YFP insertion mirrored the endogenous and it would be easier to discern if there were any changes in the number of Dlg mRNA molecules present. As this was the proof of principle example for the screen this information would increase confidence in the remainder of the data presented. AS an important part of the screen is looking at the potential for post transcriptional regulation this is an important factor to address.

Thank you for the valuable suggestion. We agree with the reviewer that the comparison of dlg1 transcript levels would provide a valuable control. This point was raised by both Reviewer #1 and Reviewer #2. Please see [Reviewer #1 - Major point 2] for our response.

Major 2: Will this pipeline capture information on whether is secreted (contain a signal regulatory peptide) or not as then would expect to be discordant. This should be clarified or commented on.

The reviewer’s comment is correct. Secreted proteins may show discordant distribution of protein and mRNA between cell types even in absence of post-transcriptional regulations. Note that Shaggy (Sgg) is a secreted protein but we observe that most of the protein products are expressed in the same cell as the RNA. We propose to follow the reviewer’s suggestion and revise the text to discuss the limitation of our pipeline in identifying proteins regulated via secretory modes.

Major 3: General molecular function is listed in supplementary table 1 but will other types of information be able to be correlated from datasets or databases as well.

This question highlights a major feature of our dataset and associated metadata The analysis in Supplementary Table 1 is used to assess the functional representation of the 200 genes in our screen against the all known genes. We found that ~90% of GOSlim terms are covered by the 200 genes, highlighting the diversity of our list of genes. On the other hand, our Zegami resource (Accompanying data for Zegami) contains a rich collection of metadata (including the full list of GO terms) associated with each gene in the dataset, and extends that information to the entire genome. We anticipate that the Zegami resource will be a valuable platform to query data from our analysis and other databases. To address this, we plan to: (i) revise the legend for the Supplementary Table 1, and (ii) revise the text to clarify what kind of information is available in our Zegami resource.

Reviewer #3

Major 1: The approach relies on gene traps that often fail to be made homozygous, presumably due to deleterious function of the YFP insert. This is an obvious limitation of the study, which the authors address, but do so insufficiently by only analyzing a single case Dlg1. The authors should report how many of the 200 YFP-traps can produce viable homozygous animals, whether phenotypes can be observed, and any other relevant information to assess the functional properties of the tagged genes.

Thank you for requesting further information on homozygous viability of the YFP-trap collection. This point was raised by both Reviewer #1 and Reviewer #3. Please see [Reviewer #1 - Major point 3] for our response.

Major 2: The term "discordant" is used for non-congruous RNA/Protein levels in soma and distal processes, and sometimes the two are analyzed in the same figure (e.g Fig 3A). When it is stated that 98% of genes are discordant, this is an over-simplification as what the authors describe as "discordant" is expected to occur frequently in the distal process, but less often in the soma (which is what the authors find when presenting the data for individual compartments - Fig 3B-C). This is confusing because the observation means completely different things in the two compartments, though both are interesting to describe. These analyses, and their interpretation, should be kept separate.

This is a fair point raised by the reviewer. To address this point we plan to: (i) prepare two separate tables summarising our annotation in soma and neurite compartments, and (ii) revise the text accordingly to explain and discuss how the discordant protein and mRNA expression pattern can arise both within different compartments of a cell or between different cell types in a cell lineage

Major 3: There is not enough emphasis placed on the cell-type specific regulation of RNAs. There are very few studies that have investigated how localization of individual RNAs changes in different cell types or regions of the nervous system, and the authors find that this is quite prevalent. Therefore, the rather superficial analysis of these data fails to take advantage of a major strength of the data. For example, for the discordant genes that differ in neuropil localization between different regions of the CNS, what types of molecules do they encode, what is their function in neurons (if known), and why might they be required locally in one region of the CNS but not the other?

We appreciate that the Reviewer recognizes the power of comparing RNA localization patterns across different brain regions (Figure 5R). We reported on a common set of synaptic mRNAs that encode nuclear proteins across the different regions of the nervous system. Per the Reviewer’s suggestion, we have begun to look into region-specific patterns of expression. In Figure 5R, two categories with the largest number of genes are ‘protein_MB_syn’ and ‘protein_OL_syn’, which contain proteins that are specific to those regions. However, given the small number of 15-16 genes, gene ontology enrichment analysis has limited power to infer information on the entire genome.

We plan to revise the manuscript:

to include tables with lists of genes specific to MB and OL regions. to revise the manuscript to include in the discussion a caveat of the limited power of analysis based on a small number of genes.

Major 4: The authors conclude that mRNA and protein co-localization in glia processes shows that mRNA localization makes a major contribution of the proteome in processes. However, there is not enough evidence for such conclusion since neither translation of these mRNAs nor lack of protein trafficking from the somas was shown.

The significant role of RNA localisation in shaping the local proteome and performing proteostatic regulation has been studied in detail (Zappulo et al., 2017, von Kugelgen and Chekulaeva 2022 Giandomenico et al., 2022). However, the reviewer’s comment is correct that we do not show direct evidence of mRNA translation or protein trafficking. Therefore, we propose to: (i) clarify the text by including the citation of these publications, and (ii) qualify our claim that mRNA localization is a major contribution of the proteome in neurite or glial processes.

Zappulo et al., 2017, DOI: 10.1038/s41467-017-00690-6

von Kugelgen and Chekulaeva 2022 DOI: 10.1002/wrna.1590

Giandomenico et al., 2022, DOI: 10.1016/j.tins.2021.08.002

Major 5: An important caveat of this technique that should be discussed is the lack of knowledge about the translation of these mRNAs, if the mRNA that is being detected is the same as the one that is translated. While the authors emphasize the discordance between mRNA and protein localization, it is not possible to know whether these mRNAs are being translated where they are found, e.g. soma vs neuropil. Moreover, there are many examples (e.g. BDNF) where the isoform influences the subcellular localization of the mRNA. There is no way of studying the isoforms here, and we could be looking for a different mRNA isoform localized to a specific compartment compared to the protein. These points must be discussed.

We agree with the reviewer that our method does not provide information on whether the detected mRNA is being translated in time and space. Elucidating the relative contribution of localised mRNA in shaping the local proteome is not a trivial task and it is being actively investigated in the field. However, we believe our dataset provides a unique high-resolution map of transcripts that are potentially regulated at post-transcriptional and translational levels. It would be promising to follow up the ‘discordant’ genes identified from our survey using experimental methods that are able to track mRNA-ribosome associations (e.g. TRICK) in future studies. To address this point, we will revise the text to discuss this caveat.

Thank you for pointing out the matter with mRNA isoforms. Our preliminary analysis indicates that 71% of the screened genes have constitutive YFP-insertions (i.e. YFP-cassette traps all mRNA isoforms). However, we agree that our approach cannot discriminate the case where protein produced from an mRNA isoform is trafficked and co-localises with another mRNA isoform that did not give rise to that protein. We plan to revise the text to discuss this point explicitly.

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

Several minor comments regarding typos and simple errors have already been incorporated in the transferred manuscript. The changes are highlighted in yellow in the revised submission.

We plan to address all the useful numerous minor comments that the reviewers have kindly highlighted to us. We feel these are straightforward to do and feasible in a short time, so do not require a detailed listed plan. If the reviewers feel they do afterall need such a list, we will be happy to provide it. However, there is one minor comment that we feel requires a little more explanation:

Description of analyses that authors prefer not to carry out

Reviewer #3 - Minor Comment on Figure 8: “...____they should characterize the (khc) mutant NMJs: what is the change in size, synapse number, etc..

The khc mutants are already known to show synapse morphology phenotypes (Kang et al., 2014), though the khc23/khc27 transheterozygous allele has previously been used to assess localization defects at the larval NMJ (Gardiol and St. Johnston, 2014). Moreover, our manuscript (Figure 8) focuses on post-developmental stimulus-dependent processes, rather than cellular-level synapse developmental parameters with this mutant. The reviewer correctly points out that the khc developmental phenotypes are likely to have other secondary defects as a result of impaired microtubule transport. The purpose of that mutant was to assess the molecular-level question of whether microtubule-based transport is required for sgg mRNA localization at the axon terminal. The consequences and exact mechanism of disrupted transport are beyond the scope of this study. To address this point explicitly, we will:

Revise the manuscript to quote more explicitly and clearly the developmental khc phenotype. Revise the manuscript to explain the difference between the developmental role of khc and role in the transport of sgg specifically to the axon terminal. Revise the manuscript to explain more explicitly the limitations of this mutant.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors address the important topic of post-transcriptional gene regulation using the larval nervous system in Drosophila. They utilize a novel approach taking advantage of existing protein trap library, which permits use of the same smFISH probe to detect an array of 200 RNAs and visualize their corresponding protein expression. Furthermore, the authors developed a computational pipeline to visualize and analyze the resulting data, which should enhance the application of this method by other researchers. A major strength of the data comes from the analysis of multiple cell types in distinct compartments of the nervous system, cell types (neuron, glia, neuroblast), and subcellular domains. From the cumulative data, the authors are able to describe several interesting observations relating to cell-specific post-transcriptional regulation, regulation within a central-neuroblast lineage and glial post-transcriptional regulation, among others.

However, in spite of these strengths, there are several concerns related to the organization and interpretation of the manuscript that the authors should address in order to improve the manuscript:

General concerns:

1. The approach relies on gene traps that often fail to be made homozygous, presumably due to deleterious function of the YFP insert. This is an obvious limitation of the study, which the authors address, but do so insufficiently by only analyzing a single case Dlg1. The authors should report how many of the 200 YFP-traps can produce viable homozygous animals, whether phenotypes can be observed, and any other relevant information to assess the functional properties of the tagged genes.
2. The term "discordant" is used for non-congruous RNA/Protein levels in soma and distal processes, and sometimes the two are analyzed in the same figure (e.g Fig 3A). When it is stated that 98% of genes are discordant, this is an over-simplification as what the authors describe as "discordant" is expected to occur frequently in the distal process, but less often in the soma (which is what the authors find when presenting the data for individual compartments - Fig 3B-C). This is confusing because the observation means completely different things in the two compartments, though both are interesting to describe. These analyses, and their interpretation, should be kept separate.
3. There is not enough emphasis placed on the cell-type specific regulation of RNAs. There are very few studies that have investigated how localization of individual RNAs changes in different cell types or regions of the nervous system, and the authors find that this is quite prevalent. Therefore, the rather superficial analysis of these data fails to take advantage of a major strength of the data. For example, for the discordant genes that differ in neuropil localization between different regions of the CNS, what types of molecules do they encode, what is their function in neurons (if known), and why might they be required locally in one region of the CNS but not the other?
4. The authors conclude that mRNA and protein co-localization in glia processes shows that mRNA localization makes a major contribution of the proteome in processes. However, there is not enough evidence for such conclusion since neither translation of these mRNAs nor lack of protein trafficking from the somas was shown.
5. An important caveat of this technique that should be discussed is the lack of knowledge about the translation of these mRNAs, if the mRNA that is being detected is the same as the one that is translated. While the authors emphasize the discordance between mRNA and protein localization, it is not possible to know whether these mRNAs are being translated where they are found, e.g. soma vs neuropil. Moreover, there are many examples (e.g. BDNF) where the isoform influences the subcellular localization of the mRNA. There is no way of studying the isoforms here, and we could be looking for a different mRNA isoform localized to a specific compartment compared to the protein. These points must be discussed.

Minor suggestions:

• The authors should identify GO terms to understand what types of molecules are subjected to RNA regulation. They provide a supplementary table for all genes, but it would be useful to have a chart showing the proportion of different GO terms represented in the overall gene set, genes that show cell-specific regulation, genes that show neuron vs glia specific regulation, etc.
• "However, post-transcriptional regulation can also manifest itself within a cell, so that a protein is localised to a distinct site from the mRNA that encodes it". While subcellular RNA localization may represent a regulatory layer, I do not agree that proteins that function in the cell at a different location than their translation site represents regulation per se. Many such cases exist for proteins that are trafficked!
• "The majority of individual puncta appearing in the dlg1::YFP line (51% in the brain, 64% in larval muscles". Why is the agreement between YFP and endogenous FISH so low? Do many individual RNAs fail to hybridize? This should be discussed.
• "However, one gene, indy, is highly transcribed in neuroblasts and a single ganglion mother cell before it is rapidly shut off (Figure S1A)". This figure does not exist. Where are the data?
• The authors should be consistent about calling perineurial or perineural glia (both correct) in their images and text.
• "We only observe a minority of localised axonal mRNAs that lack the protein they encode at the axon extremities, in contrast to our findings in the mushroom body, optic lobe, and ventral nerve cord neuropils" These results are not contrasted, as in all neuropils the minority of localized mRNAs are those lacking their corresponding proteins. For example, 9% in NMJ vs 7.5% in OL neuropil according to Fig. 1B. What is conflicting with the conclusion?
• "These results suggest that motor axons are more selective than the other neuronal extensions in the mRNAs that are transported over their very long distances from the soma to the neuromuscular synapse" The current literature says that the same mechanism (cis-elements) is used to transport mRNAs to subcellular compartments, which would be inconsistent with the idea of motor axons being "more selective" than other neurons for the same mRNA, but just a result of fewer mRNAs being found in motor neurons: 34.% of the mRNAs are found in motor neurons soma vs 83% in OL soma, 86.5% in VNC soma, and 70.5% in MB soma. To get to this conclusion, the authors should show that mRNAs previously found in the neuronal extensions of other neurons are not found in the axons of motor neurons but are still expressed in thesir somas. They might want to suggest different RBPs involved in the transport or discussing the very long distance they need to travel which can influence their detection in the tips. Figures
• Figure 1. Experimental approach summary
  • Some colors do not show well and should be changed, e.g: grey in Fig. 1A, and Fig. 1B probe sites indicated in light blue and pink within the introns of dlg1.
  • Fig. 1E': There appears to be a large discrepancy in co-detection % for CNS and muscle in the graph judging by the size of circles, yet in the text, it is stated that there is average of 51% and 64% in the two, respectively. I don't see any green circles with over 25% agreement in the graph. Are the colors correct here?
  • Fig. 1D-I: It's difficult to identify where the zoomed panels come from. E has its own square (indicating zoom in E'). Please make this square dashed or a different color in E so it is clear F and G do not come from there.
  • Comparing Fig. 1F vs K: Why does there appear to be so much more dlg1 mRNA in the YFP-tag condition? If this is due to selection of imaging area, please choose a more similar region to image so the RNA levels are comparable. Otherwise it indicates the YFP-tag line has more RNA expression, which is likely not the case.
• Figure 2. Analysis pipeline overview
  • The lines for the first two zoomed panels are switched: The optic lobe is going to VNC and vice-versa.
• Figure 3. Overall summary of results
  • Figure 3A: Soma/Neuropil/muscle should be separate or at least ordered such that they are next to each other to facilitate direct comparison of genes in the same region of the cell in neurons from different CNS areas. Why are glia not included in this summary? A third color should be used to indicate when there is neither mRNA nor protein expression.
  • "Compiling all the information together shows that there are that 196/200 or 98% of the genes show discordance between RNA and protein expression" However, 5 genes shown in Fig. 3A do not show "discordance": CG9650, cup, Lasb, rg, and vsg!!
• Figure 4. Neuroblast lineage analysis
  • Is clustering around the NB sufficient to determine lineage relationship? There seems to be other neurons around the NB.
  • More examples should be shown for the post-transcriptional category, as it is the most interesting category, and there are many different possible outcomes. Are there cases of transcriptional control and post-transcriptional regulation? Are there cases where the youngest neurons (closer to the NB) in the progeny are expressing the protein while the oldest are not? If not, could this be an artifact from a slow translation and the protein being detected only after building up in the cell? Top1 protein (Fig. 4D) seems to be less expressed in the youngest neurons.
  • "The transcription rate of these genes, as indicated by the relative intensity of smFISH nuclear transcription foci, is similar across the neuroblast lineage, however protein signal is only detectable in a minority of the progeny cells (Figure 4E)". Many nuclei lack clear large spots, but have small spots indicative of RNA; how is this interpreted? Do they lack transcription, or is this due failure of the smFISH to capture all transcription sites? Were transcripts actually counted to assess cell-specific differences? This should be possible with smFISH
• Figure 5. RNA synaptic localization
  • A have global analysis comparison of all neuropil areas would be welcome in this figure.
  • "Surprisingly, another 59 transcripts are present at synapses without detectable levels of protein (Figure 5E-H)" This text does not correspond to Fig 5E-H but 5I-L. Where is the text about 5E-H?
  • For Fig. 5J and 5N RNA appears scattered regularly throughout the entire panel area. How sure are the authors that this is not due to poor signal/noise? For example, perhaps too much probe being used for these targets.
  • Fig. 5R is not cited in the text.
• Figure 6. RNA localization in glia
  • For Fig. 6B-G it is hard to tell if there is any overlap of the RNA and Glia. Maybe show multiple zoomed-in merged images and/or highlight the structures with lines that are present in all panels.
  • For Fig. 6L-O: How reproducible is this small amount of RNA puncta in the NMJ glia? Is this possibly biologically important?
  • Why do cartoons labelling subnuclear/perinuclear glia in Fig.6 and Fig.S6 show different localization?
  • The cartoons seem to extrapolate from the data: While in Fig 6B-D, we see neither the big bright spot of transcription in the glial nucleus nor as many transcripts in the neuropil, they are both present in the cartoon. In Fig. 6E-G there is no indication of cortical glia soma nor the transcription spot only in glia nuclei.
  • "To assess glial localisation for the 200 genes of interest, we used a pan-glial gal4 driving a membrane mCherry marker (repo-GAL4>UAS-mcd8-mCherry) to learn the expression pattern of all glial cells, and then classified the pattern in the YFP lines (without the marker) based on knowledge of that expression pattern. We validated this approach by combining the RFP marker" Did the authors use mCherry or RFP for these experiments? Also, the previous sentence is redundant.
• Figure 7. RNA localization at neuromuscular synapse
  • RNA for these genes seems far too spread throughout the muscle to draw any conclusions
  • Also with so many RNAs distributed in the muscle, specific localization of RNA molecule to the precise PSD would have no conceivable benefit
  • I suggest drawing lines around the protein expression to facilitate visualization of the mRNA localization for panels B, F and J. It is especially hard to conclude anything from panels B and F.
  • Light grey with white dots is hard to see in the cartoons
• Figure 8. Role of khc and activity in sgg localization
  • Presumably there is a huge number of developmental problems associated with this mutant that could cause decrease in sgg localization
  • If the authors include this, then they should characterize the mutant NMJs: what is the change in size, synapse number, etc..
  • Is there more sgg accumulated in soma as a result of less transport? Is sgg being expressed at the same level?
  • Fig. 8F-H: Why is Dlg1 accumulated in the entire axon, not just the presume synapse?
  • Fig. 8J: Why is sgg signal occurring in circles disconnected from the main axon? The authors should show a different image

Significance

This is a significant and complex paper that contributes with novel tools to an important issue

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Referee #2

Evidence, reproducibility and clarity

Summary

Titlow et al present a data resource paper for mRNA localization and protein expression in vivo focusing on the larval nervous system which is an area of high interest currently. They screen a known group of YFP gene trap lines (200 lines) and looked at specific aspects of the nervous system such as expression in neuroblasts, the mushroom bodies, glia or the NMJ. They also present a computational workflow using this set of 200 genes for the investigation of the subcellular localization and potential role of post transcriptional regulation in whole larval tissues. This uses the image data obtained experimentally and then compares with existing datasets to obtain more information.

Major comments

The authors results largely support the claims made in the manuscript. Is a clear proof of concept analysis of specific examples and then presentation of examples from different part of the nervous system. Different aspects of the gene trap lines are taken into account. Is a high level analysis of the sub cellular localization of mRNA and protein in different parts of the nervous system. Some interesting new insights which can lead to more in depth analysis of mechanism are presented. Is an interesting idea and presents a method in which to approach a fieId that has many remaining open questions. This manuscript is an important and timely analysis that will be of high interest in the field.<br /> Is a positive that the authors confirmed the YFP mRNA in situs with an endogenous gene in situ. Although the group is using an established and published set of gene traps, it would be good to confirm protein expression for same gene to increase confidence or provide more details on how is known that the YFP insertions do not affect mRNA stabilization or transcription or protein expression/localization. For example in Figure 1 F' versus K it is unclear why in the DlgYFP insertion there are more Dlg in situ signals than are observed in and around a neuroblast as compared to the wild type control. From the description provided these appear to the maximum intensity images. Is this due to background or an effect of the YFP insertion itself? Because of the increased level of expression is there a feedback loop of the protein regulating the mRNA expression? If had expression of Dlg protein in this figure would also confirm the YFP insertion mirrored the endogenous and it would be easier to discern if there were any changes in the number of Dlg mRNA molecules present. As this was the proof of principle example for the screen this information would increase confidence in the remainder of the data presented. AS an important part of the screen is looking at the potential for post transcriptional regulation this is an important factor to address Will this pipeline capture information on whether is secreted (contain a signal regulatory peptide) or not as then would expect to be discordant. This should be clarified or commented on. General molecular function is listed in supplementary table 1 but will other types of information be able to be correlated from datasets or databases as well.

Minor comments

On page 9 refer to Figure 6S which I think is supposed to be Figure S6. In text refer to an example of gli but show gs2 in the figure so it is unclear what is being referred to or shown. Could include more description on the generation of the supplementary tables and analysis of the tables. I could not find any description/legend which made analysis of some of the tables more difficult. The data set was trained on a known set of data (analyzed by experts. It would be interesting to see what it could do with a novel set of genes in the context of post transcriptional regulation, but that is beyond the overall scope of this manuscript.

Significance

This is an interesting idea and is a useful resource for the genes analyzed. Gives an initial tool to analyze the expression of genes. Allows for systematic analysis of mRNA (smFISH) and protein on a larger scale but with high resolution. Adds new knowledge in terms of the localization of mRNAs and protein in the periphery of neural and glia processes which may inform future analyses of the role of these genes in these tissues.

Is a useful resource within neurodevelopment in Drosophila and post transcriptional regulation. Would be of interest to a general audience as workflow could be applied to any tissue or set of genes. Covers a very broad set of genes with disparate biological functions again making this of interest to a broader audience.

Expertise of reviewer Drosophila, neurodevelopment, RNA regulation, post transcriptional regulation, polarity and adhesion.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Titlow et al. systematically analyzed spatial distribution of 200 gene's mRNA and protein, and found common discordance between them. Moreover, the browsable resource is pretty useful to most fly people. Though the authors did huge amount of experiments and analysis, and got several really interesting findings, there are some basic questions need to be answered.

Major 1: For the wildtype CS flies, there is no YFP mRNA signal in neuroblast region and how about YFP mRNA signal in MB, OL VNC and NMJ regions? What is the criterion of setting laser power and gain for the mRNA level of 200 genes? Is it difficult to distinguish background and true signal of the mRNA in different area?

Major 2: Would the insertion of YFP affect gene expression? Comparing to CS in Fig 1K, the dlg1 mRNA signals in dlg1::YFP line (Fig 1F) increases a lot. I do not know if this phenotype happens only in this area. So could you show some other regions for dlg1::YFP flies.

Major 3: Is the dlg::YFP homozygous available? Among 200 gene trap lines, how many of them can be homozygous?

Major 4: Have you tried to investigate the mRNA and protein localization in adult brains?

Major 5: In Fig 3C, the authors claimed in MB or OL soma regions, some genes are protein expression only but no mRNA present. I wonder how do you explain this phenotype in soma.

Major 6: Since sgg mRNA localize to both sides of NMJ, would KCl stimulus affect sgg mRNA amount and localization in muscle?

Minor 1: You claimed that Fig 1E shows high magnification image of the inset in D, but the scale bars are the same.

Minor 2: Figure 1 legend: K-N, are the images individual channels shown in E? Or in J?

Minor 3: In Fig 2A, optic lobe neuropil and VNC neuropil are mislabeled.

Minor 4: Only one panel has scale bar in Fig 4.

Minor 5: What is Fig 5B'and F'? You should describe them in the Figure legends.

Significance

The browsable resource is pretty useful to most fly people. The authors did huge amount of experiments and analysis, and got several really interesting and important findings.This work will provide mRNA localization information for post-transcriptional regulation studies.

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Reply to the reviewers

General Statements [optional]

We are grateful for the very kind, thoughtful, and detailed comments of the reviewers, which we have strived to fully integrate into the revised manuscript.

Of note are the concerns with the data from stages S21 and S22, which we acknowledge do appear to be qualitatively and quantitatively distinct from the other samples. While we are unable to completely disambiguate meaningful biological variation from technical or experimental noise using our data, we hope a few additional analyses and visualization tools we have included can provide greater confidence in the reliability of our findings.

Additionally, while attempting to evaluate Reviewer #2’s suggestions about examining the distribution of intergenic peaks along the genome, we discovered an error in our code that resulted in the improper assignment of peak categories. The error resulted in the improper assignment of intronic and exonic peaks as intergenic peaks. While the largest group of peaks in our dataset remains distal intergenic peaks (30.2%), and distal intergenic peaks remain a larger proportion of our intergenic peaks than proximal intergenic peaks, many of the peaks originally assigned to the intergenic categories have been reclassified as exonic or intronic peaks. We have updated our code and figures upon reanalysis of our data and have revised our findings and discussion accordingly.

Description of the planned revisions

Reviewer #3, Comment #3 of 11_

“In general, I thought that the bioinformatic methods (i.e., the code or the options used for each program) would have been helpful for my understanding in some cases. The authors say that these will be published on an accompanying GitHub repository, which should be fine if this is sufficient for journal policy.”_

We are still at work compiling the code for our analyses into a more reader-friendly form and setting up a GitHub repository to enable easy access to more detailed methods for interested readers. Some of the most important settings have been included in the Methods and Supplementary Methods sections, but we hope to include more thorough detailing of our pipelines in the GitHub repository. The raw data for portions of the RNA-Seq and all of the ATAC-Seq data have been uploaded to the Sequence Read Archive, and we are finalizing additional raw data submission. We are also in the process of determining what data to include in our Gene Expression Omnibus submission, which we hope to include all pertinent final data analysis files as well as any intermediate or accompanying datasets which would facilitate downstream analyses. The large size and number of our final analysis files has resulted in some challenges with data transfer and storage, which has delayed the upload and submission process.

We are also collating several of the data visualization scripts built for this manuscript into a Jupyter notebook. This tool will enable the visualization of ImpulseDE2 models and peak classifications for arbitrary genes and genome regions of a user’s choice, alongside additional functions which are discussed in this revision plan.

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

We have addressed the following substantive concerns with the manuscript:

Reviewer #2, Comment #2 of 3:_

“Authors have repeatedly used S21 and S22 throughout the manuscript to support their claims with clustering etc. May authors shed some light on the differences in replicates for these timepoints. Furthermore, I could not find Fig 3J, perhaps author would like to point out Fig 3H.”_

Reviewer #3, Cross-comment #2 of 3:_

“Focus on stages S21/S22: This might indeed be somewhat problematic. The libraries from these two stages (particularly S21) seem to be very different from those from the other stages. In the PCA (Fig. 1C), S21 doesn't cluster well with anything, and the difference between the two replicates is massive compared to other stages. The accessibility pattern (Fig. 1D) also looks odd. The libraries also have the lowest scores for % of mapped reads (Fig. S2B), fragment size distribution (S2E), and Spearman correlation (S2I). All this could be biologically sound and be due to a major developmental transition at this point, but maybe it justifies revisiting the data and testing whether leaving out S21 (and/or S22) makes a big difference for the clustering analyses.”_

1. Reviewers #2 and #3 discussed concerns with the outlying nature of libraries S21 and S22. We had also previously held concerns about these samples and had performed some analyses to examine whether the global properties of our dataset are dramatically changed upon removing those samples. We did not observe dramatic changes to the structure of our data in the absence of the S21/S22 samples.

   • a. Samples S21 and S22 appear to be highly separated from the rest of our data using Principal Components Analysis. We had also previously believed that this suggested that these samples might be problematic. However, a colleague indicated to us that researchers in microbiome ecology had observed similar phenomena, often caused by strong single axes of variation (or “linear gradients”) in the datasets. In “Uncovering the Horseshoe Effect in Microbial Analyses” (mSystems, 2017) by Morton et al., the authors describe how a strong linear gradient can create a “horseshoe effect” or “Guttman effect”, where PCA results in the two ends of a linear gradient appearing to come together in ordinal space. The authors also describe a similar “arch effect” which strongly resembles the general shape of our PCA curve. We suggest that the strong apparent “outlier” appearance of S21 and S22 may be exaggerated or induced by the technical “arch effect” phenomenon, and may be caused by a strong single biological gradient – a developmental timecourse – which our data aimed to capture.
   • b. We also performed PCA on our dataset with the S21 and S22 time points removed prior to performing the analysis (see right panel, bottom). When we did so, we observed that the relative positions of the remaining libraries remains largely similar, with time points closer to the middle of development showing a positive loading in PC2, and time points closer to the beginning and end of development showing a negative loading. This suggests that the second major axis of variation in our dataset would remain a contrast between middle vs. terminal timepoints, even without the S21/S22 data, and that the relative positioning of the remaining data within PC-space is not entirely driven by S21/S22.
   • c. To further assess the degree of the S21/S22 samples’ outlying effects, we also performed ImpulseDE2 analysis to generate model fits without S21/S22 data. Doing so allowed us to determine to what degree the S21/S22 stages are necessary for driving the accessibility trajectory of individual peaks, and of the data more broadly. We performed IDE2 with either all data, or the S21/S22 data removed prior to input into IDE2. This generated two sets of model fits to the “cloud” of accessibility vs. time measurements: one that included the S21/S22 data, and one without. We evaluated, for each peak in our dataset, the time point at which the IDE2 model achieved maximum accessibility (the “IDE2 max fit”), and plotted both the “all” and “noS21S22” data as a histogram (see right panel, top graph). The presence of peaks that achieve predicted maximum accessibility in the S21/S22 stages in the “no S21/S22” data is a result of how we calculate “max fit”, which does not require that there is a known accessibility value at a given timepoint; only that the time point during which the model fit is maximum is closest to the timing of that developmental stage. Overall, we still observed early, middle, and late enrichment of IDE2 max fit even when the S21/S22 data are removed. We do see a rightward shift in the middle timepoint histogram in the direction of later stages, although this may be expected given the absence of concrete accessibility values at S21/S22 in the “no S21/S22” data. This indicates that our data globally retain the general trends of early, middle, and late enrichment of accessibility in the absence of the S21/S22 data. Moreover, this suggests that, even without the S21/S22 data, the remaining data from early and late stages result in a model fit that still predicts maximum accessibility at middle developmental stages for many peaks.
   • d. To further measure the influence of the S21/S22 data in IDE2 model fit, we also evaluated the degree of change in the global behavior of a peak when the S21/S22 stages were removed. This analysis aimed to assess whether removing S21/S22 data resulted in an IDE2 model with the same general trajectory as with all data, as opposed to the more stringent requirement of evaluating whether the exact developmental stage of the peak was changed. To perform this analysis, we grouped developmental stages into five quintiles, each representing three stages of development. We asked, for each peak in our dataset, whether that peak’s IDE2 max fit was “stable” when the S21/S22 data were removed; that is, if the quintile of the IDE2 max fit was altered when the S21/S22 data were removed (i.e. if a peak moved more than 3 developmental stages away from its original position), a peak was considered “unstable”. We observed that over 80% of peaks in each quintile remained “stable” after removing the S21/S22 data, suggesting that the vast majority peaks show the same general trajectory of accessibility even without the S21/S22 data. Peaks within the middle time points appeared to be more unstable than peaks at the terminal timepoints, which could be expected given that the S21/S22 timepoints constituted the middle-most timepoints in our dataset.

We acknowledge that the S21/S22 timepoints still appear to be qualitatively different in other ways. Moreover, we acknowledge that some of the peaks in our dataset are “dependent” on the S21/S22 stages, given that their accessibility trajectory changes when these stages are removed. It is difficult to determine whether a change in accessibility trajectory for a given peak caused by the removal of S21/S22 data is indicative of technical differences in sample preparation, such as batch effects; biological variation, such as a potentially unknown mutant or sick embryo; or due to genuine wildtype biological processes that occur at the S21/S22 stages.

These caveats acknowledged, a comparative analysis of the data in the absence of the S21/S22 stages suggests that much of the global picture of development remains the same. In the interest of providing the data we generated as a resource, we decided to include the S21/S22 data in the final manuscript we have prepared for submission.

We have included an additional supplementary figure (Supp. Fig. 2.2) highlighting these further analyses, which we hope future readers will consider when performing their own analyses with these timepoints, as well as a summary of the ways we evaluated this potential concern in the Supplementary Methods. To facilitate future users of this dataset, we will include the model parameters calculated from IDE2 using both the full dataset and the data with S21/S22 removed in the GEO accession data, as well as a Jupyter notebook (ParhyaleATACExplorer.ipynb) that allows users to plot the raw accessibility data and IDE2 model fits for individual peaks of interest (C, example on right panel), so that downstream experiments can consider the potential differences with the S21/S22 samples.

Reviewer #2, Comment #3:_

“The majority of ATAC-seq peaks in the distal intergenic regions is a very surprising result. Authors defend this result by suggesting that this organism has big genome. May author perform a short analysis that shows that these peaks are indeed represent nearby genes or may point towards 3D genome organisation. For example, I see that this genome might have regions in the genomes that are densely organised in gene clusters, in those cases does the pattern remains same i.e he majority of the genes are very distant from each other and hence use vital regulatory elements?”_

Reviewer #3, Cross-comment #3 of 3:_

Peaks in distal intergenic regions: I agree that this could be elaborated on. It might also be that >10 kb is not actually that distal for Parhyale. I would suggest to split the "distal peaks" further (e.g., in 10 kb or 2-log steps, or whatever makes most sense) and try to understand if >10 kb is mostly <20 kb, or if most of them are hundreds of kb from the nearest gene?_

1. Reviewers #2 and #3 expressed interest in understanding the absolute distribution of distal intergenic peak distances from nearby genes in our dataset. In generating the analyses to address this question, we stumbled upon an error in our code that reveals that the true number of intergenic peaks is much lower than we had originally reported. We discuss the nature of the error below. Moreover, we address the previous question using the new data, which overall still indicates that distal intergenic peaks remain a large portion of the Parhyale genome.
   • a. To address Reviewer #2’s comments with respect to the presence of potential clusters of intergenic regions, we built a Python tool (included in ParhyaleATACExplorer.ipynb) enabling the visualization of different cis-regulatory element categories along a genomic coordinate. Upon plotting our data with this tool, we observed problems with the categorization of the peaks – namely, that intronic and exonic peaks were erroneously classified as intergenic peaks (see right panel, top). We analyzed our script for classifying annotations more carefully and realized that we had erroneously used “bedtools closest” instead of “bedtools intersect” to try to identify all peaks overlapping with gene annotations in our genome. We corrected this error and observed the expected distribution and categories of peaks in our data (right panel, bottom).
   • b. The revised peak categories have been added to the updated manuscript in Fig. 3H and Fig. 5C. The categories of peaks we observed differ substantially from our previous results, in that we observe a much higher representation of exonic and intronic peaks in our dataset, with intronic peaks now representing 28.2% of all peaks (increased from <1%), and distal intergenic peaks representing 30.2% (decreased from 51.2%). While distal intergenic peaks remain the largest category over time, the proportion is relatively equal to the fraction of intronic peaks. Intergenic peaks (distal and proximal combined) now make up only a slightly larger fraction of peaks (37.2%) than gene body peaks (exon, intron; total 34.4%). This updated result is a significant departure from our previous report, and we have updated the text of the manuscript to correct this mistake.-
   • c. While intergenic and distal intergenic peaks constitute a much smaller portion of our data, we still wanted to address Reviewer #2 and #3’s questions about the distribution of distances between intergenic peaks and nearby genes. We generated a plot to illustrate the number of intergenic peaks at variable distances to the nearest gene (B, right panel). As illustrated in the plot, there are a very large number of distal intergenic peaks, including many peaks >100kb away from the nearest gene. The average distance of intergenic peaks from the nearest gene was 73,351bp. We neglected to mention in the original manuscript that one of the rationales for choosing a 10kb cutoff as “distal intergenic” was that peaks beyond this distance would be considerably more difficult to isolate as single fragments combined with a proximal promoter using PCR, agnostic of their orientation with respect to the promoter element. Such peaks could not have been easily identified using previous transgenic approaches, and are thus distinguished from “proximal” peaks by their necessary identification using techniques such as ATAC-Seq. We have updated the text to reflect this distinction.
   • d. Given that both intergenic and gene body peaks appeared to comprise large fractions of our revised data, we also examined the relative enrichment of intergenic and gene body peaks with respect to time (after normalizing for the fraction of “unknown” peaks, as suggested by Reviewer #3). We observed that the proportion of peaks belonging to intergenic and promoter regions declined slightly as development progressed, while the proportion of gene body peaks increased (E, below). There appeared to be slightly more intergenic peaks than gene body peaks at all developmental time points, and the ratio of intergenic peaks to gene body peaks declined very slightly over time (F, below). These data indicate that intergenic and gene body peaks have different enrichment trajectories over time. As development progresses, gene body peaks are increasingly enriched, and may have a greater impact on gene regulation. We have added these additional observations to the text and to a new Supplementary Figure 2.3.

We have also addressed the following textual and conceptual concerns with the manuscript:

Reviewer #3, Comment #1 of 11_

I felt that the first paragraph of the introduction is not necessary._

1. We believe the introductory paragraph helps frame the paper in the context of the broader scope of advances in technologies for emerging research organisms – currently, it has become straightforward to both generate a genome sequence and to identify and manipulate coding genes of interest across diverse taxa, but the identification of gene regulatory mechanisms remains more difficult. We have edited the introduction to better reflect this perspective and to link the first paragraph to the rest of the paper.

Reviewer #2, Comment #1 of 3_

“In Introductory paragraph 2, sentence one, authors suggest that gene regulation plays more important role in evolutionary process than genes. Although a significant amount of research has been dedicated to gene regulation based evolution still this field is in nascent form. For example evidence of inheritance of the gene regulation pattern across generation is scarce and requires more evidence. I suggest authors to modulate the claim that still gene based evolution is the main paradigm instead otherwise.”_

Reviewer #3, Cross-comment #1 of 3_

Evolution via gene regulation vs. coding sequence: While (to my understanding) it is largely accepted in the field that changes to the CDS will often have more deleterious effects than changes to the expression of a gene, I agree that this could be elaborated on a bit.

1. As requested by Reviewers #2 and #3, we have clarified the language surrounding the debate between gene functional and gene regulatory evolution to indicate that both mechanisms appear to be important for evolutionary processes, with the importance of the latter more recently revealed.

Reviewer #3, Comment #2 of 11_

Use of Genrich: I presume this was run on both duplicates simultaneously? This is not clear from the methods section. It might have implications for downstream analyses (e.g., differential accessibility between time points) because running on both sequencing library replicates simultaneously leads to a single "replicate" of peaks per time point, while running it individually leads to two. However, I have never tested if this actually does make a difference. Maybe the authors have and can comment on this?

1. In response to Reviewer #3’s inquiry about Genrich, we have added additional clarifying information into the Methods section. “Genrich analysis was run on both duplicate libraries simultaneously; Genrich performs peak calling on each peak individually, and then merges the p-values of the replicates using Fisher’s method to generate a q-value, obviating the need to calculate an Irreproducible Discovery Rate (IDR).” We did not test running Genrich on individual libraries, opting for the more conservative approach of using the combined q-value as a filtering score for peak quality. For further information, the reviewer can see the Genrich Github repository section here: < [https://github.com/jsh58/Genrich#multiple-replicates]

Reviewer #3, Comment #4 of 11_

The section on the IDE2 models (the paragraph at the end of page 4/beginning of page 5) was unclear to me but appears sound. (The only instance where I didn't quite understand what the program actually does.) Maybe this can be explained a bit easier?_

1. As requested by Reviewer #3, we have attempted to explain the methods and logic of using ImpulseDE2 a bit more clearly:

“To identify regions of dynamically accessible chromatin, we used the ImpulseDE2 (IDE2) pipeline (Fischer et al., 2018). IDE2 differs from other software for differential expression analysis in that it allows the investigation of trajectories of dynamic expression over large numbers of timepoints. It does so by modeling a gene expression trajectory as an “impulse” function that is the product of two sigmoid functions (Chechik and Koller, 2009; Yosef and Regev, 2011). This approach enables the modeling of a trajectory of gene expression in three parts: an initial value, a peak value, and a steady state value, thus summarizing an expression trajectory using a fixed number of parameters. With the ability to capture the differences between early, middle, and late expression values for each gene in a dataset, IDE2 also enables the detection of transient changes in gene expression or accessibility during a time course. Identifying differential expression over large numbers of timepoints is difficult for more categorical differential expression software such as edgeR and DESeq2, which generally use pairwise comparisons between timepoints to assess change over time (Love et al., 2014; Robinson et al., 2010).”

Reviewer #2, Comment #2 of 3_

2-2) Authors have repeatedly used S21 and S22 throughout the manuscript to support their claims with clustering etc. May authors shed some light on the differences in replicates for these timepoints. Furthermore, I could not find Fig 3J, perhaps author would like to point out Fig 3H.

Reviewer #3, Comment #5 of 11_

On page 7, Fig.3J needs changing to 3H. This figure should, in my opinion, also contain the absolute number of peaks for each time point to set the individual proportions into context.

1. As requested by Reviewer #3, we have added a bar charts representing the number of peaks found at each time point (Fig. 3H) and the number of peaks found in each cluster (Fig. 5C) to the peak type proportion plots. We have also fixed references to Fig. 3J to instead refer to Fig. 3H – we apologize for the confusion.

Reviewer #3, Comment #6 of 11_

Last paragraph of the "Improving the Parhyale genome annotation" section: I think this needs to focus on those regions of the genome for which the location is known - after all, the "unknown" regions" could all be "distal transgenic", which would significantly change the relative proportions._

1. We have revised our analysis of this topic with our updated peak type proportions, as described above in point 2d above under “substantive concerns”.

Reviewer #3, Comment #7 of 11_

“On page 9, t-SNE is mentioned but doesn't seem to be cited.”

1. As requested by Reviewer #3, we have added citations for the t-SNE method, as well as scikit-learn, the software we used for t-SNE visualization.

Reviewer #3, Comment #8 of 11_

“The third paragraph on page 9 ("We evaluated the differences...") should mention the fact that clusters 1 and 2 are the only ones with significant proportions of exonic and intronic peaks. In the accompanying figure (5C), the total number of peaks would again be helpful.”_

1. After identifying the error in our peak category classification pipeline, this observation was no longer true. However, upon examining the new distributions by cluster, we observed that in Clusters 3–7, for which we observed GO enrichment for developmental processes, there appeared to be slightly higher enrichment of intronic regulatory elements than distal intergenic regulatory elements. These results resemble the observation from recent work showing that tissue-specific enhancers are enriched in intronic regions in various human cell types (e.g. Borsari et al. 2021, Genome Research). We have noted this new observation in the text.

Reviewer #3, Comment #9 of 11_

In figure 5D, I can't quite make out at which stage the dip in the peak of Cluster 8 occurs. This is quite an unusual pattern of accessibility change, and I can't help but wonder if it has something to do with the quality of one of the libraries? Also, the fact that half of the peaks fall into unmapped regions of the genome is unusual, and I feel this deserves more discussion._

1. In Figure 5D, Reviewer #3 asks about a dip in accessibility for Cluster 8 peaks. The dip in accessibility was actually observed for Cluster 9 peaks and is marked by the asterisk in that panel. We have updated the figure legend to clarify the significance of the asterisk and have referred readers to examine Supp. Fig. 5.1B, where the IDE2 model fits more clearly show a collective dip in accessibility for Cluster 9 peaks. Upon examining the size distribution of the clusters, we have also noticed that Cluster 8 is the smallest cluster. We have noted the small cluster size and high “unknown” peak enrichment for Cluster 8 in the text.

Reviewer #3, Comment #10 of 11_

“On page 10, the abbreviation PFM appears, but it is only explained in the legend of Fig.4. This should appear in the text.”_

1. Reviewer #3 mentions that on page 10, we use the abbreviation for position frequency matrices (PFMs) without previous reference. We first introduce the abbreviation on page 8, but given the repeated use of “PFM” on page 10, we have added an additional explanation of the abbreviation on page 10, for ease of reading.

Reviewer #3, Comment #11 of 11_

“The section on "Concordant and discordant expression and accessibility" is the one I disagree most with. The authors seem to suggest that a repressive cis-regulatory module should become less accessible when the gene is activated. However, they leave trans-acting factors completely out of their conceptualisation here. It is in general likely the availability of transcription factors that leads to repression, while the "silencer" can be well accessible in all cells. Moreover, it has become clear in recent years that CRMs are not just repressors or enhancers per se but can act as either depending on the availability of transcription factors. I think these facts could partially explain the weak correlation and should be discussed.”_

1. We appreciate the comments from Reviewer #3, which alerted us to the more recent literature around the bifunctional potential of regulatory elements. We have revised our claims to clarify that concordance and discordance analysis cannot be used to directly assign “enhancer” or “silencer” identity to given regulatory elements. Instead, we suggest that evaluating concordance and discordance can be useful for downstream users of our data, such as those aiming to build reporter constructs for a given gene of interest. To facilitate such tool development, we have built additional functions into a Jupyter notebook to enable the visualization of accessibility, gene expression, fold change of accessibility and gene expression, significance of fold change, and concordance/discordance assignment for arbitrary peak-gene pairs. An example of this visualization is shown on the following page. Panel A shows the region around the Engrailed-1 and Engrailed-2 loci in Parhyale (text labels within the plot region were added manually in Illustrator). Panel B shows visualization of the En1 promoter peak alongside En1 expression. Significant log fold changes (DESeq2 padj < 0.05) are marked by asterisks in the bar plots, and concordance/discordance assignment at each time point is indicated by the color of the comparison text (red = concordant, blue = discordant). Panels C and D show accessibility and expression visualization for a single peak (En1 peak5) compared to two nearby genes (En1 and En2). We hope to include sufficient documentation in our GitHub repository such that using these tools is accessible for most researchers, even with limited programming knowledge.

Description of analyses that authors prefer not to carry out

We were unable to easily visualize the distribution of regulatory elements across the whole genome as suggested by Reviewer #2. One challenge of working with the Parhyale genome is the lack of complete chromosomes. The genome is distributed across ~290,000 contigs of variable size. We were unable to find any software that could be easily and quickly set up to visualize our data, although we will provide in a Jupyter notebook the tools for local visualization of peak types that we developed.

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Referee #3

Evidence, reproducibility and clarity

In this study, Sun et al. use RNAseq and ATAC-seq in 15 stages of embryonic development of the amphipod crustacean Parhyale hawaiensis to analyse gene regulation genome-wide. They assess the data in multiple ways to provide a more complete genome annotation, understand temporal changes in gene regulation, and identify different classes of cis-regulatory elements including associated GO terms and putative transcription factor binding site enrichment. The authors have made a great effort to account for potential biases in their datasets (one impressive example is the comparison of multiple transcriptome assemblies and the following quality assessment) and I enjoyed reading this manuscript for its great explanations of method usage (i.e., what each bioinformatic package does, why it was used etc.) and the overall style.

I want to make a few suggestions that would make the study - in my opinion - even better:

• I felt that the first paragraph of the introduction is not necessary.
• Use of Genrich: I presume this was run on both duplicates simultaneously? This is not clear from the methods section. It might have implications for downstream analyses (e.g., differential accessibility between time points) because running on both sequencing library replicates simultaneously leads to a single "replicate" of peaks per time point, while running it individually leads to two. However, I have never tested if this actually does make a difference. Maybe the authors have and can comment on this?
• In general, I thought that the bioinformatic methods (i.e., the code or the options used for each program) would have been helpful for my understanding in some cases. The authors say that these will be published on an accompanying GitHub repository, which should be fine if this is sufficient for journal policy.
• The section on the IDE2 models (the paragraph at the end of page 4/beginning of page 5) was unclear to me but appears sound. (The only instance where I didn't quite understand what the program actually does.) Maybe this can be explained a bit easier?
• On page 7, Fig.3J needs changing to 3H. This figure should, in my opinion, also contain the absolute number of peaks for each time point to set the individual proportions into context.
• Last paragraph of the "Improving the Parhyale genome annotation" section: I think this needs to focus on those regions of the genome for which the location is known - after all, the "unknown" regions" could all be "distal transgenic", which would significantly change the relative proportions.
• On page 9, t-SNE is mentioned but doesn't seem to be cited.
• The third paragraph on page 9 ("We evaluated the differences...") should mention the fact that clusters 1 and 2 are the only ones with significant proportions of exonic and intronic peaks. In the accompanying figure (5C), the total number of peaks would again be helpful.
• In figure 5D, I can't quite make out at which stage the dip in the peak of Cluster 8 occurs. This is quite an unusual pattern of accessibility change, and I can't help but wonder if it has something to do with the quality of one of the libraries? Also, the fact that half of the peaks fall into unmapped regions of the genome is unusual, and I feel this deserves more discussion.
• On page 10, the abbreviation PFM appears, but it is only explained in the legend of Fig.4. This should appear in the text.
• The section on "Concordant and discordant expression and accessibility" is the one I disagree most with. The authors seem to suggest that a repressive cis-regulatory module should become less accessible when the gene is activated. However, they leave trans-acting factors completely out of their conceptualisation here. It is in general likely the availability of transcription factors that leads to repression, while the "silencer" can be well accessible in all cells. Moreover, it has become clear in recent years that CRMs are not just repressors or enhancers per se but can act as either depending on the availability of transcription factors. I think these facts could partially explain the weak correlation and should be discussed.

Significance

This manuscript will greatly advance research in the emerging model organism Parhyale through a more complete genome annotation and vast amounts of gene expression and chromatin accessibility data (and accompanying analyses) at various stages of development. However, the impact goes far beyond the Parhyale community, and I believe this paper can be seen as a blueprint for similar studies in other organisms. The excellent documentation and comparison of their bioinformatic methods makes their re-use straightforward and much of the authors' pipeline can be used for a "standard" ATAC-seq data analysis - I am likely to use many of their methods myself. Therefore, I think the audience can range from the "classic" evo-devo community to developmental biologists, scientists interested in gene regulation in general, and bioinformaticians.

My own expertise is in gene regulation through transcriptional control, and I use different seq approaches (ATAC, CUT&RUN, RNAseq) to study this process.

Referees cross-commenting

Thank you to my colleagues for their comments. Since Reviewer 1 was happy with the manuscript as it is, I'll only add my views to the points raised by Reviewer 2: - Evolution via gene regulation vs. coding sequence: While (to my understanding) it is largely accepted in the field that changes to the CDS will often have more deleterious effects than changes to the expression of a gene, I agree that this could be elaborated on a bit. - Focus on stages S21/S22: This might indeed be somewhat problematic. The libraries from these two stages (particularly S21) seem to be very different from those from the other stages. In the PCA (Fig. 1C), S21 doesn't cluster well with anything, and the difference between the two replicates is massive compared to other stages. The accessibility pattern (Fig. 1D) also looks odd. The libraries also have the lowest scores for % of mapped reads (Fig. S2B), fragment size distribution (S2E), and Spearman correlation (S2I). All this could be biologically sound and be due to a major developmental transition at this point, but maybe it justifies revisiting the data and testing whether leaving out S21 (and/or S22) makes a big difference for the clustering analyses. - Peaks in distal intergenic regions: I agree that this could be elaborated on. It might also be that >10 kb is not actually that distal for Parhyale. I would suggest to split the "distal peaks" further (e.g., in 10 kb or 2-log steps, or whatever makes most sense) and try to understand if >10 kb is mostly <20 kb, or if most of them are hundreds of kb from the nearest gene?

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Referee #2

Evidence, reproducibility and clarity

Sun et al used omni-ATAC sequencing that is a modified version of classical ATAc-seq to identify and characterise the cis-regulatory elements in the P. hawaiensis genome. They further use long and short reads to improve upon existing gene annotation for this organism. The in-depth analysis ensures the results and conclusions to be sound however few points below might be needed to be addressed before the acceptance of manuscript.

In Introductory paragraph 2, sentence one, authors suggest that gene regulation plays more important role in evolutionary process than genes. Although a significant amount of research has been dedicated to gene regulation based evolution still this field is in nascent form. For example evidence of inheritance of the gene regulation pattern across generation is scarce and requires more evidence. I suggest authors to modulate the claim that still gene based evolution is the main paradigm instead otherwise.

Authors have repeatedly used S21 and S22 throughout the manuscript to support their claims with clustering etc. May authors shed some light on the differences in replicates for these timepoints. Furthermore, I could not find Fig 3J, perhaps author would like to point out Fig 3H.

The majority of ATAC-seq peaks in the distal intergenic regions is a very surprising result. Authors defend this result by suggesting that this organism has big genome. May author perform a short analysis that shows that these peaks are indeed represent nearby genes or may point towards 3D genome organisation. For example, I see that this genome might have regions in the genomes that are densely organised in gene clusters, in those cases does the pattern remains same i.e he majority of the genes are very distant from each other and hence use vital regulatory elements?

Significance

The study by Sun et al is timely in nature and significantly improve the gene annotation of P. hawaiensis. It definitely advances the current knowledge for this organism regulatory elements. The comparison to other model organisms can be further improved by extending the discussion of the results especially in context of distal regulatory elements. The resource generated will be helpful for the researchers working in the field of developmental biology.

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Referee #1

Evidence, reproducibility and clarity

The contribution by Sun et al. describes a very deep and thorough analysis of an Omni-ATAC-seq approach to identifying cis-regulatory elements in the crustacean Parhyale. This is a resource paper, so it does not explicitly have a research question or conclusions. The findings are a detailed dataset of putative regulatory elements, tested and validated with a number of different computational approaches, and - to a lesser extent - with a number of experimental approaches.

The authors' work is very thorough, and while it may be possible to add more analyses and more validations, the work presented in the manuscript is impressive and stands on its own as a useful body of data. No additional work is needed to make this a complete contribution.

The text is very well written and clear. It is a bit arduous in some places, but that is understandable, given the technical nature of the paper. The figures are clear and many of them are very eye-catching (in a positive sense).

All in all, I have no criticism of this contribution. It is a very carefully executed and thorough analysis.

Significance

I am not aware of any other species outside of the main experimental model organisms for which there is data about putative regulatory elements that is as detailed as that presented in this manuscript. It is thus not only a fantastic resource for people working on Parhyale, but also a model for how such data can and should be generated for other species. The authors say this explicitly in their concluding paragraphs and I agree. The Parhyale community will pounce on this paper as a useful resource, whereas people working on other species might be inspired by it to generate equivalent data for their communities.

I am an evolutionary developmental biologist who has worked on a number of species that are not traditional model species (I avoid the term "non-model", since every species is a model for something). I for one, fall into the category of people who will be inspired to generate equivalent data, although I must confess that I do not have the bioinformatic expertise of the authors, and therefore I am not able to critically assess the specifics of the tools they have used to generate and validate their data.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): Excellent quality of cell biology and biochemistry. the additional supports are needed for the claim of actin elongation using different formin variants.

Reviewer #1 (Significance (Required)): Ingrid Billault-Chaumartin and co-authors described interesting research that provides insights on formin-isoform specific function in fission yeast and a new role of Fus1 FH2 domain in cell-cell fusion event. While three formin isoforms have different localization, research proposed an additional dissection in their functional differences by having different functions in C-terminus, including FH1 FH2 and formin C-terminus. The work also described additional factors that regulate cell fusions from autotrophy effect and formin expression level, in addition to the well-accepted formin biochemical activities. Here are my comments regarding the strengths of the work and improvements that could further strengthen the story.

Major comments 1. Fig.1 shows Cdc12C could recapitulate Fus1 function by ~80% if fused with Fus1C, whereas deletion of the C-terminal tail of Cdc12 following FH2 introduces drastic dysfunction. Together with Fig. 3, these results indicate Cdc12 Cter plays more important roles than Fus1 Cter for there respective functions. Such results suggested a Cter-mediated mechanism that differentiates the functions of three fission yeast formin isoforms. The authors examined contributions from the difference in FH1 (Figs 4,5) and FH2 residues (Fig. 6). Whereas the obvious phenotype of Cter was not further investigated and not much discussed. The Cter of budding yeast formins interacts with nucleation-promoting factors, Bud6 and Aip5. Although S. Pombe does not have orthologs of budding yeast Bud6 and Aip5, I wonder would the author discuss the potential contribution of Cter in differentiating S. Pombe formins.

The reviewer is correct that the C-terminal tail region of Cdc12 beyond the FH1-FH2 domains has a strong influence on the ability of Cdc12C to replace Fus1C. This is one reason why we specifically investigated the possible role of Fus1 C-terminal tail, which is much shorter than that of Cdc12. We found that Fus1 C-terminal tail plays only very minor role in regulating Fus1 function, as described in Figure 3. We note that contrary to what the reviewer states, Bud6 exists in S. pombe and binds the C-terminal tail of the formin For3 (see Martin et al, MBoC 2007), but whether it binds Fus1 is unknown. We have expanded our discussion to include a paragraph on the role of formin C-termini.

Because the manuscript is focused on the function of Fus1 formin, we did not explore further the role of the Cdc12 C-terminal tail. It was previously shown that this region of Cdc12 contains an oligomerization domain that promotes actin bundling (Bohnert et al, Genes and Dev 2013). It is thus likely that this helps Cdc12 FH1-FH2 perform well in replacement of Fus1. In fact, it is likely that oligomerization boosts formin function, as we have discovered that Fus1 N-terminus contains a disordered region that fulfils exactly this function. This is described in a distinct manuscript under review elsewhere and just deposited on BioRxiv (Billault-Chaumartin et al, BioRxiv 2022; DOI: 10.1101/2022.05.05.490810). We have now cited this point in the discussion.

1. Here, the study focuses on the FH1 between Fus1 and Cdc12 to understand their different functions in actin polymerization. FH1 mediated actin elongation through its interaction with profilin via polyP. The transfer rate of G-actin from profilin and profilin sliding depends on the polyP patterns regarding the length of each polyp motif and their distance to FH2 (Naomi Courtemanche and Thomas D. Pollard, JBC, 2012). To better understand the mechanisms by which these engineered FH1 variants on both Fus1 and Cdc12 in Fig. 4, the author may want to list the sequence of these engineered FH1 domains, including the information of the number and length of polyp motifs, and discuss these patterns.

This list and discussion were available in the initial paper that characterized each of the constructs in vitro (Scott et al, MBoC 2011). We have now re-drawn it in a supplemental figure for convenience (as also answered in response to minor point 2), which is already provided in the revised manuscript as Figure S1. (Previous supplementary figures are re-numbered S1>S2, S2>S3 and S3>S4).

1. Figs.4,5 cell biology results do not directly support the point of specific elongation rate unless the LifeAct-labeled actin cable elongation speed could be followed and quantified. The fluorescent tagging of tropomyosin does not show the actin cable pattern, which makes it very difficult to be used to study actin cable dynamics, such as elongation. Therefore, I feel the data in current Fig. 4 and Fig. 5 could not claim the differences in actin elongation without a quantitative comparison of elongation rate. I suggest a CK666 treatment to increase the visibility of the actin cable pattern of LifeAct, used before in both fission and budding yeasts, which would allow the author to quantify the actin cable elongation rate. Another way is to use the TIRF assay used in this study, which would give a better quantitation of formin nucleation and profilin-aided elongation.

We respectfully disagree with the reviewer on this point. All the constructs we use in vivo have been characterized in vitro and their elongation rate carefully measured (Scott et al, MBoC 2011). These values are thus known and can be directly compared to our results in vivo.

Of course, it would be fantastic to be able to directly measure formin elongation rates in vivo, but we are not aware that this has been done in any system. The proxy experiments that the reviewer suggests would be good ones, but each faces technical challenges that make them impossible in our system. First, because the fusion focus is a structure that forms in response to cell-cell pheromonal communication, we cannot add CK-666 or any other drug during this phase, as this perturbs the pheromone signal. Indeed, we had shown that simple buffer wash leads to loss of the fusion focus (see Dudin et al, Genes and Dev 2016). Second, the fusion focus is at the contact site between partner cells, i-e somewhat distant (1-2µm) from the coverslip during imaging. It is thus impossible to use TIRF. Finally, the fusion focus is a tightly packed actin structure. This is the reason why (rather than use of the tropomyosin marker) we cannot image single actin filaments (or even bundles) of which we could follow the dynamics as has been done to measure the retrograde flow of actin cables in yeast.

What we have done is to use a better tropomyosin tag, mNeonGreen-Cdc8, which was just described (Hatano et al, BioRxiv 2022; DOI: 10.1101/2022.05.19.492673) to quantify amounts of linear actin. Although this is not a measure of elongation rate, it would give some sense about amounts of polymer assembled. We have obtained images with mNeonGreen-Cdc8 of all experiments previously conducted with GFP-Cdc8 and have replaced them in Figure 4C, Figure 5E, Figure 6E and Figure S2B. We have also quantified the relevant strains. The relative intensities of mNeonGreen-Cdc8 at the fusion focus at fusion time reflect remarkably well the measured elongation rates of the various formin constructs characterized in vitro. These data are now provided as new panels Figure 4F and Figure 5F.

1. I appreciated the detailed biochemical dissections of multiple aspects of WTFus1 and Fus1R1054E, although the biochemical assays could not identify the mechanism by which R1054E causes the cell fusion. In many cases, the formin functions are diverse in diverse biological processes and sophisticated that cannot be explained well only from its biochemical activities in actin polymerization, such as the bundling, nucleation, and elongation studied in this story regarding fusion. This exciting information allows us to think of more possibilities that might regulate formin function rather than a direct change of formin activities in actin polymerization. I think a discussion of different aspects of functional regulation of formin might inspire society to investigate new possibilities to solve the mysteries. For example, the changes in formin behaviors and functions could be regulated by stress-induced formin turnover by degradation, cell signaling-regulated formin clustering and complex assembly, and their potential relevance to recruit protein constituents for fusion progression.

We have added a paragraph on the role of Fus1 C-terminus. If you feel we should expand more on the diverse modes of regulation of formins, we could, but we have so far kept the discussion centred around the points of investigation in this paper, whose aim was to probe how changes in nucleation and elongation rates, rather than other regulations, affect the in vivo function of Fus1.

Minor comments. 1. There are two types of "C", one includes FH1/FH2 and one following FH2, used in the manuscript, and it is a bit confusing. Better to differentiate them that allows an easy following. Fig. 1 uses Cdc12C-deltaC, Fig. 3 uses Fus1-delta Cter.

We have updated the nomenclature to make this clearer: the C-terminal region beyond the FH1-FH2 domains is now called Cter throughout the manuscript.

1. It's better to specify the amino acid position on the schematic of formins, such as panel A in many figures. It's always more informative to compare formin activities by considering the domain lengths, especially for the C-terminal tail that is variable in lengths and sequences. With similar thoughts, I suggest a supplementary figure that lists the sequence of all FH1 domains variants and Cter domains, such as the FH2 domain in Fig. S1.

We have made a supplementary figure (new Figure S1) listing all constructs with specific aa positions as well as the FH1 domain variants and their sequences (see also answer to point 2 above). We have not added the sequence of the Cter domains in this figure, as these are extremely divergent and not particularly informative at this point.

1. "n" for the statistic needs to be provided for Fig. S3.

We have added the information to the legend of the figure (now Fig S4).

1. The SDS-PAGE staining gel of the purified recombinant proteins for biochemical assays should be provided, particularly for these newly reported mutant variants.

This is now provided as new panel S4C. We show the purified recombinant Cdc122FH1-Fus1FH2 proteins, which are the newly reported ones.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): In this study, Billaut-Chaumartin and colleagues investigate the molecular specialization of the S. pombe formin, Fus1. The authors systematically modulate the actin filament elongation and nucleation activities of Fus1 by expressing chimeric constructs that contain Formin Homology 1 and 2 domains from two other formins with known polymerization activities. By characterizing the architecture of the fusion focus and the efficiency of cell fusion, they find that both the elongation and nucleation properties of Fus1 are specifically tailored for its cellular role. Comparison of formin constructs with similar elongation and nucleation activities also reveals that the Fus1 FH2 domain possesses a specific property that promotes efficient cell fusion. Using sequence alignment and homology modeling, the authors identify R1054 as the residue that confers this novel, fusion-specific activity to Fus1, despite producing no effect on its bundling or polymerization properties in vitro.

Overall, this study is well motivated, and the results support the conclusions that are drawn. I have only minor suggestions, as described below.

Minor comments: (1) The schematic diagrams of the chimeric formin constructs are very helpful. However, it is difficult to distinguish the colors from one another, especially in the case of the Cdc12FH1-Fus1FH2 variant, which requires discernment of the relatively small purple region within the dark blue molecule. Would it be possible to modify the colors to increase their contrast? Similarly, the blue and gray data sets in Figure 3B are very difficult to discern.

We have changed the colours to improve contrasts.

(2) The affinities (Kd) with which the formins bind the barbed ends as described in the second-to-last paragraph on page 8, in Figure Legend 7G, and in the "Analysis of pyrene data" section of the Materials and Methods should be defined as dissociation "constants", rather than dissociation "rates". Also, these affinities are lacking units in the following sentence on page 8.

We have corrected this. The unit is nM.

(3) When comparing the TIRF micrographs in Figure S3A, it looks as though both formins (but especially the R1054E variant) nucleate more filaments in the presence of profilin than in its absence. Is this a reproducible effect? If so, can the authors provide an explanation for this?

There is strong variability in the filament numbers observed by TIRF in replicate experiments, which makes it difficult to use this technique to determine the nucleation efficiency. This may be due for instance to the stickiness of the glass, which may influence the number of observed filaments. We have measured the number of filaments after 130s of polymerization for each condition to test whether there are any significant differences between conditions despite overall variability. The measurements suggest that the addition of profilin increases the number of actin filaments. However, these results should be taken very carefully due to the experimental variations (very large error bars). Additionally, because Fus1-associated filaments are very short in absence of profilin, it is quite likely that this influences their crowding at the glass surface compared to longer filaments (in presence of profilin). Since in TIRF we can only observe the filaments at the glass surface, we may miss a portion of short Fus1-bound actin filaments in absence of profilin.

For these reasons, and because the possible role of profilin in modulating nucleation efficiency by formins is not the object of the work here, would thus prefer not to include this graph in the manuscript.

Reviewer #2 (Significance (Required)): This study contributes a key advancement towards understanding how the polymerization activities of formins are tailored to support diverse and specific cellular functions. The results in this study nicely complement and expand upon similar recent work that dissected the polymerization requirements of the formin Cdc12, which mediates cytokinetic ring assembly in S. pombe, and For2, which drives the assembly of apical networks that are necessary for polarized growth in Physcomitrella patens. As such, this work will likely be of significant interest to scientists who study mechanisms of actin dynamics regulation. The identification of R1054 as a residue that confers a novel regulatory activity to the FH2 domain of Fus1 will also likely be of great interest to biochemists and other scientists who study formins at the molecular level.

My expertise is in the field of formins and actin polymerization.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, Billaut-Chaumartin and colleagues investigate the molecular specialization of the S. pombe formin, Fus1. The authors systematically modulate the actin filament elongation and nucleation activities of Fus1 by expressing chimeric constructs that contain Formin Homology 1 and 2 domains from two other formins with known polymerization activities. By characterizing the architecture of the fusion focus and the efficiency of cell fusion, they find that both the elongation and nucleation properties of Fus1 are specifically tailored for its cellular role. Comparison of formin constructs with similar elongation and nucleation activities also reveals that the Fus1 FH2 domain possesses a specific property that promotes efficient cell fusion. Using sequence alignment and homology modeling, the authors identify R1054 as the residue that confers this novel, fusion-specific activity to Fus1, despite producing no effect on its bundling or polymerization properties in vitro.

Overall, this study is well motivated, and the results support the conclusions that are drawn. I have only minor suggestions, as described below.

Minor comments:

1. The schematic diagrams of the chimeric formin constructs are very helpful. However, it is difficult to distinguish the colors from one another, especially in the case of the Cdc12FH1-Fus1FH2 variant, which requires discernment of the relatively small purple region within the dark blue molecule. Would it be possible to modify the colors to increase their contrast? Similarly, the blue and gray data sets in Figure 3B are very difficult to discern.
2. The affinities (Kd) with which the formins bind the barbed ends as described in the second-to-last paragraph on page 8, in Figure Legend 7G, and in the "Analysis of pyrene data" section of the Materials and Methods should be defined as dissociation "constants", rather than dissociation "rates". Also, these affinities are lacking units in the following sentence on page 8.
3. When comparing the TIRF micrographs in Figure S3A, it looks as though both formins (but especially the R1054E variant) nucleate more filaments in the presence of profilin than in its absence. Is this a reproducible effect? If so, can the authors provide an explanation for this?

Significance

This study contributes a key advancement towards understanding how the polymerization activities of formins are tailored to support diverse and specific cellular functions. The results in this study nicely complement and expand upon similar recent work that dissected the polymerization requirements of the formin Cdc12, which mediates cytokinetic ring assembly in S. pombe, and For2, which drives the assembly of apical networks that are necessary for polarized growth in Physcomitrella patens. As such, this work will likely be of significant interest to scientists who study mechanisms of actin dynamics regulation. The identification of R1054 as a residue that confers a novel regulatory activity to the FH2 domain of Fus1 will also likely be of great interest to biochemists and other scientists who study formins at the molecular level.

My expertise is in the field of formins and actin polymerization.

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

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Referee #1

Evidence, reproducibility and clarity

Excellent quality of cell biology and biochemistry. the additional supports are needed for the claim of actin elongation using different formin variants.

Significance

Ingrid Billault-Chaumartin and co-authors described interesting research that provides insights on formin-isoform specific function in fission yeast and a new role of Fus1 FH2 domain in cell-cell fusion event. While three formin isoforms have different localization, research proposed an additional dissection in their functional differences by having different functions in C-terminus, including FH1 FH2 and formin C-terminus. The work also described additional factors that regulate cell fusions from autotrophy effect and formin expression level, in addition to the well-accepted formin biochemical activities. Here are my comments regarding the strengths of the work and improvements that could further strengthen the story.

Major comments

1. Fig.1 shows Cdc12C could recapitulate Fus1 function by ~80% if fused with Fus1C, whereas deletion of the C-terminal tail of Cdc12 following FH2 introduces drastic dysfunction. Together with Fig. 3, these results indicate Cdc12 Cter plays more important roles than Fus1 Cter for there respective functions. Such results suggested a Cter-mediated mechanism that differentiates the functions of three fission yeast formin isoforms. The authors examined contributions from the difference in FH1 (Figs 4,5) and FH2 residues (Fig. 6). Whereas the obvious phenotype of Cter was not further investigated and not much discussed. The Cter of budding yeast formins interacts with nucleation-promoting factors, Bud6 and Aip5. Although S. Pombe does not have orthologs of budding yeast Bud6 and Aip5, I wonder would the author discuss the potential contribution of Cter in differentiating S. Pombe formins.
2. Here, the study focuses on the FH1 between Fus1 and Cdc12 to understand their different functions in actin polymerization. FH1 mediated actin elongation through its interaction with profilin via polyP. The transfer rate of G-actin from profilin and profilin sliding depends on the polyP patterns regarding the length of each polyp motif and their distance to FH2 (Naomi Courtemanche and Thomas D. Pollard, JBC, 2012). To better understand the mechanisms by which these engineered FH1 variants on both Fus1 and Cdc12 in Fig. 4, the author may want to list the sequence of these engineered FH1 domains, including the information of the number and length of polyp motifs, and discuss these patterns.
3. Figs.4,5 cell biology results do not directly support the point of specific elongation rate unless the LifeAct-labeled actin cable elongation speed could be followed and quantified. The fluorescent tagging of tropomyosin does not show the actin cable pattern, which makes it very difficult to be used to study actin cable dynamics, such as elongation. Therefore, I feel the data in current Fig. 4 and Fig. 5 could not claim the differences in actin elongation without a quantitative comparison of elongation rate. I suggest a CK666 treatment to increase the visibility of the actin cable pattern of LifeAct, used before in both fission and budding yeasts, which would allow the author to quantify the actin cable elongation rate. Another way is to use the TIRF assay used in this study, which would give a better quantitation of formin nucleation and profilin-aided elongation.
4. I appreciated the detailed biochemical dissections of multiple aspects of WTFus1 and Fus1R1054E, although the biochemical assays could not identify the mechanism by which R1054E causes the cell fusion. In many cases, the formin functions are diverse in diverse biological processes and sophisticated that cannot be explained well only from its biochemical activities in actin polymerization, such as the bundling, nucleation, and elongation studied in this story regarding fusion. This exciting information allows us to think of more possibilities that might regulate formin function rather than a direct change of formin activities in actin polymerization. I think a discussion of different aspects of functional regulation of formin might inspire society to investigate new possibilities to solve the mysteries. For example, the changes in formin behaviors and functions could be regulated by stress-induced formin turnover by degradation, cell signaling-regulated formin clustering and complex assembly, and their potential relevance to recruit protein constituents for fusion progression.

Minor comments.

1. There are two types of "C", one includes FH1/FH2 and one following FH2, used in the manuscript, and it is a bit confusing. Better to differentiate them that allows an easy following. Fig. 1 uses Cdc12C-deltaC, Fig. 3 uses Fus1-delta Cter.
2. It's better to specify the amino acid position on the schematic of formins, such as panel A in many figures. It's always more informative to compare formin activities by considering the domain lengths, especially for the C-terminal tail that is variable in lengths and sequences. With similar thoughts, I suggest a supplementary figure that lists the sequence of all FH1 domains variants and Cter domains, such as the FH2 domain in Fig. S1.
3. "n" for the statistic needs to be provided for Fig. S3.
4. The SDS-PAGE staining gel of the purified recombinant proteins for biochemical assays should be provided, particularly for these newly reported mutant variants.

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Reply to the reviewers

From the start, the authors would like to thank all the reviewers for their careful and constructive consideration of our manuscript. We have now made several changes to the paper and believe it to be better for the feedback.

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

In this study, Rees et al. perform an RNA-seq circadian time course experiment in the recently formed allopolyploid wheat. Through comparisons with other circadian transcriptomic datasets in other species it appears that the period of rhythmic genes is much more variable in wheat with a shift to longer periods compared to the other species examined. Interestingly, by analyzing circadian parameters among expressed genes, they find evidence that this newly formed allopolyploid already shows signs of divergence in circadian traits among homoeologs. A thorough comparison with circadian regulated genes in Arabidopsis reveals overlap in phasing of genes involved in certain biological processes such as photosynthesis and light signaling whereas genes involved in starch metabolism were found to have different levels of rhythmicity and phasing. This dataset will be a great resource for the community and enable new predictions about the influence of polyploidy on the circadian control of important crop improvement traits and the circadian regulation of gene expression.

Major Comments

1. The results section starts with very little explanation of the experiment. It would help to provide a little more detail at the start of the results to explain the context for the experiment and what was done, when samples were collected and for how long. For the methods section, it isn't until line 650 that it is clearly stated that the sampling started at ZT0. It would be better to put this in the plant materials and growth condition section.

Thank you for highlighting the need for this context, we agree that the manuscript is improved by an introduction to the experiments. We have now included an “Experimental context” section in the results and have taken the opportunity to explain how the full 0-68h and 24-68h datasets are used within our analysis. Ln 74-82. We have also edited the Methods as suggested Ln 610-615.

The low proportion of circadian regulated genes is likely due to the very low cutoff for calling a gene expressed, especially when there are three days of repeated timepoints. If a gene is expressed across the time course it should have values above TPM 0 for at least 3 time points in order for it to be expressed each day. I'd also be suspicious of a gene with a TPM value less than 0.5. Comparing these types of numbers is always challenging due to the various cutoffs used. Along those lines, why was a different filtering scheme used for Arabidopsis (line 657)?

We completely agree that the proportion of genes described as rhythmic changes a great deal with the threshold at which you exclude low expression transcripts as well as the window over which measurements are taken and the q-value cut-off for rhythmicity. We performed an analysis to test the effects of applying a pre-filtering step to exclude low-expression genes and discuss our findings in Supplementary Note 1. Briefly, we removed genes with expression less than 0.1 TPM in six or more timepoints and again ran Metacycle to define numbers of rhythmic genes. Our results are discussed in Supplementary Note 1 and are presented in Supplementary Table 1. Regardless of the cut-offs applied, Arabidopsis and wheat data was treated identically, and our findings reported in the main results were consistent with those reported in the Supplementary analysis. Thank you for raising this point, as we have now improved our description of this analysis in the main text (Ln 92-95).

Regarding the different filtering schemes, the filtering mentioned by Reviewer 1 was applied to both Arabidopsis and wheat data for a stricter retention of rhythmic genes, as part of the pre-WGCNA clustering analysis. Filtering to retain genes with >0.5TPM across 3 timepoints was applied to reduce lowly expressed genes, that act as background 'noise' when defining clusters. We applied this across 3 timepoints rather than the WGCNA suggestion of 90% of samples - because the patterns of expression in our rhythmically filtered datasets were cyclical in nature.

In reference to the shortening of the period every day, this should be interpreted with caution. Period estimate of a single cycle are not very reliable and the SD for each day is around 3h so it is difficult to draw any conclusions about changes in period each day. One option would be to only include genes with an SD less than 1h or alternatively to remove the discussion surrounding the comparison of period across the three days and focus on the period results for the full 24h-68h window shown in 1b. While 2 days is better it is still not ideal for calling period; however, your first day will still have a strong diurnal driven pattern that will likely skew your circadian period.

Thank you for your comments. Our question here was to determine whether the mean period lengths of rhythmic transcripts in wheat were always immediately longer upon transfer to constant light, or whether they got progressively longer over time. Upon reading the reviewer’s comment, we realize that the explanation provided of how we conducted this analysis was misleading. Our approach was to take a 44h sliding window (almost 2 days) and measure period at 0-44h, 12-56h and 24-68h. We have now added the previously missing statistics that support our findings in the main text, and which hopefully show the significance of the period changes over time (supplementary note 2). One of the most surprising findings from this analysis was that the periods in the first window were the longest 28.61h (SD=3.421), suggesting that the diel (driven) oscillation had little impact upon immediate transfer to free run. Our interpretation is that the mean period initially lengthens trying to follow the missing dusk signal, before the free-running endogenous period asserts itself in later cycles (Ln 129-128).

Line 87-93: If the dusk cue is important for clock expression you would think this would be biased towards genes that peak later in the day or near dusk. This argument should be connected better to the period results discussed on lines 98-101.

Following on from our statement above, we have now combined our hypothesis for why wheat transcripts expressed at dusk have longer periods with the discussion about longer periods upon transfer to constant light. We agree that the two processes are likely to be connected and have now placed them together in Ln 129-128.

1. Lines 650-652 of the Methods mentions that one of the main interests was the response to transfer to L:L, but this isn't mentioned in the introduction and doesn't come up much in the Results section. Most of the expression comparisons are focused on the 24-68h window. It also isn't clearly explained why the first day in LL is still a diurnal cycle. This would be helpful for non-circadian readers who may wonder why the first day is not included in all the analyses.

We believe this point is now also addressed by the addition of an Experimental Context section in the results (Ln 74-82), in response to the reviewer’s previous comment.

1. The phase comparisons shown in Figure suppl 4 are confusing. Suppl. Note 3 states that the period from the 24-68h data window was used to establish the bins but then the phase is shown for 3 different windows for each column? When calculating the phase for each of those 3 windows which period was used as the denominator in the phase calculation? Was it the period that matches the window used to calculate phase? What does the plot look like if phase is called on the same window used to calculate period (24-68)? What method was used to call phase in Suppl. Fig 4? As shown in Suppl Fig. 3 the method can influence the phase distributions. The methods suggest that the phase was determined with Metacycle but then FFT and MESA were used to verify. What does this mean verify, were they adjusted if FFT/MESA didn't agree?

We agree that this Figure was unnecessarily complicated. We have now simplified Supplementary Figure 4 so that only the phases from 24-68h are presented. We have also clarified the legend to explain why we used FFT-NLLS to improve accuracy of Metacycle predictions.

It is difficult to interpret the value of the period and phase comparisons shown in Fig. 1b, c, e and f after the preceding section about how variable the period and phase is across days. It is also surprising that the full 3 days were used to calculate the circadian statistics considering the first day is still under diurnal control. Do the ratios remain the same if the statistics are performed only on the 24h-68h window? For consistency with the rest of the paper and avoid confusion it would be best to have all circadian parameters measured using the same time window (24h-68h).

Thank you for your comments, we can see how our logic in using the different data windows was not clear enough. As mentioned above, we have now explained the use of the full and shortened data windows in Experimental context section (Ln 74-82). Fig 1c is a comparison between different circadian datasets and as such we have only compared periods across 24-68h window. Similarly, Fig 1b is a global analysis of periods in rhythmic genes in comparison with Arabidopsis and so is again measured from 24-68h. We have now clarified this in the Figure legend for 1b.

For comparisons of homoeologs within wheat triads, our question was in identifying homoeologs which behaved differently when placed under free-running conditions. We therefore still feel justified in using the full 0-68h dataset to identify homoeolog periods and phases which indicate differential circadian regulation, but we have now clarified that we are using the full dataset for the triad analysis in the results (Ln 140).

Fig 1h-m. How were those genes chosen? It would help to see the SD of the replicates shown, since this is just showing one triad. It would be helpful to see a plot that represents the full set of triads rather than just one that looks best. If normalized to a standard phase they could be put on the same plot. For example, panel j is meant to show the 8h lag of subgenome D. If the data is normalized so that A and B are set to the same phase all the triads could be displayed with shaded SD bars to show the variation. Something like this would be a better representation of the data rather than showing just one example.

Fig. 1h-m are case-studies illustrating the different forms of circadian imbalance between homoeologs. We agree that it is helpful to see the standard deviation as error bars on these triad plots and have added it as suggested. In line with another Reviewer 2’s suggestion we have removed Fig 1k and have replaced this with a comparison of mean normalised data for Triad 408 and Triad 2454, highlighting the difference between imbalanced rhythmicity and imbalanced amplitudes between homoeologs. Fig 1 I and m do not have error bars as adding standard deviations to mean normalised data wasn’t appropriate.

Thank you for your suggestion on how to display the different phases between homoeologs. We feel that if we were to plot all of the triads displaying imbalanced phases, the differences in period length and accompanying noise differences would make the plot so busy as to be unreadable. We hope that the pie charts Fig 1 d-g give a global overview of the proportions of triads with circadian imbalance, but agree with the point that it is useful to allow readers to view triads of their own preference. Therefore, we have now provided the replicate level TPM data with the triad IDs annotated (Supplementary File 12) and Supplementary file 11 provides the classification of each triad alongside Metacycle statistics, ortholog identification and cluster information discussed elsewhere in the paper. Readers can now look up a triad or gene of interest and see how it was classified and what the expression looks like over the full dataset.

It is surprising that there aren't more comparisons with the B. rapa dataset, especially when discussing the clock genes that show balanced or imbalanced expression. Are they similar in B. rapa and does it support your hypothesis that unbalance for certain genes are selected against?

While we agree that a thorough, multiple species, comparative transcriptomic analysis is undoubtably of interest for the future, we feel it is beyond the scope of the questions being addressed in this paper. We do compare paralogs defined as “similar” in the Greenham dataset with homoeologs described as “balanced” in our dataset and find that genes involved with “photosynthesis” and “generation of precursor metabolites and energy” tend to be common between the two groups, potentially suggesting conservation of balance for certain types of genes (Ln 206-217).

Figure 2 networks. Why were these specific modules selected? Is it actually appropriate to directly compare these modules? I do see that some of the comparisons have high correlations from panel a, but not all. For example, in panel b the W9 and A9 modules have a correlation value of 0.92, which seems appropriate. However, panel c (modules W3 and A2) have a correlation of 0.42, which seems far too low to make any sort of comparison meaningful.

The modules were selected to simplify the comparison of genes expressed in the dawn, midday, dusk, and night. We were interested in identifying common GO-enrichment in genes peaking throughout the day, although as you have identified, the differences in period length between Arabidopsis and wheat made this difficult. Our reasons for comparing module W3 with module A2, were that, even though their eigengenes are not highly correlated per se, when period length is taken into account, both modules peak during the subjective day (CT 6.34h and 6.19h) and they share commonly enriched GO terms which make sense for day peaking genes.

Further, as described in methods comments, using a cutHeight as low as 0.15 will likely lead to some number of genes in any given module that do not necessarily "share" a similar expression pattern. These genes could have a pattern that has very low correlation to their module eigengene and were only placed in that module because the pattern was "less similar" to other module eigengenes. The current expression plots in this figure follow a clear pattern, but I suspect this would be even more apparent if the genes within these modules had a higher correlation to the module eigengene. Perhaps the current genes in these modules could just be filtered to have a higher correlation score?

Thank you for your comments, we have now made changes to the Results and Methods to clarify our approach (Ln 237-239 and Ln738-765). Merging modules with highly correlated module eigengenes (ME) is the final step in constructing our co-expression networks. To do this, as the reviewer describes - we used the WGCNA default parameter of a mergeCutHeight() of 0.15. This results in the merging of modules with highly correlated ME as the 0.15 mergeCutHeight() refers to the dissimilarity metric of 1 minus the eigengene correlation. So for WGCNA, a mergeCutHeight() of 0.15 corresponded to a correlation of 0.85. For the wheat modules, we took the additional step of merging closely related modules (mergeCloseModules()) using a cutHeight of 0.25, again a dissimilarity metric of 1 minus the eigengene correlation (corresponding to a correlation of 0.75). Reducing the stringency of the cutHeight to merge highly correlated wheat modules enabled us to more easily compare significantly correlated wheat and Arabidopsis co-expression modules to identify groups of genes in wheat and Arabidopsis expressed at similar times in the day, and enable the comparison of whether similar phased transcripts in wheat and Arabidopsis had similar biological roles.

Lines 327-334: I am not following the connection between 'response to abiotic stimulus' and the photoreceptor and light signaling proteins. At the start of this section (line 308) the authors say that the GO analysis was only done on rhythmically expressed genes but the reference to only one PHYA being rhythmic and yet multiple genes are shown in the plot in fig. S16. Does this mean that all the genes were shown and not just the rhythmic ones? This would explain why many of the PHY and CRY genes don't seem to have rhythms. This should be clarified better in the text or indicated in the plot which ones were called rhythmic. Since the first day following transfer is still the diel pattern from the entrainment condition, what does the PHY and CRY expression look like? Does it appear rhythmic under diel but lose rhythmicity in LL? It should be noted in the text that arrhythmicity in circadian conditions doesn't mean there isn't rhythmicity under diel conditions. This could be an additional explanation apart from the current one in the text that the regulation is at the level of protein stability/localization. Overall, this entire section is very long and entirely based on data shown in the supplemental material. I do appreciate having the individual gene plots that supplement Figure 4 and would suggest either providing a main figure to highlight a small subset of genes or pathways in this section or shorten it and focus on the results shown in the main figures.

Upon reading the reviewer’s comment, we realize that we should have made our motivations and processes clearer within this section. We used the data filtered for rhythmicity to conduct the GO-enrichment analysis and then used that to identify processes which should be of interest for further investigation. We have now added an additional sentence (Ln 352-354) to explain this more clearly. We then considered the orthologs of well-known Arabidopsis gene networks and extracted their expression from our circadian dataset, whether rhythmic or not. Supplementary Table 10 contains all of the genes we investigated, their expression and their MetaCycle statistics. We have also indicated here which genes are plotted in which Supplementary Figure 18-20. The reasons for plotting non-rhythmic genes in some cases was that it illustrates the differences between circadian control in Arabidopsis versus wheat (as is the case for the PHY and CRY genes). We understand that it is useful to see at a glance which genes are classified as rhythmic or arrhythmic, so have now highlighted each row in Supplementary Table 10 to make this more intuitive, and added a read me tab.

Regarding your point about oscillation under diel cycles, we agree that some transcripts will show rhythmic behaviour under entraining environments but not under constant conditions, and may perform time-of-day specific functions. However, these transcripts are likely to not be regulated by the circadian clock (at the transcriptional level) and so are not discussed in the context of a circadian transcriptome.

For your interest, here is the full expression of PHY and CRY transcripts starting at ZT0:

[Image]

It is difficult to say for definite, but it seems likely that some of these photoreceptors will have rhythmic patterns of expression under diel cycles, but these rhythms do not endogenously persist under constant conditions.

We appreciate your feedback that this section would benefit from cutting down of text and addition of a Figure to illustrate the text. We have now cut some of this section down and created a new main figure based on some of the oscillation plots from Supplementary Figure 18 and 19. We chose examples that reflect a conservation of relationships between transcripts of different peak phases, as we find it interesting that both species have similar patterns. (Main Figure 4, Ln 361--363, 382).

1. Primary metabolism section: in terms of the supplemental figure, similar to the previous one I think it would declutter the plots if the genes that are not rhythmic were left out and simply indicate below the plot that they didn't meet the rhythmicity cutoff. This is another area where there is more discussion surrounding the supplemental figures than the main figure 4.

One of the overall findings of this section was that many of the genes involved in Starch and T6P metabolism which are rhythmically expressed in Arabidopsis are not rhythmically expressed in wheat. We feel removing these genes from the results would detract from the importance of this finding. We have now edited Supplementary Table 10 to highlight which genes are classified as rhythmic. We have also added in a sentence to the start of this section which lays out our motivations for this analysis, summarises our findings and better connects the text with an explanation of Fig. 5 (Ln 408-430).

For all gene expression figures there should be SD or SE shown either as bars or ribbons to represent the variation in replicates.

Although we agree that error bars are informative for showing variation between replicates (and have added them to Fig. 1 to show differences within wheat triads) we feel that adding error bars to the gene expression plots in Fig. 3, Fig 4 and Supplementary Fig 19-20 would make these plots difficult to read, particularly where the wheat homeologs are very similar. The purpose of these gene expression plots is to compare circadian profiles in Arabidopsis and wheat orthologs rather than to claim significant differences in expression at any particular timepoint. This is fairly common in other circadian biology studies:

https://www.pnas.org/doi/10.1073/pnas.1408886111 ,

https://www.jbc.org/article/S0021-9258(17)49454-3/fulltext#seccestitle20 , https://journals.plos.org/plosone/article/comments?id=10.1371/journal.pone.0169923 , https://www.science.org/doi/10.1126/science.290.5499.2110?url_ver=Z39.88-2003&rfr_id=ori:rid:crossref.org&rfr_dat=cr_pub%20%200pubmed,

https://www.frontiersin.org/articles/10.3389/fgene.2021.664334/full,

https://www.science.org/doi/full/10.1126/science.1161403

The replication level information for each gene has now been made available in Supplementary file 12.

1. It would be very helpful to include the code used to generate the networks and perform the cross-correlation of eigengenes across networks should be included in the Methods. This will also save you from responding to email requests!

Thank you for your comment, Code for the cross-correlation analysis, Loom plots and WGCNA network construction is now available from our groups GitHub repository: https://github.com/AHallLab/circadian_transcriptome_regulation_paper_2022/tree/main

Minor Comments

1. Figure 1, panel d: - The "unbalanced" triads that are depicted by the lighter shading; do these in fact have a different cutoff than the original rhythmic homoeologs? In the figure it says qThank you for bringing this to our attention, this has now been corrected.

Hard to directly compare the GO term overlap in Figure 2f. Might be better to only show the results for the 4 pairs shown in b-e and put them side by side in the bubble plot.

Thank you for this feedback, We have tried to make this plot easier to understand without losing any of the available information. Hopefully it is now more intuitive to understand which columns are being compared. We have changed the coloured lines to make them slightly wider, put the modules in corresponding coloured boxes and highlighted GO-slim terms shared by modules being compared.

1. Line 314 -316 don't see supp tables 10, 11

Our apologies, these files were missed previously from the upload are now available.

1. For the selection of B. rapa circadian paralogs with similar and differential expression patterns (starting line 714), the authors choose a hard cut off of 0.001 (differentially patterned) OR 0.1 (similarly patterned). What happens to the genes that are between these two cut offs or is this a typo. Since all the other cutoffs for rhythmicity was set at 0.01 it seems likely that this is a typo.

We have now clarified this in the methods, (Ln 807-822). This is not a typo, but it is a different method to the Metacycle approach we have used for our wheat data. We defined similar/different paralogs as characterized in Greenham et al, (2020) using DiPALM p-values. We chose these DiPALM p-value cut-offs as they gave us approximately equal numbers of paralogs in each category, which represent tails of similarly expressed or differently expressed circadian genes. We checked these cut-offs by calculating average Pearson’s correlation statistics between paralogs and found that differential Brassica paralogs had a mean Pearson correlation coefficient of 0.31 (SD = 0.43) and similar Brassica paralogs had a mean Pearson correlation of 0.75 (SD= 0.23) which confirms that the DiPALM method of defining expression patterns makes sense in the context of this analysis.

Line 681. Should be supplemental Figure 6 not 9.

1. References to most supplemental figures are not the correct number.

2. Labels above the plots in Supp Fig5 do not match the legend.

We apologise for these mistakes. We realize that we had mistakenly submitted an earlier draft of the Supplementary materials file, which was missing Supplementary Figure 5, 6 and 9 which therefore shifted the order of the remaining figures. This is now updated.

1. Suppl table 7 should be as a separate .csv file or similar to be able to see the full table.

This is a good suggestion, and we have added this.

1. Line 723 should be B. rapa not B. napus.

Thank you for catching this! Corrected.

1. Figure 4. There is no explanation for what the black boxes represent in the figure legend.

Thank you for your comment. Figure 4 (new Figure 5) has now been updated.

Reviewer #1 (Significance (Required)):

This study provides new insight into the circadian regulation of the transcriptome in a new allopolyploid. It adds a valuable resource to a growing collection of circadian studies in important crops and will greatly improve our efforts to learn more about the circadian control of important crop improvement traits. The dataset will be of interest to other plant circadian biologists as well as the general plant biology community who focus on monocot crops. My expertise is more on the transcriptomic side and I do not have the expertise to evaluate the phylogenetic work presented in this study.

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

Summary Rees et al. present an RNAseq time course of bread wheat. Its recent polyploidisation is one motivation for this study as gene expression dosage is known to be important for clock function in other plants. The time course covers 3 days at sampling intervals of 4h of 2-week old wheat plants (all aerial tissues), in triplicates. The subsequent analysis of the RNAseq data includes analysis of the generated data by itself (e.g. GO analysis, rhythmicity, period and phase analysis, rhythmicity of transcription factor families as well as TF binding sites) as well as thorough comparison with published datasets of other species (Arabidopsis, Brassica rapa, Brachypodium dystachion). One of the key findings is that the mean period length and the period spread are larger in wheat than in these other species). Circadian clock genes largely have similar dynamics in wheat compared to Arabidopsis. In addition, one focus is the analysis of the dynamics of three genes of one triad and imbalance / balance of such triads. To the surprise of the authors, circadian regulated and clock genes were not necessarily balanced. Silencing is one of their explanation for imbalance of circadian genes as arrhythmic genes of one triad are typically those with the lowest expression level. Finally, the authors point out more examples of rhythmic processes and genes (photoreceptors and signalling, auxin, carbon metabolism) and their commonalities and differences with Arabidopsis.

Major comments - The key conclusions and the data are convincing

We thank the reviewer for their supportive comments.

• line 120 and figure 1: In my opinion, q > 0.05 is not a good definition of arrhythmicity as non-significant q-values can result from either noise in spite of rhythmicity or from arrhythmicity. A more statistically sound way to detect arrhythmicity could for example be two-one-side tests (for example in the R package 'equivalence', e.g. see usage for time courses by Noordally et al. 2018, https://www.biorxiv.org/content/10.1101/287862v1).

Thank you for pointing us in the direction of this package, we agree that choosing methods for circadian quantification and q-value cut-offs is always tricky and different approaches will perform better for noisier or non-sinusoidal waveforms. For future work, we will investigate the application of the suggested method in circadian rhythmicity analysis. However, we believe that the criteria used in this paper for rhythmicity quantification is suitable for addressing our questions, and overall, we are satisfied that rhythms with a q-value of >0.05 would also be classified by eye as being arrhythmic, and rhythms with a q-value Many other studies have used meta2d B.H q-values as a metric of rhythmicity: e.g. (https://bmcplantbiol.biomedcentral.com/articles/10.1186/s12870-022-03565-1 , https://link.springer.com/content/pdf/10.1186%2Fs12915-022-01258-7 , https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8782462/pdf/pcbi.1009762.pdf )

• lines 480-484 and intro: In the introduction, the authors write that expression levels of clock components are important for the function of the clock, and that this is one motivation for the current study where polyploidisation is expected to affect the expression levels of clock genes and their outputs. I wonder what answers or speculations this study provides in the end, or whether such answers / speculations should be made clearer. For example, do the authors think that the higher variability of periods in wheat could be a consequence of lower robustness (in addition to possible spatial differences that are mentioned) due to polyploidisation? Is anything known about the period of rhythms of close wheat relatives that did not undergo polyploidisation? Did you look at dampening over the time course in wheat vs. Arabidopsis?

The point above is an interesting one, and we thank the reviewer for raising it. We agree that the high variability of periods in wheat may be a product of polyploidisation, as functional redundancy between homoeologs may allow a tolerance for less tightly regulated, non-dominantly expressed circadian transcripts. We have now added this hypothesis to our discussion: Ln536-550.

In our comparative analysis of period distributions, we looked at periods of transcripts from a diploid relative of hexaploid wheat, Brachypodium distachyon. In Brachypodium, period lengths have around the same SD as in Arabidopsis but the mean period length is slightly longer (Supplementary table 2). We have now edited our results to make the relationship between wheat and Brachypodium clearer (ln 109-110).

Minor comments:

Introduction - lines 49: it is unclear what is meant by ppd-1 at this position of the sentence

We agree this was unclear and have revised it to “notably the ppd-1 locus within TaPRR3/7” Ln 52

• line 54/55: clarify that this refers to Arabidopsis thaliana

Corrected.

Results - line 69 and 76: cite references for these tools here (not only in the methods section)

Corrected.

• line 90-93: Why wouldn't the same thing happen on subsequent subjective evenings?

Thank you for your comments. We have now combined our hypothesis for why wheat transcripts expressed at dusk have longer periods with the discussion about longer periods upon transfer to constant light. We think that the two processes are likely to be connected and have now placed them together in Ln 126-131.

The behaviour of mean period lengths of wheat transcripts upon transfer to constant light was unexpected and we believe is quite interesting. One explanation is that the influence of the ongoing light zeitgeber when dusk was expected causes a delay in the expression of evening peaking genes which are delayed by the continuous light signal. Then, on subsequent evenings the influence of the diel dusk signal is ‘forgotten’ as the governance of the endogenous clock takes over. The very long period observed at 0-24h (28.61h) may be due to a phase shift rather than an intrinsic lengthening of period per se. Whether this trait is unique to wheat or can also be seen in other plant species is, to our knowledge, unknown.

• line 118: what is your defined cutoff for significance of the Chi square test (p=0.03 not regarded significant?)

The reviewer is completely right, we have now clarified this. Ln 145-149

• figure 1h,i: In order for the reader to see whether A and D (Figure 1h) or A (figure 1i) are indeed arrhythmic, one would need to see plots with a normalisation as done in figure 1m for 1l.

We have now removed the triad showing one rhythmic gene and two arhythmic genes (as Fig. 1h already illustrates this type of circadian imbalance) and replaced this with a side by side comparison of how imbalance in rhythmicity differs from imbalance in relative amplitude as suggested.

• figure 1h-m (and others with circadian time course traces): could a measure of variation (e.g. SD, SEM, confidence interval) be plotted as a shaded region around the curves (unless they're so small that they are there but not visible)?

We have now added error bars to these plots to show standard deviation between replicates, in Fig. 1 h, j, k and l. We could not think of an accurate way to display this information for the mean normalised data (Fig 1. i and m) so have not put error bars on these plots.

• line 139 (also in 737 and 450): give reference to Ramirez-Gonzalez et al in the same style as the rest of the manuscript (number)

Thank you for raising this, we believe we have corrected all in-text citations (both narrative and fully parenthetical form) for consistency with the APA format used by the majority of Review Commons affiliate journals.

• Clustering (modules): What is the reason for choosing 9 clusters? Was this number optimised or chosen for other reasons?

WGCNA uses an unsupervised clustering algorithm that works within the supplied parameters to determine the optimum number of clusters to explain the dataset, without prior specification of the number of clusters. We have amended the manuscript text to clarify this Ln237-239.

• lines 280 - 284: The TaELF3-1D phenotype could be explained a bit better to the non-wheat specialist, for example by mentioning in the beginning of this set of sentences.

Done (Ln 314-318).

• The authors present an analysis of TF binding sites. Can they say something about binding sites in a less sophisticated manner, such as on some very well-known motifs in promoters like the evening element?

We agree that this is a very interesting question, and one that we may investigate in more detail with our data in the future. In this paper, we performed a global analysis of wheat TFBS predicted from orthologous Arabidopsis TF targets. These targets have been experimentally validated in Arabidopsis using DAP-seq, but we have not validated that these binding sites exist in wheat promoters. We therefore took a tentative approach, and presented only enrichments at the superfamily level rather than talking about specific regulatory motifs.

The evening element would fit most likely fit within the MYB or MYB-related TFBS superfamily, however the diversity of transcription factors in this family means that there is significant enrichment of these TFBS in multiple modules throughout the day (Supplementary Figure 11). In summary, a more in depth TFBS analysis of known circadian motifs is of great interest, but we feel would be a substantial work in its own right.

• Figure 1h-l: If known or meaningful, it would be interesting to know the gene identities behind the triads shown, as in supplementary figure 5.

These triads were selected as case studies to exemplify the ways in which we were defining imbalanced circadian triads. They have no particular relevance to the figure, but out of curiosity, these are the closest Arabidopsis orthologs for the triads displayed in Fig. 1:

Triad 408 has highest identity to a hypothetical protein (AT4G26415).

Triad 2454 is similar to AT3G07600, a heavy metal transport/detoxification superfamily protein

Triad 13405 is similar to AT3G22360, encoding an ALTERNATIVE OXIDASE 1B, AOX1B

Triad 10854 is similar to NSE4A, a δ-kleisin component of the SMC5/6 complex, possibly involved in synaptonemal complex formation (AT1G51130).

Information about wheat gene names in each triad and their Arabidopsis orthologs can be viewed in Supplementary Table 11, so that readers can search for genes of particular interest to them.

• Figure 4 and text: The illustration of starch metabolism is very helpful. However, I think the paper would benefit from giving a better reason for the selection of this specific set of processes, for example by relating these findings to functional differences in starch metabolism in the two species (in contrast to Arabidopsis, wheat stores little starch in leaves but uses fructans as main reserve carbohydrate)? Are there known differences in the dynamics of starch degradation during the night?

The reviewer raises an interesting point, and we have now clarified in our results that the stated differences between starch regulation in Arabidopsis and wheat was part of the motivation behind studying this pathway. Starch is at the centre of plant primary metabolism as a carbon storage source and is arguably one of the most important features that breeders look for in regard to grain filling and yields. Additionally, it is of interest to circadian biologists as starch (as well as sucrose) have been shown to transiently cycle and to be regulated by the circadian clock. However, in wheat, carbon storage primarily uses sucrose rather than starch, and we have now added sucrose to Figure 5 to place it in this context. We think your suggestion has now improved our explanation for why we focused on starch in the manuscript, and we are grateful for your input (Ln 408-421).

We also agree that the differences in the ways that Arbaidopsis and wheat utilise starch versus sucrose, and perhaps the role that fructans have in as a reserve carbohydrate and in protection against freezing in wheat may be one of the reasons we are seeing differences in circadian regulation of starch. We have now added this to our discussion (Ln 584-592).

• Figure 4: triose-phosphates can be transported in and out of the chloroplast, as is illustrated in the figure. However, the illustration looks as though they are converted to hexose phosphates during the transport process. In order to be consistent with other transport processes of the figure (maltose and glucose), triose-phosphate should be repeated on the cytosolic side.

We have now amended this (new Fig. 5). Thank you for your feedback.

Methods - line 543: if I understand correctly that triplicates were collected and analysed for each time point, '18 samples' is mis-leading (18 time points would be more accurate).

We agree this was badly worded. Changed Ln 615.

Supplementary - Supplementary figure 3: x axis label very small and contains typo

Now corrected. Also enlarged axis for Supplementary Figure 2.

• Supplementary table 1: Romanowski et al 2020 (add year), or use ref. number citation style as in the rest of the manuscript

Thank you for raising this, we have now hopefully corrected all in text citations (both narrative and fully parenthetical form) to be consistent with APA format used by the majority of Review commons affiliate journals.

• Supplementary table 9, primary metabolism: does bold highlighting of Arabidopsis accession numbers have a meaning or is it accidental?

We apologise that this was unclear. We have corrected this. Supplementary Table 10 now also has a “Read me” tab which explains that table.

Reviewer #2 (Significance (Required)):

I believe this is a precious, carefully generated and analysed dataset which many biologists will benefit from, beyond wheat or circadian specialists. The dataset expands the knowledge of circadian transcriptome regulation to an important crop and contributes a resource of which only a handful of others exist in other species. Many high impact papers on RNAseq include some follow-up on candidates, for example in Romanowski et al 2020, which is admittedly easier to do in Arabidopsis than wheat due to the availability of genetic resources.

My expertise: Plant circadian clock (Arabidopsis), dataset analysis (but not specifically for RNAseq)

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

This manuscript is based on the analysis of a single experiment consisting in transcriptomic profiling of one (hexaploid) wheat genotype along 3 days (samples taken every 4 hours). The experiment is performed in constant light conditions, allowing detection of transcripts controlled by the circadian clock. The bioinformatic analysis studies the dynamics of the different homoeologous transcript in the polyploid genome and compares cycling transcripts in wheat with what is known from Arabidopsis.

The manuscript is well written, the methods are correct, the analysis performed is sufficiently extensive and the figures are clear. The manuscript finds interesting expression patterns among homeologous genes, and goes into detail on important differences in circadian regulation of relevant gene families between Arabidopsis and wheat. The work is purely descriptive and does not aim at associations with physiological phenotypes, but the bioinformatic analysis is very thorough and uncovers interesting examples.

Only one caveat: For what I gather, there is no replication in the RNA-seq experiment, although the exact method does not appear in the text. From the Methods section: "tissue was sampled every 4h for 3 days (18 samples in total)" and "At each timepoint, we sampled the entire aerial tissue from 3 replicate plants". Whether these samples were pooled or not is not described. The "Data Availability" section links to 18 RNA-seq paired end libraries, which suggest that the replicates were pooled, although some type of barcoding might have been used. The text should mention if the replicates were pooled or not, and, if so, what was the method used for poling (tissue, RNA or libraries). Even in the case of no biological replication the manuscript brings interesting insights into wheat transcriptomics and circadian biology. The editor (or the rules of the journal) should decide if they accept articles with no "real" biological replication (I am sure we all understand by now the benefits and limitations of pooling biological replicates into a single RNA-seq library).

There was replication within the RNA sequencing experiment, and we apologise that this was unclear from our manuscript. Each timepoint consisted of three independent biological replicates. We have now created a new “Experimental context” section in the results to explain this (Ln 74-82) and have clarified in the methods how our data was processed (Ln 609-615 and 636-638).

We have now included an additional matrix with TPMs at the replicate level to assist readers in looking at specific genes of interest (Supplementary Table 12).

Minor comments:

The description of the experimental setup in the first sentence of the Results section is too brief. Could you please talk about for how long the experiment was running? At what intervals the samples were taken? What conditions were used?

We apologise that this was unclear. We hope that the new Experimental Context section, added in response to comments from several reviewers, makes this much clearer, alongside the clarification in the methods (Ln 609-615 and 636-638).

Line 280: "...due *to* an introgression..."

Corrected. Ln 315

The legend of Figure 3l says elf4 instead of elf3

We thank the reviewer for noticing this mistake that we have now corrected.

Line 306 "says Supplementary Note 7 instead of Supplementary Note 7

We are not sure what is to be corrected here!

Reviewer #3 (Significance (Required)):

This works advances our knowledge on how genome wide expression levels are controlled by the circadian clock in polyploids. Although previous works had performed similar analyses in other polyploid plants, this is the first time this is done in an hexaploid. This work is a starting step to understand gene regulation in this important crop, and have interest for researchers working in fundamental and applied plant biology.

Thank you for your positive comments and your feedback in improving this manuscript. We would like to clarify that to our knowledge, this work presents the first analysis of a circadian transcriptome in a polyploid crop. The work by Greenham et al, although undoubtably providing insight into circadian regulation of ancient paralogs, was performed in the diploid Brassica rapa.

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Referee #3

Evidence, reproducibility and clarity

This manuscript is based on the analysis of a single experiment consisting in transcriptomic profiling of one (hexaploid) wheat genotype along 3 days (samples taken every 4 hours). The experiment is performed in constant light conditions, allowing detection of transcripts controlled by the circadian clock. The bioinformatic analysis studies the dynamics of the different homoeologous transcript in the polyploid genome and compares cycling transcripts in wheat with what is known from Arabidopsis.

The manuscript is well written, the methods are correct, the analysis performed is sufficiently extensive and the figures are clear. The manuscript finds interesting expression patterns among homeologous genes, and goes into detail on important differences in circadian regulation of relevant gene families between Arabidopsis and wheat. The work is purely descriptive and does not aim at associations with physiological phenotypes, but the bioinformatic analysis is very thorough and uncovers interesting examples.

Only one caveat: For what I gather, there is no replication in the RNA-seq experiment, although the exact method does not appear in the text. From the Methods section: "tissue was sampled every 4h for 3 days (18 samples in total)" and "At each timepoint, we sampled the entire aerial tissue from 3 replicate plants". Whether these samples were pooled or not is not described. The "Data Availability" section links to 18 RNA-seq paired end libraries, which suggest that the replicates were pooled, although some type of barcoding might have been used. The text should mention if the replicates were pooled or not, and, if so, what was the method used for poling (tissue, RNA or libraries). Even in the case of no biological replication the manuscript brings interesting insights into wheat transcriptomics and circadian biology. The editor (or the rules of the journal) should decide if they accept articles with no "real" biological replication (I am sure we all understand by now the benefits and limitations of pooling biological replicates into a single RNA-seq library).

Minor comments:

The description of the experimental setup in the first sentence of the Results section is too brief. Could you please talk about for how long the experiment was running? At what intervals the samples were taken? What conditions were used?

Line 280: "...due to an introgression..."

The legend of Figure 3l says elf4 instead of elf3

Line 306 "says Supplementary Note 7 instead of Supplementary Note 7

Significance

This works advances our knowledge on how genome wide expression levels are controlled by the circadian clock in polyploids. Although previous works had performed similar analyses in other polyploid plants, this is the first time this is done in an hexaploid. This work is a starting step to understand gene regulation in this important crop, and have interest for researchers working in fundamental and applied plant biology.

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Referee #2

Evidence, reproducibility and clarity

Summary

Rees et al. present an RNAseq time course of bread wheat. Its recent polyploidisation is one motivation for this study as gene expression dosage is known to be important for clock function in other plants. The time course covers 3 days at sampling intervals of 4h of 2-week old wheat plants (all aerial tissues), in triplicates. The subsequent analysis of the RNAseq data includes analysis of the generated data by itself (e.g. GO analysis, rhythmicity, period and phase analysis, rhythmicity of transcription factor families as well as TF binding sites) as well as thorough comparison with published datasets of other species (Arabidopsis, Brassica rapa, Brachypodium dystachion). One of the key findings is that the mean period length and the period spread are larger in wheat than in these other species). Circadian clock genes largely have similar dynamics in wheat compared to Arabidopsis. In addition, one focus is the analysis of the dynamics of three genes of one triad and imbalance / balance of such triads. To the surprise of the authors, circadian regulated and clock genes were not necessarily balanced. Silencing is one of their explanation for imbalance of circadian genes as arrhythmic genes of one triad are typically those with the lowest expression level. Finally, the authors point out more examples of rhythmic processes and genes (photoreceptors and signalling, auxin, carbon metabolism) and their commonalities and differences with Arabidopsis.

Major comments

• The key conclusions and the data are convincing
• line 120 and figure 1: In my opinion, q > 0.05 is not a good definition of arrhythmicity as non-significant q-values can result from either noise in spite of rhythmicity or from arrhythmicity. A more statistically sound way to detect arrhythmicity could for example be two-one-side tests (for example in the R package 'equivalence', e.g. see usage for time courses by Noordally et al. 2018, https://www.biorxiv.org/content/10.1101/287862v1).
• lines 480-484 and intro: In the introduction, the authors write that expression levels of clock components are important for the function of the clock, and that this is one motivation for the current study where polyploidisation is expected to affect the expression levels of clock genes and their outputs. I wonder what answers or speculations this study provides in the end, or whether such answers / speculations should be made clearer. For example, do the authors think that the higher variability of periods in wheat could be a consequence of lower robustness (in addition to possible spatial differences that are mentioned) due to polyploidisation? Is anything known about the period of rhythms of close wheat relatives that did not undergo polyploidisation? Did you look at dampening over the time course in wheat vs. Arabidopsis?

Minor comments:

Introduction

• lines 49: it is unclear what is meant by ppd-1 at this position of the sentence
• line 54/55: clarify that this refers to Arabidopsis thaliana

Results

• line 69 and 76: cite references for these tools here (not only in the methods section)
• line 90-93: Why wouldn't the same thing happen on subsequent subjective evenings?
• line 118: what is your defined cutoff for significance of the Chi square test (p=0.03 not regarded significant?)
• figure 1h,i: In order for the reader to see whether A and D (Figure 1h) or A (figure 1i) are indeed arrhythmic, one would need to see plots with a normalisation as done in figure 1m for 1l.
• figure 1h-m (and others with circadian time course traces): could a measure of variation (e.g. SD, SEM, confidence interval) be plotted as a shaded region around the curves (unless they're so small that they are there but not visible)?
• line 139 (also in 737 and 450): give reference to Ramirez-Gonzalez et al in the same style as the rest of the manuscript (number)
• Clustering (modules): What is the reason for choosing 9 clusters? Was this number optimised or chosen for other reasons?
• lines 280 - 284: The TaELF3-1D phenotype could be explained a bit better to the non-wheat specialist, for example by mentioning in the beginning of this set of sentences.
• The authors present an analysis of TF binding sites. Can they say something about binding sites in a less sophisticated manner, such as on some very well-known motifs in promoters like the evening element?
• Figure 1h-l: If known or meaningful, it would be interesting to know the gene identities behind the triads shown, as in supplementary figure 5.
• Figure 4 and text: The illustration of starch metabolism is very helpful. However, I think the paper would benefit from giving a better reason for the selection of this specific set of processes, for example by relating these findings to functional differences in starch metabolism in the two species (in contrast to Arabidopsis, wheat stores little starch in leaves but uses fructans as main reserve carbohydrate)? Are there known differences in the dynamics of starch degradation during the night?
• Figure 4: triose-phosphates can be transported in and out of the chloroplast, as is illustrated in the figure. However, the illustration looks as though they are converted to hexose phosphates during the transport process. In order to be consistent with other transport processes of the figure (maltose and glucose), triose-phosphate should be repeated on the cytosolic side.

Methods

• line 543: if I understand correctly that triplicates were collected and analysed for each time point, '18 samples' is mis-leading (18 time points would be more accurate)

Supplementary

• Supplementary figure 3: x axis label very small and contains typo
• Supplementary table 1: Romanowski et al 2020 (add year), or use ref. number citation style as in the rest of the manuscript
• Supplementary table 9, primary metabolism: does bold highlighting of Arabidopsis accession numbers have a meaning or is it accidental?

Significance

I believe this is a precious, carefully generated and analysed dataset which many biologists will benefit from, beyond wheat or circadian specialists. The dataset expands the knowledge of circadian transcriptome regulation to an important crop and contributes a resource of which only a handful of others exist in other species. Many high impact papers on RNAseq include some follow-up on candidates, for example in Romanowski et al 2020, which is admittedly easier to do in Arabidopsis than wheat due to the availability of genetic resources.

My expertise: Plant circadian clock (Arabidopsis), dataset analysis (but not specifically for RNAseq)

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Referee #1

Evidence, reproducibility and clarity

In this study, Rees et al. perform an RNA-seq circadian time course experiment in the recently formed allopolyploid wheat. Through comparisons with other circadian transcriptomic datasets in other species it appears that the period of rhythmic genes is much more variable in wheat with a shift to longer periods compared to the other species examined. Interestingly, by analyzing circadian parameters among expressed genes, they find evidence that this newly formed allopolyploid already shows signs of divergence in circadian traits among homoeologs. A thorough comparison with circadian regulated genes in Arabidopsis reveals overlap in phasing of genes involved in certain biological processes such as photosynthesis and light signaling whereas genes involved in starch metabolism were found to have different levels of rhythmicity and phasing. This dataset will be a great resource for the community and enable new predictions about the influence of polyploidy on the circadian control of important crop improvement traits and the circadian regulation of gene expression.

Major Comments

1. The results section starts with very little explanation of the experiment. It would help to provide a little more detail at the start of the results to explain the context for the experiment and what was done, when samples were collected and for how long. For the methods section, it isn't until line 650 that it is clearly stated that the sampling started at ZT0. It would be better to put this in the plant materials and growth condition section.
2. The low proportion of circadian regulated genes is likely due to the very low cutoff for calling a gene expressed, especially when there are three days of repeated timepoints. If a gene is expressed across the time course it should have values above TPM 0 for at least 3 time points in order for it to be expressed each day. I'd also be suspicious of a gene with a TPM value less than 0.5. Comparing these types of numbers is always challenging due to the various cutoffs used. Along those lines, why was a different filtering scheme used for Arabidopsis (line 657)?
3. In reference to the shortening of the period every day, this should be interpreted with caution. Period estimate of a single cycle are not very reliable and the SD for each day is around 3h so it is difficult to draw any conclusions about changes in period each day. One option would be to only include genes with an SD less than 1h or alternatively to remove the discussion surrounding the comparison of period across the three days and focus on the period results for the full 24h-68h window shown in 1b. While 2 days is better it is still not ideal for calling period; however, your first day will still have a strong diurnal driven pattern that will likely skew your circadian period.
4. Line 87-93: If the dusk cue is important for clock expression you would think this would be biased towards genes that peak later in the day or near dusk. This argument should be connected better to the period results discussed on lines 98-101.
5. Lines 650-652 of the Methods mentions that one of the main interests was the response to transfer to L:L, but this isn't mentioned in the introduction and doesn't come up much in the Results section. Most of the expression comparisons are focused on the 24-68h window. It also isn't clearly explained why the first day in LL is still a diurnal cycle. This would be helpful for non-circadian readers who may wonder why the first day is not included in all the analyses.
6. The phase comparisons shown in Figure suppl 4 are confusing. Suppl. Note 3 states that the period from the 24-68h data window was used to establish the bins but then the phase is shown for 3 different windows for each column? When calculating the phase for each of those 3 windows which period was used as the denominator in the phase calculation? Was it the period that matches the window used to calculate phase? What does the plot look like if phase is called on the same window used to calculate period (24-68)? What method was used to call phase in Suppl. Fig 4? As shown in Suppl Fig. 3 the method can influence the phase distributions. The methods suggest that the phase was determined with Metacycle but then FFT and MESA were used to verify. What does this mean verify, were they adjusted if FFT/MESA didn't agree?
7. It is difficult to interpret the value of the period and phase comparisons shown in Fig. 1b, c, e and f after the preceding section about how variable the period and phase is across days. It is also surprising that the full 3 days were used to calculate the circadian statistics considering the first day is still under diurnal control. Do the ratios remain the same if the statistics are performed only on the 24h-68h window? For consistency with the rest of the paper and avoid confusion it would be best to have all circadian parameters measured using the same time window (24h-68h).
8. Fig 1h-m. How were those genes chosen? It would help to see the SD of the replicates shown, since this is just showing one triad. It would be helpful to see a plot that represents the full set of triads rather than just one that looks best. If normalized to a standard phase they could be put on the same plot. For example, panel j is meant to show the 8h lag of subgenome D. If the data is normalized so that A and B are set to the same phase all the triads could be displayed with shaded SD bars to show the variation. Something like this would be a better representation of the data rather than showing just one example.
9. It is surprising that there aren't more comparisons with the B. rapa dataset, especially when discussing the clock genes that show balanced or imbalanced expression. Are they similar in B. rapa and does it support your hypothesis that unbalance for certain genes are selected against?
10. Figure 2 networks. Why were these specific modules selected? Is it actually appropriate to directly compare these modules? I do see that some of the comparisons have high correlations from panel a, but not all. For example, in panel b the W9 and A9 modules have a correlation value of 0.92, which seems appropriate. However, panel c (modules W3 and A2) have a correlation of 0.42, which seems far too low to make any sort of comparison meaningful. Further, as described in methods comments, using a cutHeight as low as 0.15 will likely lead to some number of genes in any given module that do not necessarily "share" a similar expression pattern. These genes could have a pattern that has very low correlation to their module eigengene and were only placed in that module because the pattern was "less similar" to other module eigengenes. The current expression plots in this figure follow a clear pattern, but I suspect this would be even more apparent if the genes within these modules had a higher correlation to the module eigengene. Perhaps the current genes in these modules could just be filtered to have a higher correlation score?
11. Lines 327-334: I am not following the connection between 'response to abiotic stimulus' and the photoreceptor and light signaling proteins. At the start of this section (line 308) the authors say that the GO analysis was only done on rhythmically expressed genes but the reference to only one PHYA being rhythmic and yet multiple genes are shown in the plot in fig. S16. Does this mean that all the genes were shown and not just the rhythmic ones? This would explain why many of the PHY and CRY genes don't seem to have rhythms. This should be clarified better in the text or indicated in the plot which ones were called rhythmic. Since the first day following transfer is still the diel pattern from the entrainment condition, what does the PHY and CRY expression look like? Does it appear rhythmic under diel but lose rhythmicity in LL? It should be noted in the text that arrhythmicity in circadian conditions doesn't mean there isn't rhythmicity under diel conditions. This could be an additional explanation apart from the current one in the text that the regulation is at the level of protein stability/localization. Overall, this entire section is very long and entirely based on data shown in the supplemental material. I do appreciate having the individual gene plots that supplement figure 4 and would suggest either providing a main figure to highlight a small subset of genes or pathways in this section or shorten it and focus on the results shown in the main figures.
12. Primary metabolism section: in terms of the supplemental figure, similar to the previous one I think it would declutter the plots if the genes that are not rhythmic were left out and simply indicate below the plot that they didn't meet the rhythmicity cutoff. This is another area where there is more discussion surrounding the supplemental figures than the main figure 4.
13. For all gene expression figures there should be SD or SE shown either as bars or ribbons to represent the variation in replicates.
14. It would be very helpful to include the code used to generate the networks and perform the cross-correlation of eigengenes across networks should be included in the Methods. This will also save you from responding to email requests!

Minor Comments

1. Figure 1, panel d: - The "unbalanced" triads that are depicted by the lighter shading; do these in fact have a different cutoff than the original rhythmic homoeologs? In the figure it says q<0.1 but I thought it was q<0.01.
2. Hard to directly compare the GO term overlap in Figure 2f. Might be better to only show the results for the 4 pairs shown in b-e and put them side by side in the bubble plot.
3. Line 314 -316 don't see supp tables 10, 11
4. For the selection of B. rapa circadian paralogs with similar and differential expression patterns (starting line 714), the authors choose a hard cut off of 0.001 (differentially patterned) OR 0.1 (similarly patterned). What happens to the genes that are between these two cut offs or is this a typo. Since all the other cutoffs for rhythmicity was set at 0.01 it seems likely that this is a typo.
5. Line 681. Should be supplemental Figure 6 not 9.
6. References to most supplemental figures are not the correct number.
7. Labels above the plots in Supp Fig5 do not match the legend.
8. Suppl table 7 should be as a separate .csv file or similar to be able to see the full table.
9. Line 723 should be B. rapa not B. napus.
10. Figure 4. There is no explanation for what the black boxes represent in the figure legend.

Significance

This study provides new insight into the circadian regulation of the transcriptome in a new allopolyploid. It adds a valuable resource to a growing collection of circadian studies in important crops and will greatly improve our efforts to learn more about the circadian control of important crop improvement traits. The dataset will be of interest to other plant circadian biologists as well as the general plant biology community who focus on monocot crops. My expertise is more on the transcriptomic side and I do not have the expertise to evaluate the phylogenetic work presented in this study.

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Reply to the reviewers

Manuscript number: RC-2021-01219

Corresponding author(s): Rajan, Akhila

1) General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

The goal of this study is to:

• Define how prolonged exposure to a high-sugar diet (HSD) regime alters both the lipid landscape and feeding behavior.
• Determine how changes in lipid classes within the adipose tissue regulates feeding behavior. Key findings:

In this study, by taking an unbiased systems level and genetic approach, we reveal that phospholipid status of the fat tissue controls global satiety sensing.

Impact of Key findings:

By uncovering a critical role for adipose tissue phospholipid balance as a key regulator of organismal feeding, our work raises the possibility that the rate-limiting enzymes in phospholipid synthesis, including Pect, are potential targets for therapeutic interventions for obesity and feeding disorders.

Peer review comments:

This study has immensely benefited from the thoughtful peer-review of three reviewers. As per their recommendations, we have performed a major revision by performing additional experiments (see summary table below in next section) and strived to address the major concerns raised. Based on our reading, there were two major concerns that overlapped between all three reviewers raised. They are as follows:

• Does the genetic disruption of Pect in fly fat body alter phospholipid levels? Two reviewers (#2 and #3) recommended that we perform lipidomic analyses on adult flies with adipose tissue specific knockdown of For the revised version, we have completed this lipidomic experiment, and present results as a new main Figure 6, Supplemental S7 and S9.
• Is the dampened HSD induced hunger-driven feeding (HDF) behavior because of increased baseline feeding (#1 and #3)? In addition, reviewer #1, asked us whether HSD flies experience an energy-deficit? In other words, we were asked to uncouple whether what we observed was HSD-driven allostasis or indeed, as we had interpreted, that HSD dampened hunger-driven feeding response.

Hence, they recommended that we:

1. Re-analyze our hunger-driven feeding datasets and present non-normalized data (also requested by Reviewer #3) and show baseline feeding behavior on HSD. To address this, we have completed this analysis and present our results in Figure 1B-D and S1.
2. Determine whether the HSD fed flies display an energy deficit on starvation. To this end, we performed an assayed starvation-induced fat mobilization on HSD, results for this are now presented on Figure 1E-G and S2. Conclusions after the revision:

First, it is important to note here that the additional experiments have not caused a significant revision of the major conclusions of the original version of our study. In fact, we hope that the revised version provides clarity and further substantiation to our original arguments.

• The lipidomics experiments on Pect fat-specific knock-down flies show that reducing Pect in fat-body causes a significant reduction in certain PE lipid species (PE 36.2 specifically- Figure 6B). This is consistent with a prior report on lipidomics of the Pect null allele by Tom Clandinin’s group (PMID: 30737130). Furthermore, we note that when Pect is knocked down in the fat body, there is a significant increase in two other classes of phospholipids LPC and LPE (Figure 6A). Together, this suggests that an imbalance in phospholipid composition in the absence of Pect activity in fat.
• The starvation-induced fat mobilization experiments show that despite being fed a prolonged HSD, adult flies sense starvation and effectively mobilize fat stores, at a level comparable to Normal food (NF) fed adult flies, suggesting that even despite HSD exposure, adult flies experience an energy deficit on starvation.
• In our non-normalized data, we find that the baseline feeding events are not significantly altered between HSD and NF-fed flies (Figure 1D). This suggests that the effects we observe are not due to an increase in the “denominator”, but a dampening of hunger-driven feeding on HSD. With regard to our original version, all three peer-reviewers found that the study was interesting, significant, important, and novel – Reviewer #1: “The work is potentially novel and interesting”; #2 : “I find the study to be potentially very important - the authors combine a longitudinal study that would be difficult in any other model with the powerful genetic tools available in the fly. The conclusions are mostly convincing”; #3: “This manuscript demonstrates how fat body Pect levels affect HSD induced changes in hunger-driven feeding response. I agree with all the reviewers points; potentially very interesting”. But had requested that we provide further substantiation and clarification.

We sincerely hope that the peer-reviewers find that our revised version with additional new experimental datasets, improved data visualization, and the presentation of non-normalized raw data points, makes this study clear, compelling, and well-substantiated.

• Point-by-point description of the revisions This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

Below we summarize in Part A, the key experiments that were performed to address the major concerns. In Part B, we provide a point-point response to each reviewer with embedded datasets.

Part a:

We performed several new experiments, including:

• To address the primary concern of Reviewer #1 regarding whether the HSD flies have a similar energy deficit to Normal food (NF) fed flies, we performed analysis of stored neutral fat Triacylglycerol (TAG) reserves and how HSD fed flies mobilized fat stores on starvation. We present these results in Figure 1E-G, S2. These results show that HSD-flies despite accumulating more TAG (S2), breakdown a similar amount of fat reserves as NF-fed flies on starvation at any time-point (Figure 1E-G). This suggests that HSD-fed flies do sense and respond to energy deficit.
• To address concerns of reviewer #2 and #3 on whether Pect genetic manipulation affects specific phospholipid classes, we performed lipidomic analyses. The table below summarizes the new 3 new figures and 4 supplemental figures (blue text are all new figure numbers and figure panels) and three new Supplementary files as per reviewer’s request.

Figure #

Main point

New datasets in revision

Companion Supplement

1

HSD alters feeding behavior, but flies still breakdown TAG on starvation.

TAG storage and breakdown over longitudinal HSD shows that HSD and NF fed flies show similar levels of TAG breakdown on starvation, despite consistently elevated TAG on HSD. This supports the idea that flies do sense starvation even on HSD, but there is a uncoupling of the feeding behavior after Day 14. Revised the data representation of Figure 1 to show non-normalized data over time. S1 and S2 companions are new in the revision. Panels 1D to 1E are new for the revision.

S1- Raw data of feeding events plotted.

S2 Elevated TAG at all time points.

2

HSD causes insulin resistance

S3A added to show that insulin transcript levels remain the same in response to reviewer #3’s concerns.

S3

3

Phospholipid concentration raw data from lipidomic on Day 7 and Day 14 HSD suggest that PC, PE levels are increased on Day 14 HSD.

Figure 3 revamped to show new data visualization and non-normalized raw data to address Reviewer #2’s major concerns. S4A and S4B added. In addition Supplementary File 1 and 2 provided with raw lipidomics data as per reviewer #2’s request.

S4.

S4A- non normalized raw data of all other lipid classes on HSD.

S4B- fatty acid species data on Day 14 added as per request of rev.#2.

4

HSD regulate Apo-I levels in the IPCs and phenocopies Pect KD.

Added Figure 4A to show that HSD phenocopies Pect-KD in terms of delivery to brain

S5 showing the validation of the Apo-I antibody.

S6 validation of Pect KD and over-expression and Pect mRNA levels dysregulation on HSD.

5

Pect RNAi is insulin resistant

N/A

N/A

6

Pect knockdown shows significant increase in LPC and LPE, and a non-significant reduction in PC, PE levels. Specifically, the PE lipid class PE36.2 is downregulated.

Fig 6, S7, S9 are completely new based on reviewer #2 and #3 requests. In addition Supplementary File 3 provided with raw lipidomics data as per reviewer #2’s request

S7, S8, S9#.

S7- new Pect KD other classes

S8- new PE classes for day 14 and Pect associated classes.

S9- Pect OE lipidomics

7

Pisd and Pect activity in adipocytes are required for hunger-driven feeding behavior in normal diets

Pisd RNAi data was moved from supplement to main figure.

N/A

Note on revised text: We have revised text not only in the results section, but also as per reviewer #2’s recommendation, we have revamped our introduction and discussion as well. Since the manuscript has been significantly revised to include a main figure 6, fully altered Figure 1 and 3, multiple new supplemental figures, the changes in text are extensive. Hence, they are unmarked in the main text. Nonetheless, we hope that the reviewers will be able to evaluate these changes, as we have provided the specific locations in text and embed key figures in the point-point response below.

__Part B: __Point-Point responses to reviewer comments.

Reviewer #1 comments in Blue, author response in black.

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

In this manuscript, Kelly et al. show that the difference between the feeding behavior of fed and starved flies (hunger-driven feeding; HDF) is absent in animals fed a high-sugar diet (HSD) for two weeks or more. The disappearance of HDF with HSD coincides with changes in phospholipid profiles caused by HSD. Furthermore, RNAi-mediated downregulation of Pect in the fat body-a key enzyme in the PE biosynthesis pathway-phenocopies physiological effects of HSD. Moreover, downregulation or overexpression in the fat body abolishes or induces HDF, respectively, abolishes or induces HDF, respectively, independent of HSD treatment.

Overall, the manuscript is well-written and the phenotypes are clear. However, I have major concerns regarding the authors' interpretation of the data and their conclusion. Most importantly, while it is clear that the authors' high-sugar dietary treatment affects feeding behavior and physiology, I am not convinced that the changes can be considered "hunger-driven"-which is central to the main point of the manuscript. Therefore, it is my recommendation that the authors substantially revise the manuscript by either showing additional/re-analyzed data that rule out alternative hypotheses, or rewriting the manuscript keeping alternative interpretations in mind.

We are thankful to this reviewer for their thoughtful critique, and constructive and specific suggestions on how we can redress these concerns. We have taken on board the concerns of this reviewer regarding our interpretation of whether the changes in feeding behavior can be considered hunger-driven or not. Based on their advice, we have made significant changes by addressing: i) does HSD increased baseline feeding- we now show non-normalized raw data and data supports conclusion that baseline feeding is not higher; ii) whether HSD- fed flies can sense an energy deficit at levels similar to NF fed flies- we show that HSD flies sense energy deficit. We have provided detailed response below, and we hope the reviewer finds the additional datasets and re-analyzed data are consistent with the interpretation that prolonged HSD dampens starvation induced feeding. In addition to this key concern this reviewer has made a many other salient points that we have addressed with additional data or by clarifying the text.

Major comments: 1) The data do not sufficiently show that the long-term HSD regime disrupts "hunger-sensing." The manuscript should address alternative hypotheses by showing raw instead of normalized data, rewriting the manuscript with a new central conclusion, or running additional experiments that actually show a defect in hunger-driven response. a. The main results that the authors rely on for the argument is that the ratio of feeding events that the starved and non-starved flies eat is different between the groups fed normal or HSD. However, because the authors only show normalized data (normalized to non-starved flies; Fig. 1), it is difficult to tell whether the change is due to a chronically increased feeding in non-starved HSD flies-maybe in perpetual hunger-like allostasis-or dampened starvation response. Indeed, the data shown in Fig S1 show that flies fed HSD for as short as 5 days show more frequent feeding events compared to age-matched controls fed normal food. It is possible that because the HSD-fed flies eat more than NF-fed flies, even without being starved, the ratio of starved/non-starved feeding is lower in the HSD-fed group-due to changes in the denominator, rather than the numerator.

We have taken onboard this concern regarding presenting only normalized data, and that clouded the interpretation and left open other possibilities. In the completely revised figure 1 and S1. We now show non-normalized data, as a function of time. First we note that HSD-fed flies, do not show higher baseline feeding that NF fed flies, except on Day 10 of HSD, when there is a modest but significant elevation (Figure 1D).

Nonetheless, on Day 10 HSD, flies still display increased hunger-driven feeding HDF (Figure 1C), it is only after Day 14 HSD that HSD dampens the starvation induced feeding.

1. It is also possible that the HSD-fed flies are simply not in as big an energy deficit physiologically, due to the increased fat deposits they've accumulated (as the authors show later in the manuscript). It may take longer for the fat HSD flies to reach substantial energy deficiency than the NF flies, but they still may eventually be able to appropriately respond to hunger, just like NF flies. In such case, it would be a misnomer to call this behavioral change a 'defect in hunger-driven feeding behavior.' Maybe an experiment with a dose-response curve of "hunger driven feeding response" as a function of duration of starvation would help? Prompted by this reviewers question, we asked whether HSD fed flies, that have a higher baseline neutral fat store (Triacylglycerol-TAG) level, and if HSD-fed flies can sense energy deficit. For this, we revisited the longitudinal assays for neutral fat triacylglycerol (TAG) storage that our lab had generated, along with the HSD-HDF studies. We now present this evidence as Figure 1E-1G and Figure S2. Overall, our experiments point to the idea that adult flies fed HSD, are able to sense and mobilize TAG stores effectively throughout the 28-day time point that we analysed.

First as shown in Figure S2, flies fed HSD display an increase in TAG levels. But it is to be noted that while TAG stores increase, the increase is not linear with time. This suggests that adult flies exposed to HSD store excess energy as TAG, but the increased TAG stores stay within a certain range despite the length of HSD exposure. This suggests that adult flies on HSD still display TAG homeostasis.

Next, to directly address the reviewers point about HSD fed flies not sensing an energy deficit, we subject HSD-fed flies to an overnight starvation, same regime as used in the overnight feeding experiments, and asked whether they mobilize TAG. We noted that flies exposed to HSD breakdown TAG throughout the 28-day exposure at statistically significant levels for Day 3- Day 28, except on 14 and 21 days (Figure 1F). While there is TAG mobilization on Day 14 and 21, the difference is not statistically significant. Nonetheless, we note the same levels TAG breakdown for normal lab food (NF) fed flies on Day 14 and 21 (Figure 1E). Overall, HSD fed flies sense and display energy deficit, as measured by TAG store mobilization, throughout the 28 days of HSD exposure, at levels comparable to NF-fed flies (Figure 1G).

Taken together, these results suggest that while HSD-fed flies experience an energy deficit on starvation, at levels comparable to NF-fed flies, throughout the 28-day time point assayed. But, their starvation driven feeding-response is dampened by Day 14 and by Day 28, the HSD-fed flies display more feeding events than HSD starved flies. These results are consistent with the interpretation that in HSD-fed flies the starvation-induced feeding behavior becomes desynchronized from the starvation induced TAG-mobilization, suggesting that there is an absence of hunger-driven feeding.

2) How can you be sure that lower Dilp5 immunofluorescence is indicative of increased Dilp5 secretion? Wouldn't decreased production of dilp5 also have the same results?

It has been shown previously in HSD fed larvae are hyperinsulinemic, i.e., they have 55% increase in circulating Dilp2 ( PMID: 22567167). Additionally, we have shown that ectopic activation of the insulin-producing neurons by expressing TRPA1, an ion channel that activates neurons, reduces Dilp5 accumulation without a change in Dilp5 mRNA levels (PMID: 32976758), suggesting that reduced Dilp5 accumulation, without alterations to mRNA levels is a proxy for increased secretion. Now, in response to this concern, in the revised manuscript, we have added qPCR data of Dilp2 and 5 (Figure S3A), which show no difference in expression levels after 14 days on HSD. Therefore, there is no dip in Dilp5 mRNA production. Given that Dilp2 and Dilp5 mRNA levels remain the same, but we see reduced Dilp5 accumulation, we interpret this to mean that Dilp5 secretion is increased.

1. Also, the authors should state in the main text that it is Dilp5, not just any Dilp. Thanks for this suggestion and we have fixed this and referred to Dilp5 specifically throughout the text in the results section.

3) Data presentation: a. Sometimes the data are normalized to NF (Fig 4B-C), sometimes not (ex. Fig 4A, S4C). Unless there is a specific rationale for the data transformation, it would be more appropriate to show untransformed data (ex. Fig 4A, S4C), especially as the authors use two-way ANOVA to determine significance. Only showing the differences implies comparison against a hypothetical mean (i.e. μ0=0), not between two group means.

We thank the reviewers for bringing this issue to our attention. We updated all the figures to show untransformed data in the revised manuscript.

1. Some figures show both individual data points and summary statistics (mean, SD, ... ex. Fig 2A)-which I believe is ideal-but some show only one or the other (ex. Fig 2B, no summary statistics; Fig. 3, no data points. The manuscript would read more convincing if data visualization is consistent across figures. We thank the reviewers for their feedback. We have made changes to all the figures in the revised manuscript to improve visual consistency.

Minor comments: 1) High sugar diet: what is the actual sugar concentration in the NF v. HSD diets? The authors write that the HSD diet contains "30% more sugar" than the NF, but providing the final sugar concentrations-sucrose or others-would be informative for other scientists studying the effect of high sugar diets.

We thank the reviewer for their suggestion and now we have updated the methods to include this sentence. “After 7 days, flies were either maintained on normal diet or moved to a high sugar diet (HSD), composed of the same composition as normal diet but with an additional 300g of sucrose per liter”.

1. Additionally, the definition of HSD is inconsistent. Main text (Page 5, line 17) states that their HSD is "60% more sugar than normal media," whereas the figure legend (Fig 1) and the Methods state that the HSD contains "30% more sugar." We apologize for this egregious typo in the figure legend! We have now fixed this to say 30% HSD. Only 30% HSD was used throughout this study.

2) Starvation medium: please provide justification for why the authors used 1% sucrose/agar for starvation medium, instead of plain agar/water that most labs use. At least clarify and provide a reference for the claim that the 1% sucrose/agar "is a minimal food media to elicit a starvation response."

We are very grateful for this reviewer identifying this this methods description error and bring it to our attention. We used 0% sucrose agar for overnight starvation in this study as most labs do. The error occurred because we were using another manuscript from the lab to help draft the methods section (PMID: 29017032). In that study, where we assayed the effect of chronic starvation our lab used: “1% sucrose agar for 5 days at 25C”. However, in this current study, because we are testing acute effects of overnight starvation, we are using 0% sucrose agar.

3) Pect mRNA level is higher with HSD. This is surprising because not only, as authors mention, is increased PC32.2 with HSD suggests lower Pect activity, but also because Pect RNAi phenocopies long-term HSD in HDF behavior, lipid morphology, FOXO accumulation in fat body. The authors speculate that the data "likely shown an upregulation in an attempt to mediate the Pect dysregulation occurring at the protein level." If that were true, a western blot may be informative. Zhao and Wang (2020, PLoS Genetics) generated a Pect antibody that seems compatible with western blot applications. That being said, I don't think such data is critical for the manuscript. I mention this simply as a suggestion for the authors. a. page 8, line 22-23, did you mean to write "Given how PC32.2 is elevated after 14 days of exposure to HSD, we assumed that Pect levels would be low for flies under HSD," not "high?" Otherwise the subsequent 2 sentences don't make sense.

We agree that the most confusing aspect of the study was that Pect mRNA levels being very high on Day 14 HSD, but nonetheless the effects of Pect-KD phenocopied HSD. To resolve this, we have now performed lipidomic analyses on whole adult flies, when Pect is knocked-down (KD) by RNAi in the fat tissue. We now present a new dataset in Figure 6. Two striking changes occur. They are:

1. Pect-KD shows increase in the phospholipid classes LPC and LPE (Figure 6A). In contrast, LPE is significantly downregulated on HSD Day 14 (Figure 3).
2. Pect-KD shows a significant reduction in specific class of PE 36.2 (Figure 6B). Our data regarding increase in PE 36.2 agree with a previous lipidomic analyses of Pect mutant retina (PMID: 30737130). In contrast, PE 36.2 trends upwards on 14 day HSD (Figure S7C) though not significantly. On 14-day HSD consistent with extreme upregulation of Pect mRNA fed flies (Figure S6A; Pect mRNA 200-250 fold), PE trends upwards on 14-day HSD (Figure 3) and PE 36.2 trends higher (Figure S7C). We note that on the surface of it PE and LPE per se are contrasting between 14-day HSD lipidome and fat-specifc Pect-KD. But there is a significant commonality that under both states there is an imbalance of phospholipids classes PE and LPE. Hence, we propose that maintaining the compositional balance of phospholipid classes PE and LPE is critical to hunger-driven feeding and insulin sensitivity. Hence, either increase or decrease, of these key phospholipid species, may lead to abnormal hunger-driven feeding.

We agree that a western blot would be informative as well, but we were unable to obtain the reagent from Dr. Wang’s group, precluding us from performing this request. See email snapshot.

To ensure that we appropriately discuss and clarify this issue, we have now included a section in the discussion - Page 14 Lines 26-34- under the subtitle “The implications of relationship between Pect levels and HSD”. We have pasted an excerpt from that subsection below for this reviewers assessment.

“Also, we note that over-expression of Pect cDNA in the fat-body does not alter phospholipid balance (Figure S9) and indeed improves HDF on HSD (Figure 7B). While this may appear inconsistent, it is critical to note that over-expression of Pect cDNA using UAS/Gal4 only increases Pect mRNA expression by 7-fold (Figure S6A), whereas HSD causes its upregulation by 250-fold (Figure S6B). Hence, we speculate that an increased ‘basal’ level of Pect such as by that provided by a cDNA over-expression in fat, may be protective to the negative effects of HSD (Figure 7B) without affecting overall phospholipid levels (Figure S9) , but extreme upregulation Pect on HSD affects the PE and LPE balance (Figure 3).”

Reviewer #1 (Significance (Required)):

The work is potentially novel and interesting, but at this stage it's difficult to interpret what the phenotype signifies. Although the manuscript could be revised simply by modifying the text, experimentally addressing the concerns would significantly improve the work.

In sum, we hope we have addressed the key concern for Reviewer #1 as to whether the behavior we report here is indeed a dampening of starvation-induced feeding, or an effect of increase in baseline feeding. We hope that by reviewing our non-normalized data, they can appreciate that it is the former. Also, we hope that Reviewer #1 appreciates that we have strived to address the concerns by additional experiments, to clarify our findings and improve the impact of the work.

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

This intriguing manuscript by Kelly and colleagues uses the fruit fly Drosophila melanogaster as a model to understand how diet-induced obesity alters the feeding response over time. In particular, the authors findings indicate that chronic exposure to a high-sugar diet significantly alters the starvation-induced feeding response. These behavioral studies are complemented by a lipidomics approach that reveals how a chronic high sugar affects many lipid species, including phospholipids. The authors then pursue mechanistic studies that indicate phospholipid metabolism within the fat body appears to remotely affect insulin secretion from the insulin producing cells. Moreover, the changes in phospholipid abundance are associated with changes in insulin-signaling, including increased insulin secretion from the IPCs and elevated levels of FOXO within the nucleus.

I find the study to be potentially very important - the authors combine a longitudinal study that would be difficult in any other model with the powerful genetic tools available in the fly. The conclusions are mostly convincing, but a few follow-up experiments are required:

We are grateful for the reviewers constructive, detail-oriented, and balanced feedback, and their recognition of the value of this study. Now, we have performed additional experiments to address the key concerns raised by all reviewers. We hope that on reading the revised version of our study, that the reviewer continues to feel positive about the message of this study and its potential impact.

1. The key conclusions from the manuscript assume that manipulation of Pect expression levels alters phosphatidylethanolamine (PE) levels. However, the authors make no attempt to verify that the genetic experiments described herein actually affect PE levels. At a minimum, changes in PE levels should be verified for the Pect knockdown and overexpression lines. Similarly, there is no evidence that manipulation of either EAS or Pcyt2 induces the expected metabolic effects. I'm not asking that the longitudinal feeding experiments be repeated, simply that the authors measure the relevant lipid species, preferably with a targeted LC-MS approach.

Prompted by this reviewer, we performed targeted LC-MS on whole adult flies, on normal diet, to assess lipid levels for fat-specific Pect-KD and overexpression. We decided to focus on Pect, as its knock-down even on normal diet causes a dampened hunger-driven feeding behavior (Figure 7A) and phenocopied a 14-day HSD feeding phenotype.

We now present a new dataset in Figure 6. Two striking changes occur:

They are:

Pect-KD shows a significant reduction in specific class of PE 36.2 (Figure 6B). Our data regarding decrease in PE 36.2 agree with a previous lipidomic analyses of Pect mutant retina (PMID: 30737130). It is to be noted that though overall levels of all PE species trend downwards, like the Clandinin lab study on Pect (PMID: 30737130), we did not find a significant change in the overall PC and PE levels.

• Pect-KD shows increase in the phospholipid classes LPC and LPE (Figure 6A). In contrast, LPE is significantly downregulated on HSD Day 14 (Figure 3). On 14-day HSD consistent with extreme upregulation of Pect mRNA fed flies (Figure S6A; Pect mRNA 200-250 fold), PE trends upwards on 14-day HSD (Figure 3) and PE 36.2 trends higher (Figure S7C). We note that on the surface of it PE and LPE per se are contrasting between 14-day HSD lipidome and fat-specifc Pect-KD. But there is a significant commonality that under both states there is an imbalance of phospholipids classes PE and LPE. Hence, we propose that maintaining the compositional balance of phospholipid classes PE and LPE is critical to hunger-driven feeding and insulin sensitivity. Hence, either increase or decrease, of these key phospholipid species, may lead to abnormal hunger-driven feeding.

Finally, fat-specific Pect-OE did not cause significant changes to lipid species (Figure S9). This could either be due to the fact that in fat-specific Pect-OE flies under normal food and that we were assaying whole body lipid levels and not fat-specific lipid changes. But to counter that, even a 60% reduction in Pect mRNA levels (Figure S6A), was sufficient to produce an effect on whole body phospholipid balance (Figure 6). Hence, we speculate that by maintaining a basally higher (7-fold higher Pect mRNA level Figure S6A), might allow 14-day HSD-fed flies to buffer the negative effects of HSD and we predict that it might take longer to disrupt the phospholipid balance and HDF response.

We have now included a section in the discussion - Page 14 Lines 26-34- under the subtitle “The implications of relationship between Pect levels and HSD”. We have pasted an excerpt from that subsection below for this reviewers assessment.

“Also, we note that over-expression of Pect cDNA in the fat-body does not alter phospholipid balance (Figure S9) and indeed improves HDF on HSD (Figure 7B). While this may appear inconsistent, it is critical to note that over-expression of Pect cDNA using UAS/Gal4 only increases Pect mRNA expression by 7-fold (Figure S6A), whereas HSD causes its upregulation by 250-fold (Figure S6B). Hence, we speculate that an increased ‘basal’ level of Pect such as by that provided by a cDNA over-expression in fat, may be protective to the negative effects of HSD (Figure 7B) without affecting overall phospholipid levels (Figure S9), but extreme upregulation Pect on HSD affects the PE and LPE balance (Figure 3).”

A central hypothesis in the study is that the HSD over a period of 14 days results in insulin resistant and that these changes are leading to changes in hunger dependent feeding. I would encourage the authors to determine if Foxo mutants are resistant to these HSD-induced effects on HFD.

We thank the reviewers for this suggestion. However, given that dFOXO nuclear localization rather than expression levels regulate insulin sensitivity, we feel that disrupting dFOXO levels via mutation or knockdown will produce a plethora of indirect effects including developmental abnormalities (PMID: 24778227, PMID: 16179433, PMID: 29180716, PMID: 12893776). Our data suggest that chronic HSD treatment and Pect affect insulin sensitivity in fat tissue. However, we feel that investigating whether insulin sensitivity/FOXO signaling in fat tissue regulates feeding behavior is outside the scope of our work.

1. In lines 25-30, the authors draw the conclusion that an increase in unsaturated fatty acid species is associated with the HSD and that these changes results in a more fluid lipid environment. While I agree with the model, the manuscript contains no evidence to support such a model. Either test the hypothesis or move the last line of the section to the discussion.

We thank the reviewer for this important and insightful comment. We agree that the data we presented and discussed in the original version is at the moment speculative. Addressing the hypothesis that increase in unsaturated fatty acid species result in a more fluid lipid environment will require us to build tools and expertise. Hence, this hypothesis is better suited for exploration in a future study. Given this, we have moved this out of the results section into the Discussion section titled “HSD and fat-specific PECT-KD causes changes to phospholipid profile” (See excerpt below from page 13, lines 24-35).

“In addition to changes in phospholipid classes, we found that HSD caused an increase in the concentration of PE and PC species with double bonds (Figure S4C and S4D). Double bonds create kinks in the lipid bilayer, leading to increased lipid membrane fluidity which impacts vesicle budding, endocytosis, and molecular transport14,92. Hence it is possible that a mechanism by which HSD induces changes to signaling is by altering the membrane biophysical properties, such as by increased fluidity, which would have a significant impact on numerous biological processes including synaptic firing and inter-organ vesicle transport.”

Also, as per the reviewer’s guidance, given that we are speculating here, we have also shifted this dataset from Main figure 4 to supplement S4C and S4D.

In addition, lines 25-30 state that FFAs are increased after 14 days of a HSD. Figure 3A shows the exact opposite - FFAs are significantly decreased in 14 day fed animals despite being elevated in the 7 day fed animals. This is an interesting result that warrants discussion. Moreover, I would encourage to examine the lipidomic data more carefully to ensure that the text accurately portrays the lipid profiles.

We apologize for misstating that FFAs are decreased on 14-day HSD in the lines 25-30. It was an error and we have corrected this. We agree with the reviewer that the reduction of FFA on Day 14-HSD is an intriguing and unexpected observation that needs to be emphasized and further discussed. To this end, we have added figure S4B, wherein we have provided the difference in FFA concentration (by species) after days 7 and 14.

Furthermore, we have discussed what the potential meaning of reduced FFA at Day 14 implies in page 12, lines 19-27 of the Discussion section titled “HSD and fat-specific PECT-KD causes changes to phospholipid profile”. We have stated the following-

“We speculate that this reduction in FFA maybe due to their involvement in TAG biogenesis (PMID: 13843753). We were interested to see if the decrease in FFA correlated to a particular lipid species, as PE and PC are made from DAGs with specific fatty acid chains. However, further analysis of FFAs at the species level did not reveal any distinct patterns. The majority of FFA chains decreased in HSD, including 12.0, 16.0, 16.1, 18.0, 18.1, and 18.2 (Figure S4B). This data was more suggestive of a global decrease in FFA, likely being converted to TAG and DAG, rather than a specific fatty acid chain being depleted.”

The processed lipidomics data should also be included as supplementary data table so that they can be independently analyzed by the reader.

We thank the reviewer for this suggestion. As per the reviewers request, we have included the raw data as an attachment in our supplementary material (Supplementary Files 1-3.), so that interested readers can use the datasets generated in this study for future work and further analysis.

Beyond these experimental suggestions, the manuscript needs significant editing for clarity. While I won't provide a comprehensive list, the authors need to provide accurate descriptions and annotation of genotypes (including w[1118], which is written as W1118), typos, and formatting. I've listed a few examples below:

1. Page 3, Line 1 and 2: "...have been shown to impact feeding behavior and metabolism that leads to..." This is an awkward and grammatically incorrect sentence.
2. Page 3, Lines 7-32 is one very large paragraph but contains concepts that should be broken down over at least three paragraphs.
3. Page 3, Line 25: A description of the reaction catalyzed by Pect would be helpful for a manuscript focused on Pecte activity.
4. Page 4, Line 10: "previously characterized method of eliciting diet induced feeding behavior." As stated in the text, the method is previously described yet the manuscript characterizing the method isn't cited.
5. Figure legend 3 contains a random assortment of capitalized lipid species. Also, the names of lipid species are inappropriately broken into multiple names. Please use correct nomenclature throughout the manuscript.

The list above is nowhere near comprehensive. The manuscript requires significant editing.

We are grateful to the reviewer for drawing our attention to these errors. We have made significant edits to the revised manuscript to address the above-mentioned concerns, as well as made additional textual changes throughout and copyedited it. We hope that the reviewer will find the manuscript reads better and the clarity and preciseness is significantly improved.

Reviewer #2 (Significance (Required)):

I find the study to be potentially very important - the authors combine a longitudinal study that would be difficult in any other model with the powerful genetic tools available in the fly. The findings will significantly advance our understanding of how lipid metabolism links dietary nutrition with feeding behavior.

Once again, we are grateful for this reviewer’s thoughtful critique and encouraging words regarding our work and its potential impact.

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

Summary: This manuscript uses Drosophila to investigate how diet-induced obesity and the changes in the lipid metabolism of the fat boy modulate hunger-driven feeding (HDF) response. The authors first demonstrate that chronic exposure (14 days) of high sugar diet (HSD) suppresses HDF response. Through lipidome analysis, the authors identify a specific class of lipids to be elevated upon chronic HSD feeding. This coincided with the changes in expression of Pect, an enzyme that regulates the biosynthesis of these lipids. Modulating the expression of Pect specifically in the fat body affected HDF response.

We thank this reviewer for their rigorous and thoughtful critique and for identifying a key issue with our original study pertaining to a gap in how Pect mRNA levels on 14-day HSD are elevated but the Pect-KD phenocopies the HDF. Now by performing whole-body adult fly lipidomic on fat-specific Pect-KD we have resolved this issue and provided clarity on role of Pect in maintaining phospholipid homeostasis and thus subsequently impacts hunger-driven feeding. We hope the reviewer finds that the revised manuscript provides further clarity to the functional link between Pect’s role in fat-body and hunger-driven feeding.

Major comments: The author claim that the HDF response in HSD is distinct between early (5d, 7d) and chronic (day 14) HSD feeding. However, the data seem to indicate that HDF response is significantly decreased at all time points in HSD. For example, at day 5 HDF response was increased only 3-fold in HSD (Figure 1C) compared to around 50-fold increase in NF (Figure 1B). The scale of the Y-axis in Figure 1B and 1C is an order of magnitude different. Including the starved data (NFstv and HSDstv) in Figure S1, normalized to NF fed group, would better visualize the overall trends. Related to this, having the source data for the actual number of feeding events would be useful (e.g., to see the baseline changes in feeding in different time points in Figure 1 and the effect of genetic manipulations in Figure 7).

As per the reviewers request, we now have modified our graphs to show source data (Figure S1) and show the raw feeding events.

Then in the non-normalized graphs we plot, over a longitudinal time course, baseline and hunger-driven feeding events (Figure 1B-D). We also show that HSD fed flies do not display increased baseline feeding (Figure 1D) suggesting that the effect we see on HDF are no clouded by increased baseline feeding.

Yes, the reviewer makes an important point that HDF response on HSD fed flies is of a lower magnitude than NF fed flies. We think that is a biologically meaningful observation, as it suggests that flies have a remarkably fine-tuned ability to coordinate food-intake with nutrient store levels.

­­Now we have included a paragraph in the Discussion, Page 11 Lines 23-27, that say the following to ensure the readers appreciate this salient point raised by this reviewer.

*It is to be noted that the HDF response of HSD-fed flies (Figure 1C, Days 3-10) is of lower order of magnitude than the NF-fed flies. This suggests that that in addition to sensing an energy deficit and mobilizing fat stores (Figure 1F, 1G, S1), HSD fed flies calibrate their starvation-induced feeding to compensate only for the lost amount of fat. Overall, this suggests that flies have a remarkably fine-tuned ability to coordinate food-intake with nutrient store levels. *

The association between fat body Pect level and phospholipid levels is not clear. Day 14 of HSD feeding shows high expression of Pect in the fat body and elevated levels of PC32.0 and PC32.2. The authors assume the high expression of Pect in the fat body is due to the compensatory response, but there are no data indicating downregulation of Pect levels at the earlier time points of HSD feeding. A previous study demonstrated that Pect mutant flies have lower levels of PC32.0 but higher PC32.2 (PMID: 30737130).

We agree that one puzzling aspect of the original version of this study was that Pect mRNA levels being very high on Day 14 HSD, but nonetheless the effects of Pect-KD phenocopied HSD. To resolve this, prompted by Reviewer #2 and #3 concerns, for this revised version we have now performed lipidomic analyses on whole adult flies, when Pect is knocked down (KD) by RNAi in the fat tissue. We now present a new dataset in Figure 6. Two striking changes occu. They are:

1. Pect-KD shows increase in the phospholipid classes LPC and LPE (Figure 6A). In contrast, LPE is significantly downregulated on HSD Day 14 (Figure 3).
2. Pect-KD shows a significant reduction in specific class of PE 36.2 (Figure 6B). Our data regarding increase in PE 36.2 agree with a previous lipidomic analyses of Pect mutant retina (PMID: 30737130). In contrast, PE 36.2 trends upwards on 14 day HSD (Figure S7C) though not significantly. On 14-day HSD consistent with extreme upregulation of Pect mRNA fed flies (Figure S6A; Pect mRNA 200-250 fold), PE trends upwards on 14-day HSD (Figure 3) and PE 36.2 trends higher (Figure S7C). We note that on the surface of it PE and LPE per se are contrasting between 14-day HSD lipidome and fat-specifc Pect-KD. But there is a significant commonality that under both states there is an imbalance of phospholipids classes PE and LPE. Hence, we propose that maintaining the compositional balance of phospholipid classes PE and LPE is critical to hunger-driven feeding and insulin sensitivity. Hence, either increase or decrease, of these key phospholipid species, may lead to abnormal hunger-driven feeding.

On day 14, HDF response was increased 70-fold in w1118 flies in NF (Figure 1B; w1118), but only 2.5-fold in lpp>LucRNAi control flies in NF (Figure 7A). This suggests that lpp-gal4 driver lines have a significant effect on HDF response. Using a different fat-body specific Gal4 line would be necessary to validate conclusions.

Regards reduced HDF magnitude, in our experience using UAS-Gal4 reduces HDF response magnitude consistently and cannot be compared to w1118 which is more robust. To account for background differences, we use Uas-Gal4 with control RNAi. It clearly shows differences in HDF response on starvation, but Pect and Pisd RNAi does not (Figure 7A). Hence, given that this experiment internally controls for any changes in HDF response for UAS-Gal4>RNAi, we conclude that HDF response in disrupted in Pect and PISD KD (Figure 7).

We only presented the Lpp-driver in our study, as this driver is the only fat-specific driver that has no leaky expression in other tissues, and is specific to fat as apolpp promoter used to generate this Gal4 line is only expressed in fat tissue (Eaton and colleagues, PMID: 22844248). Other widely used fat-specific drivers, including the pumpless-Gal4 (ppl-Gal4) driver has leaky expression in gut or other tissues (See Table 2 of this detailed study by Dr. Drummond- Barbosa https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7642949/). If the reviewer is aware of a fat-specific Gal4 line, other than Lpp-Gal4, which has a highly specific expression in the fat tissue without leaky expression in other tissues, then we are happy to take onboard the reviewer’s suggestion and try that fat-specific Gal4 that they suggest.

HSD feeding promotes Pect expression (Figure S3C) and global changes in phospholipid levels (Figure 3, 4). Therefore, shouldn't Pect overexpression (not Pect RNAi) in a normal diet mimic HSD feeding state and promote loss of HDF response? Conversely shouldn't knockdown of Pect in HSD rescue loss of HDF response?

We agree that a puzzling aspect is that Pect mRNA levels are significantly elevated in HSD Day-14, but Pect-KD showed displays the inappropriate HDF response. As we have described in our response to this reviewer on Page 19, we believe that Pect-KD and HSD disrupt PE and LPE balance overall but in different ways. Whereas Pect-OE using cDNA expression in fat body does not cause a significant change to any lipid class (Figure S9), and our results suggest that basally higher level of PECT is likely to be protective on HSD with respect to HDF(Figure 7B).

To ensure that we appropriately discuss and clarify this issue, we have now included a section in the discussion - Page 14 Lines 26-33- under the subtitle “The implications of relationship between Pect levels and HSD”. We have pasted an excerpt from that subsection below for this reviewers assessment.

“Also, we note that over-expression of Pect cDNA in the fat-body does not alter phospholipid balance (Figure S9) and indeed improves HDF on HSD (Figure 7B). While this may appear inconsistent, it is critical to note that over-expression of Pect cDNA using UAS/Gal4 only increases Pect mRNA expression by 7-fold (Figure S6A), whereas HSD causes its upregulation by 250-fold (Figure S6B). Hence, we speculate that an increased ‘basal’ level of Pect such as by that provided by a cDNA over-expression in fat, may be protective to the negative effects of HSD (Figure 7B) without affecting overall phospholipid levels (Figure S9) , but extreme upregulation Pect on HSD affects the PE and LPE balance (Figure 3).”

We would have liked to test Pect protein expression on HSD, but since we were unable to access antibodies for Pect published in a prior study (PMID: 33064773) from Dr. Wang’s lab (see Page 10-11, of response to Reviewer #1). Hence, we were unable to test how the proteins levels of Pect correlate with the 250-fold increase mRNA expression.

In conclusion, we hope the reviewer appreciates that our results regarding Pect function are consistent with the main conclusion that achieving the right phospholipid balance between PE and LPE, is critical for an organism to display an appropriate HDF response.

Minor comments: All graphs should plot individual data points and showed as box and whisker plot as much as possible.

Thanks for this suggestion, we have added individual data points to the vast majority of figures in the paper. We have made exceptions to graphs such as seen in figure 1 and FigureS4B-D where we find individual data points add an unnecessary layer of complexity. We hope these changes provide additional clarity and strength to the claims made in this manuscript.

Data for day 14 missing in Figure S4A and S4B.

We have provided Day 14 for the PC composition and PE composition, due to changes in Figures, they are now S7A and S7B.

Reviewer #3 (Significance (Required)):

The interactions between diet-induced obesity, peripheral tissue homeostasis and feeding behavior is an interesting topic that can be addressed using Drosophila. This manuscript demonstrates how fat body Pect levels affect HSD induced changes in hunger-driven feeding response. However, at this point, the functional association between fat body Pect level, global phospholipid level, and loss of hunger-driven feeding response in chronic HSD feeding is not clear.

We hope the revised data, and discussion of the paper, provides well-substantiated functional association on the importance of maintaining phospholipid balance, driven by Pect enzyme, as a critical regulator of hunger-driven feeding behavior. As stated in the revised discussion, the key take home message of our manuscript is that on prolonged HSD exposure PC, PE and LPE levels are dysregulated, the loss of phospholipid homeostasis coincided with a loss of hunger-driven feeding. Following this lead on phospholipid imbalance, we then uncovered a critical requirement for the activity of the rate-limiting PE enzyme PECT within the fat tissue in controlling hunger-driven feeding.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript uses Drosophila to investigate how diet-induced obesity and the changes in the lipid metabolism of the fat boy modulate hunger-driven feeding (HDF) response. The authors first demonstrate that chronic exposure (14 days) of high sugar diet (HSD) suppresses HDF response. Through lipidome analysis, the authors identify a specific class of lipids to be elevated upon chronic HSD feeding. This coincided with the changes in expression of PECT, an enzyme that regulates the biosynthesis of these lipids. Modulating the expression of PECT specifically in the fat body affected HDF response.

Major comments:

The author claim that the HDF response in HSD is distinct between early (5d, 7d) and chronic (day 14) HSD feeding. However, the data seem to indicate that HDF response is significantly decreased at all time points in HSD. For example, at day 5 HDF response was increased only 3-fold in HSD (Figure 1C) compared to around 50-fold increase in NF (Figure 1B). The scale of the Y-axis in Figure 1B and 1C is an order of magnitude different. Including the starved data (NFstv and HSDstv) in Figure S1, normalized to NF fed group, would better visualize the overall trends. Related to this, having the source data for the actual number of feeding events would be useful (e.g., to see the baseline changes in feeding in different time points in Figure 1 and the effect of genetic manipulations in Figure 7).

The association between fat body PECT level and phospholipid levels is not clear. Day 14 of HSD feeding shows high expression of pect in the fat body and elevated levels of PC32.0 and PC32.2. The authors assume the high expression of pect in the fat body is due to the compensatory response, but there are no data indicating downregulation of pect levels at the earlier time points of HSD feeding. A previous study demonstrated that pect mutant flies have lower levels of PC32.0 but higher PC32.2 (PMID: 30737130). To better understand the link the authors should knockdown/OE PECT specifically in the fat body and assess changes in phospholipids.

On day 14, HDF response was increased 70-fold in w1118 flies in NF (Figure 1B; w1118), but only 2.5-fold in lpp>LucRNAi control flies in NF (Figure 7A). This suggests that lpp-gal4 driver lines have a significant effect on HDF response. Using a different fat-body specific Gal4 line would be necessary to validate conclusions.

HSD feeding promotes PECT expression (Figure S3C) and global changes in phospholipid levels (Figure 3, 4). Therefore, shouldn't PECT overexpression (not PECT RNAi) in a normal diet mimic HSD feeding state and promote loss of HDF response? Conversely shouldn't knockdown of PECT in HSD rescue loss of HDF response?

Minor comments:

All graphs should plot individual data points and showed as box and whisker plot as much as possible. Data for day 14 missing in Figure S4A and S4B.

Significance

The interactions between diet-induced obesity, peripheral tissue homeostasis and feeding behavior is an interesting topic that can be addressed using Drosophila. This manuscript demonstrates how fat body PECT levels affect HSD induced changes in hunger-driven feeding response. However, at this point, the functional association between fat body PETC level, global phospholipid level, and loss of hunger-driven feeding response in chronic HSD feeding is not clear.

Referees cross-commenting

I agree with all the reviwers points; potentially very interesting, but requires a significant amount of work.

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Referee #2

Evidence, reproducibility and clarity

This intriguing manuscript by Kelly and colleagues uses the fruit fly Drosophila melanogaster as a model to understand how diet-induced obesity alters the feeding response over time. In particular, the authors findings indicate that chronic exposure to a high-sugar diet significantly alters the starvation-induced feeding response. These behavioral studies are complemented by a lipidomics approach that reveals how a chronic high sugar affects many lipid species, including phospholipids. The authors then pursue mechanistic studies that indicate phospholipid metabolism within the fat body appears to remotely affect insulin secretion from the insulin producing cells. Moreover, the changes in phospholipid abundance are associated with changes in insulin-signaling, including increased insulin secretion from the IPCs and elevated levels of FOXO within the nucleus.

I find the study to be potentially very important - the authors combine a longitudinal study that would be difficult in any other model with the powerful genetic tools available in the fly. The conclusions are mostly convincing, but a few follow-up experiments are required:

1. The key conclusions from the manuscript assume that manipulation of PECT expression levels alters phosphatidylethanolamine (PE) levels. However, the authors make no attempt to verify that the genetic experiments described herein actually affect PE levels. At a minimum, changes in PE levels should be verified for the PECT knockdown and overexpression lines. Similarly, there is no evidence that manipulation of either EAS or Pcyt2 induces the expected metabolic effects. I'm not asking that the longitudinal feeding experiments be repeated, simply that the authors measure the relevant lipid species, preferably with a targeted LC-MS approach.
2. A central hypothesis in the study is that the HSD over a period of 14 days results in insulin resistant and that these changes are leading to changes in hunger dependent feeding. I would encourage the authors to determine if Foxo mutants are resistant to these HSD-induced effects on HFD.
3. In lines 25-30, the authors draw the conclusion that an increase in unsaturated fatty acid species is associated with the HSD and that these changes results in a more fluid lipid environment. While I agree with the model, the manuscript contains no evidence to support such a model. Either test the hypothesis or move the last line of the section to the discussion.

In addition, lines 25-30 state that FFAs are increased after 14 days of a HSD. Figure 3A shows the exact opposite - FFAs are significantly decreased in 14 day fed animals despite being elevated in the 7 day fed animals. This is an interesting result that warrants discussion. Moreover, I would encourage to examine the lipidomic data more carefully to ensure that the text accurately portrays the lipid profiles.

The processed lipidomics data should also be included as supplementary data table so that they can be independently analyzed by the reader.

Beyond these experimental suggestions, the manuscript needs significant editing for clarity. While I won't provide a comprehensive list, the authors need to provide accurate descriptions and annotation of genotypes (including w[1118], which is written as W1118), typos, and formatting. I've listed a few examples below:

1. Page 3, Line 1 and 2: "...have been shown to impact feeding behavior and metabolism that leads to..." This is an awkward and grammatically incorrect sentence.
2. Page 3, Lines 7-32 is one very large paragraph but contains concepts that should be broken down over at least three paragraphs.
3. Page 3, Line 25: A description of the reaction catalyzed by PECT would be helpful for a manuscript focused on PECT activity.
4. Page 4, Line 10: "previously characterized method of eliciting diet induced feeding behavior." As stated in the text, the method is previously described yet the manuscript characterizing the method isn't cited.
5. Figure legend 3 contains a random assortment of capitalized lipid species. Also, the names of lipid species are inappropriately broken into multiple names. Please use correct nomenclature throughout the manuscript.

The list above is nowhere near comprehensive. The manuscript requires significant editing.

Significance

I find the study to be potentially very important - the authors combine a longitudinal study that would be difficult in any other model with the powerful genetic tools available in the fly. The findings will significantly advance our understanding of how lipid metabolism links dietary nutrition with feeding behavior.

Referees cross-commenting

I agree. We all think the manuscript is potentially interesting and important, but requires further experimentation. I agree with all concerns raised by the other reviewers. A revision would likely represent a significant amount of work.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Kelly et al. show that the difference between the feeding behavior of fed and starved flies (hunger-driven feeding; HDF) is absent in animals fed a high-sugar diet (HSD) for two weeks or more. The disappearance of HDF with HSD coincides with changes in phospholipid profiles caused by HSD. Furthermore, RNAi-mediated downregulation of PECT in the fat body-a key enzyme in the PE biosynthesis pathway-phenocopies physiological effects of HSD. Moreover, downregulation or overexpression in the fat body abolishes or induces HDF, respectively, abolishes or induces HDF, respectively, independent of HSD treatment.

Overall, the manuscript is well-written and the phenotypes are clear. However, I have major concerns regarding the authors' interpretation of the data and their conclusion. Most importantly, while it is clear that the authors' high-sugar dietary treatment affects feeding behavior and physiology, I am not convinced that the changes can be considered "hunger-driven"-which is central to the main point of the manuscript. Therefore, it is my recommendation that the authors substantially revise the manuscript by either showing additional/re-analyzed data that rule out alternative hypotheses, or rewriting the manuscript keeping alternative interpretations in mind.

Major comments:

1. The data do not sufficiently show that the long-term HSD regime disrupts "hunger-sensing." The manuscript should address alternative hypotheses by showing raw instead of normalized data, rewriting the manuscript with a new central conclusion, or running additional experiments that actually show a defect in hunger-driven response.
   • a. The main results that the authors rely on for the argument is that the ratio of feeding events that the starved and non-starved flies eat is different between the groups fed normal or HSD. However, because the authors only show normalized data (normalized to non-starved flies; Fig. 1), it is difficult to tell whether the change is due to a chronically increased feeding in non-starved HSD flies-maybe in perpetual hunger-like allostasis-or dampened starvation response. Indeed, the data shown in Fig S1 show that flies fed HSD for as short as 5 days show more frequent feeding events compared to age-matched controls fed normal food. It is possible that because the HSD-fed flies eat more than NF-fed flies, even without being starved, the ratio of starved/non-starved feeding is lower in the HSD-fed group-due to changes in the denominator, rather than the numerator.
   • b. It is also possible that the HSD-fed flies are simply not in as big an energy deficit physiologically, due to the increased fat deposits they've accumulated (as the authors show later in the manuscript). It may take longer for the fat HSD flies to reach substantial energy deficiency than the NF flies, but they still may eventually be able to appropriately respond to hunger, just like NF flies. In such case, it would be a misnomer to call this behavioral change a 'defect in hunger-driven feeding behavior.' Maybe an experiment with a dose-response curve of "hunger driven feeding response" as a function of duration of starvation would help?
2. How can you be sure that lower Dilp5 immunofluorescence is indicative of increased Dilp5 secretion? Wouldn't decreased production of dilp5 also have the same results?
   • a. Also, the authors should state in the main text that it is Dilp5, not just any Dilp.
3. Data presentation:
   • a. Sometimes the data are normalized to NF (Fig 4B-C), sometimes not (ex. Fig 4A, S4C). Unless there is a specific rationale for the data transformation, it would be more appropriate to show untransformed data (ex. Fig 4A, S4C), especially as the authors use two-way ANOVA to determine significance. Only showing the differences implies comparison against a hypothetical mean (i.e. μ0=0), not between two group means.
   • b. Some figures show both individual data points and summary statistics (mean, SD, ... ex. Fig 2A)-which I believe is ideal-but some show only one or the other (ex. Fig 2B, no summary statistics; Fig. 3, no data points. The manuscript would read more convincing if data visualization is consistent across figures.

Minor comments:

1. High sugar diet: what is the actual sugar concentration in the NF v. HSD diets? The authors write that the HSD diet contains "30% more sugar" than the NF, but providing the final sugar concentrations-sucrose or others-would be informative for other scientists studying the effect of high sugar diets.
   • a. Additionally, the definition of HSD is inconsistent. Main text (Page 5, line 17) states that their HSD is "60% more sugar than normal media," whereas the figure legend (Fig 1) and the Methods state that the HSD contains "30% more sugar."
2. Starvation medium: please provide justification for why the authors used 1% sucrose/agar for starvation medium, instead of plain agar/water that most labs use. At least clarify and provide a reference for the claim that the 1% sucrose/agar "is a minimal food media to elicit a starvation response."
3. PECT mRNA level is higher with HSD. This is surprising because not only, as authors mention, is increased PC32.2 with HSD suggests lower PECT activity, but also because PECT RNAi phenocopies long-term HSD in HDF behavior, lipid morphology, FOXO accumulation in fat body. The authors speculate that the data "likely shown an upregulation in an attempt to mediate the PECT dysregulation occurring at the protein level." If that were true, a western blot may be informative. Zhao and Wang (2020, PLoS Genetics) generated a PECT antibody that seems compatible with western blot applications. That being said, I don't think such data is critical for the manuscript. I mention this simply as a suggestion for the authors.
   • a. page 8, line 22-23, did you mean to write "Given how PC32.2 is elevated after 14 days of exposure to HSD, we assumed that PECT levels would be low for flies under HSD," not "high?" Otherwise the subsequent 2 sentences don't make sense.

Significance

The work is potentially novel and interesting, but at this stage it's difficult to interpret what the phenotype signifies. Although the manuscript could be revised simply by modifying the text, experimentally addressing the concerns would significantly improve the work.

The co-reviewer and I have expertise in Drosophila neurobiology and behavior.

Referees cross-commenting

Hi all, although the reviews hit upon some overlapping, but mostly different points, I agree with all of the concerns raised. There's some really interesting stuff here but some of the results, as presented, don't make sense. It's possible this will be clarified by revising the text, although I suspect it's more likely that the authors will have to add a number of the experimental suggestions made by the reviewers.

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Reply to the reviewers

Reviewer 1

Summary: The authors used conventional confocal and super-resolution STED microscopy to characterize the actin filament network in response to SARS-CoV-2 infection in pulmonary cells. They demonstrate that, although total levels of actin are unchanged, F-actin polymerization increases upon infection, with the most significant changes occurring at 48 hours post infection. Notably, F-actin remodels from primarily stress-fiber architectures to circularized, F-actin nanostructures that tend to colocalize with viral M cluster rings at 48 hours post infection. Additionally, there is a significant increase in F-actin-associated filopodia-like structures, with an example of a possible cell-to-cell filopodia that could possibly be a mode of inter-cellular viral transmission. The authors complement their imaging-based experiments with RNAseq to profile the cellular gene expression of SARS-CoV-2 infected pulmonary cells, revealing an upregulation of RHO GTPases activate PKNs and alpha-actinins. They show that treatment of pulmonary cells with Rho/SFR and PKN inhibitors during infection decreases the size of viral M clusters and release to comparable levels as the known viral therapeutic, Remdesivir.

Major comments:

1. The majority of the author's conclusions are based off of qualitative and quantitative analysis of their fluorescence images. While they do mention briefly an ImageJ plug-in and the statistical tests performed, the description of their quantitative image-based analyses for each experiment is lacking. For example, how was viral M cluster and actin intensity measured? How was the signal intensity normalized to account for variations in antibody labeling or other cell-to-cell variations? For figures 3C&D, how did the authors calculate viral and actin ring diameter? It is necessary to expand on the details of the quantitative analysis for each parameter mentioned in the methods section and/or include a figure panel demonstrating the details of the analysis (similar to what is nicely displayed for M cluster size in Figure S1B). Response:

We would like to thank reviewer suggestions to improve the material and methods section. We have incorporated all the suggested details for image analysis and also schematic where ever it is necessary in the figures and SI figures in the revised manuscript to clarify:

• viral M cluster measurement (Figure S1A) ; no variation in M antibody labelling or in cells was observed per se. the pic of infection regarding M clusters was always 48h pi (maximum of M clusters intensity and area.
• F-actin intensity was considered for each cells, labelling cells with Phalloidin (for at least 30 cells in each condition), imaging z-stack and then considering the whole F-actin content for each cell.
• Intracellular viral and F-actin ring diameter was calculating using the scale bar on 3D STED images using ImagJ.

In particular, the details regarding the F-actin orientation measurements is lacking. Is there a consistent reference point for the orientation of the actin filaments? When comparing across two different cells, it is unclear how the orientations are normalized. Perhaps it would be more informative to plot the difference or the range in angles? Or the distribution of the differences in angles? Another point that is a bit misleading is describing this analysis as "F-actin orientation" since the term "orientation" can has a specific meaning for polar filaments such as actin. For example, given resolution limitations of the imaging approaches used in this manuscript, the authors are reporting on the orientations of bundles/populations of actins and not orientations of individual filaments relative to one another within the bundle (e.g. anti-parallel vs parallel vs branched). The authors should clarify this in the text and also further expand on the utility of their F-actin orientation analysis and how it informs us on the mechanisms of actin-mediated viral infection.

Response:

To quantify F-actin rearrangements, we have analyzed the orientation angle of actin nano-fibers from STED images (as in Nature Communications. 8 (2017), doi:10.1038/ncomms14347).

For this analysis all the images were imaged with STED 2D microscopy for better resolution (axial 60 nm resolution). From STED 2D microscopy images of F-actin, the orientation angle of nano-fibers were evaluated based on the structure tensor of each nano-fibers compares to its local neighborhood using the Java plugin for ImageJ “OrientationJ”. From the given images, the OrientationJ plugin computes the structure tensor for each pixel in the image by sliding the Gaussian analysis window over the entire image. The local angle of orientation properties encoded in color and it is also generating a distribution of angles for each nano-fibers for a given image. Here, in the STED images, it is considered the vertically elongated nano-fibers as the major orientation angle (as around +90 Deg and – 90 Deg from the cell edge) and others orientation angles were calculated accordingly. Area are normalized to the distribution curve of angles to compare the changes in distribution for infected and non-infected cell (as in Fig. 3B).

We have incorporated above explanations in the material and method section (Image analysis section, Page 11) in the revised manuscript.

For the majority of figures and findings, they report that between "22

Response:

We have incorporated the exact number of cells analyzed for each condition and details about data sets used for analysis in each figure legend in the revised manuscript.

The actin filament network can assemble into different architectures that are dependent on subcellular location. For example, actin at the basal region of the cell closest to the coverslip often assembles into stress fibers, whereas the cortical actin network often forms astral, highly branched networks. It would be important to take this into account when comparing across different cellular conditions. It is unclear if the authors were consistent with the z-slice examined for the different cellular treatment/infection conditions. Were the analyses performed on individual z-stacks or max projection images?

Response:

We agree with the reviewer views on actin network in different planes. Thus, to ensure reasonable quantification and comparison among conditions, all images were taken with the same objective (63x oil N 1.4) and microscope settings (same gain, same laser power). For post-processing, we mainly choose individual cells, which are not in contact with others and individual z-stacks were taken. Z-stacks images with fixed 0.3 micrometer slices for each cells were taken to ensure the whole cell was in focus. The Z-projection images of individual cells were then performed and used to calculate the F-actin or viral M cluster or ER mean intensity in the whole cell. We have analyzed the mean intensity per individual cell using a Fiji/Image J.

We have incorporated above details in material method (image analysis) section in the revised manuscript.

Since a major impact of this paper is the first imaging-based characterization of actin filament assembly in response to infection, the authors should provide a more comprehensive display of the raw data images. For example, figure S2 provides a nice gallery of images of actin and viral M particles, however it should show separate image channels in gray scales and consistent scaling across all images. Furthermore, all figure panels showing distinct imaging experiments and quantitative results should be complemented with a supplemental figure showing a gallery of images. This would apply to actin nanostructure rings (Figure 3C/E), filopodia and cell-to-cell contacts (Figure 4A/D), treatment with remdesivir/PKN inihibitor (Figure 6B), and ER localization of M particles (Figure S5).

Response:

As the reviewer suggested, we have now created an image gallery for each figure panel (Figures 3, 4, 6 and S5, S3, S8, S9) including STED images that were added as supplemental figures.

The results in Figure 3D are difficult to interpret. The images should be larger and labeled. Also, based on the 3D STED image in Figure 3D, it appears that the brightest actin signal is actually at the center portion of the viral M cluster. Does this contradict the TEM image and what is described in the text? For Figure 3E: a more relevant analysis might be line scans across multiple images showing how relative actin-M cluster intensity varies within the dimensions of the nanostructure to demonstrate more clearly a pattern of ring assembly of both M clusters and actin.

Response:

Since the virus “rings” were mostly found in intracellular places, far from membrane surface, some times during imaging we observed F-actin signal from the upper plane, which is possibly the reason for brightest F-actin signal appears at the center portion of the viral M cluster. Thus, for better clarity of the image and to support our statements we have now incorporated other new images in the Figure 3E (STED 3D images) showing that an heterogeneity of the F-actin labelling but strongly associated with intracellular viral M clusters.

The authors should address the implications and significance of the described cellular morphological changes in the context of the more physiologically relevant tissue/organ system. How do the changes they observe upon infection in isolated cultured cells compare to when these cells are assembled into tissue/organs?

Response:

The significance of the cellular morphological changes upon SARS-CoV2 infection showing a contraction-like effect on the cells as well as higher cells and less contact area could account in a pulmonary tissue by the destructuration of the lung tissue, consistent with the lung damaged seen in the case of COVID19. A sentence in that sense was added in the Discussion section.

For Figure 6 and S5, the authors infected and treated cells with an inhibitor at the same time point and demonstrate that M cluster size and release is reduced to somewhat comparable levels as treatment with Remdesivir. The authors should expand their analyses for this experiment to include the other quantitative parameters outlined in the paper: F actin/M cluster nanostructures, cellular morphology, filopodia formation, orientation of actin, etc. Additionally, it would be more informative to treat cells post-infection to more closely mimic cellular conditions of infection/treatment.

Response:

We have now included quantitative analysis for cellular morphological changes of cells with or without drug treatment (both in the presence of PKN inhibitor and Remdesivir upon SARS-CoV-2 infection) in the revised manuscript (Supplemental Figure S7). We observed a restoration of F-actin nanostructures as well as did not observe any filopodia-like structure formation upon treatment with PKN inhibitor in infected cells.

Minor comments:

1. The individual data points should be overlaid on the violin plots for better interpretability of the variability in the data. Response:

We have incorporated new violin plots with overlaid data points in the revised version of the manuscript for each figure with quantitative data (Figures 1,2,5,6).

For Figure 3E: the images look "stretched" with an altered relative aspect ratio.

Response:

For sake of clarity, we have incorporated new (better) 3D STED images for a better visualization of intracellular F-actin/M clusters “rings” in revised manuscripts (Figure 3E).

1. The authors should include a cartoon model figure highlighting both (1) how their results contribute to our knowledge of actin-mediated viral assembly/replication and (2) unknown portions of the pathway that need to be further probed to better understand the mechanistic underpinnings of this process.

Response:

We have now included a model scheme figure summarizing our results in the revised manuscript, as a new figure 7.

There have been several high resolution cellular imaging studies using other complementary 3D volumetric imaging approaches (e.g. cryo-electron tomography and FIB/SEM) to characterize the subcellular ultrastructure’s of SARS-CoV-2 infection. The authors should include a brief discussion on how their study complement or compare to these reports, in particular noting whether or not actin filament assemblies were observed in these data.

Response:

Thanks to the reviewers for this very pertinent remark, we have added in the Discussion (Page 7,8), a section commenting previous high-resolution cellular imaging studies (REFERENCES: Mendonçà et al Nature Comm 12, 4629, 2021; Klein et al 2020) comparing our 2D/3D STED imaging with complementary 3D EM or 3D cryo-ET or FIB/SEM of SARS-CoV-2 infected cells recently published.

From Mendonca et al 2021, one can see some intracellular dense structure underneath the CoV-2 budding membrane area, but not able to see if F-actin filaments were present or not. It would be difficult to observe because the vRNP underneath the Spike decorating membrane are very dense. The study was focus on viral assembly and egress using cryo-ET/FIB but not on F-actin filament per se. We don’t know if their imaging conditions would preserve F-actin fibers on membranes. On the other side, when studying virus egress, then we can clearly see CoV-2 individual particles surfing on giant filopodia-like structures very much resembling our STED imaging of viruses on filopodia 48h pi. We can clearly see and recognize parallel F-actin filament bundles inside the enlarged filopodia (Figure 5 D/E) with viruses on it.

Same results were observed using Cryo-EM tomography in another study (Klein et al 2020) where one can see viruses on filopodia for many cell types A549-hACE2, VeroE6, Calu3 infected cells.

Reviewer 2

The authors investigate the role of F-actin in infected human pulmonary alveolar A549-hACE2 cells. They investigate infection progression at different time points by the detection of the M protein by confocal microscopy and western blot. They compare the detection of M with S and N in western blot and with viral RNA detection by Q-PCR. The authors correlate M cluster formation to peak at 48h p.i. with particle assembly and particle release at 72h p.i. An increase in F-actin at 24h and 48h p.i. was monitored by confocal microscopy and z-stacks, whereas the overall amount of actin determined by western blot was not changed. Using 2D STED microscopy the authors identified F-actin rearrangement from stress fibers to filamentous protrusions at 24h-48h p.i. and conclude importance for particle assembly and release. By 3D STED microscopy M labeled intracellular organelles called "viral rings" surrounded by actin called "actin rings" are shown. By transmission electron microscopy (TEM) vesicular structures with budding particles were shown at intracellular membranes. The authors conclude from these findings that F-actin stabilizes assembly platforms at membranes or support the transport of virus loaded vesicles to the plasma membrane. The authors found more and longer filopodia in infected cells which were loaded with virus particles bridging cells suggesting role in cell-cell spread. At the plasma membrane they found bigger particles and at the filopodia smaller, suggesting release from the plasma membrane in packages.

Transcriptom analysis of non infected and SARS-CoV-2 infected A549-hACE2 revealed upregulation of Rho-GTPases activated proteins like PKN and α-actinins upon infection. The levels of α-actinins in WB were 2-fold higher in infected cells. The authors show that inhibitors of Rho/SRF and PKN restored cell morphology, reduced M cluster formation and virus release. The PKN inhibitor blocked M in the ER. The authors conclude from this data a role of the alpha-actinins superfamily in SARS-CoV-2 assembly and egress.

Major comments:

The presented data are convincing but some figures may need improvements, see in minor comments. For some conclusions, more evidences like marker staining may be needed.

Response:

In accordance with the reviewer, we have significantly improve the figures in the revised manuscript. We identified that the intracellular compartment containing budding viruses were derived from the ER (gpr78 marker) – shown in revised Figure 6 - and not in lysosomes (Lamp1 marker) or extracellular vesicles (CD81 marker) – See new supplemental revised Figure S10. We have included all the new results and discussion in revised manuscripts.

Minor comments:

The authors conclude that F-actin stabilizes assembly platforms at membranes like ERGIC, but an ERGIC marker staining is not provided. The authors suggest that F-actin might also be involved in transport of virus loaded vesicles to the plasma membrane. Here a plasma membrane marker or native staining of particles may help to descriminate between intracellular Exosomes and extracellular particles. Co-staining with exosomal markers would also be more convincing.

Response:

Also as per reviewer suggestion we have identified that the intracellular compartment containing budding viruses were derived from the ER (gpr78 marker) – shown in revised Figure 6, Fig. S8. New quantitative analysis (including with PKN inhibitor) to support the data also included in the figures. Also we have used lysosomes marker LAMP1 and extracellular vesicles (EV) marker CD81 and we found that there was no colocalization with Viral M clusters ( Supporting Figure 10). we have tried the ERGIC marker grp53 without any success so far,

Further, It is well documented on CryoFIB/SEM study of SARS-CoV-2-infected cells suggested the presence of “exit tunnels”, linking virion-rich intracellular vacuoles to the extracellular space (Mendonça, L. et al. Nature Communications 12, (2021)). The size of this vacuoles observed in the cell periphery was approximately 1 µm, which is well corelated with actin and viral ring we have observed from STED 2D images Also the author suggested that SARS-CoV-2 could possibly egress through these tunnels by a mechanism of exocytosis from these large intracellular vacuoles.

We have now included all above results and discussions in revised manuscripts to support our claims.

Figure S1 A. Align individual pictures in one line and do not overlap, scale bars not readable, Is in each picture the same magnification shown? Show representative pictures with the same area magnification!

Response:

Thanks to the reviewer to point out these imperfections, so we have improved the figures accordingly in the revised manuscript. Individual images are aligned properly, scale bars are readable, images are with the same magnification.

Figure 3C and 3E for better orientation magnified areas should be indicated as squares, not in circles.

Response:

As suggested, we have modified the figure 3 accordingly in the revised manuscript.

Figure S4 quality of pictures not appropriate to see differences.

Response:

We improved the figure quality in the revised manuscript (see new Figures 6 and S8)

Fig S5 All pictures overlap in one? ER marker in blue very difficult to read.

Response:

We have modified the new figure S8 as such as the ER marker is visible (in magenta color) in the revised manuscript.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors investigate the role of F-actin in infected human pulmonary alveolar A549-hACE2 cells. They investigate infection progression at different time points by the detection of the M protein by confocal microscopy and western blot. They compare the detection of M with S and N in western blot and with viral RNA detection by Q-PCR. The authors correlate M cluster formation to peak at 48h p.i. with particle assembly and particle release at 72h p.i. An increase in F-actin at 24h and 48h p.i. was monitored by confocal mircroskopy and z-stacks, whereas the overall amount of actin determined by western blot was not changed. Using 2D STED microscopy the authors identified F-actin rearrangement from stress fibers to filamentous protrusions at 24h-48h p.i. and conclude importance for particle assembly and release. By 3D STED microscopy M labeled intracellular organelles called "viral rings" surrounded by actin called "actin rings" are shown. By transmission electron microscopy (TEM) vesicular structures with budding particles were shown at intracellular membranes. The authors conclude from these findings that F-actin stabilizes assembly platforms at membranes or support the transport of virus loaded vesicles to the plasma membrane. The authors found more and longer filopodia in infected cells which were loaded with virus particles bridging cells suggesting role in cell-cell spread. At the plasma membrane they found bigger particles and at the filopodia smaller, suggesting release from the plasma membrane in packages. Transcriptom analysis of non infected and SARS-CoV-2 infected A549-hACE2 revealed upregulation of Rho-GTPaes activated proteins like PKN and α-actinins upon infection. The levels of α-actinins in WB were 2-fold higher in infected cells. The authors show that inhibitors of Rho/SRF and PKN restored cell morphology, reduced M cluster formation and virus release. The PKN inhibitor blocked M in the ER. The authors conclud from this data a role of the alpha-actinins superfamily in SARS-CoV-2 assembly and egress.

Major comments:

The presented data are convincing but some figures may need improvements, see in minor comments. For some conclusions more evidences like marker staining may be needed.

Minor comments:

The authors conclude that F-actin stabilizes assembly platforms at membranes like ERGIC, but an ERGIC marker staining is not provided. The autors suggest that F-actin migth also be involved in transport of virus loaded vesicles to the plasma membrane. Here a plasma membrane marker or native staining of particles may help to descriminate between intracellular Exosomes and extracellular particles. Co-staining with exosomal markers would also be more convincing. - Figure S1 A. Align individual pictures in one line and do not overlap, scale bars not readable, Is in each picture the same magnification shown? Show representative pictures with the same area magnification! - Figure 3C and 3E for better orientation magnified areas should be indicated as squares, not in circles. - Figure S4 quality of pictures not appropriate to see differences. - Fig S5 All pictures overlap in one? ER marker in blue very difficult to read.

Significance

The presented data provide a nice peace of work to the knoweledge on SARS-COV-2 replication in human pulmonary cells. The authors use advanced imaging and molecular biology methods for their experiments. The indentified cellular target may help to develop specific inhibitors for antiviral therapy.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors used conventional confocal and super-resolution STED microscopy to characterize the actin filament network in response to SARS-CoV-2 infection in pulmonary cells. They demonstrate that, although total levels of actin are unchanged, F-actin polymerization increases upon infection, with the most significant changes occurring at 48 hours post infection. Notably, F-actin remodels from primarily stress-fiber architectures to circularized, F-actin nanostructures that tend to colocalize with viral M cluster rings at 48 hours post infection. Additionally, there is a significant increase in F-actin-associated filopodia-like structures, with an example of a possible cell-to-cell filopodia that could possibly be a mode of inter-cellular viral transmission. The authors complement their imaging-based experiments with RNAseq to profile the cellular gene expression of SARS-CoV-2 infected pulmonary cells, revealing an upregulation of RHO GTPases activate PKNs and alpha-actinins. They show that treatment of pulmonary cells with Rho/SFR and PKN inhibitors during infection decreases the size of viral M clusters and release to comparable levels as the known viral therapeutic, Remdesivir.

Major comments:

1. The majority of the author's conclusions are based off of qualitative and quantitative analysis of their fluorescence images. While they do mention briefly an ImageJ plug-in and the statistical tests performed, the description of their quantitative image-based analyses for each experiment is lacking. For example, how was viral M cluster and actin intensity measured? How was the signal intensity normalized to account for variations in antibody labeling or other cell-to-cell variations? For figures 3C&D, how did the authors calculate viral and actin ring diameter? It is necessary to expand on the details of the quantitative analysis for each parameter mentioned in the methods section and/or include a figure panel demonstrating the details of the analysis (similar to what is nicely displayed for M cluster size in Figure S1B).
2. In particular, the details regarding the F-actin orientation measurements is lacking. Is there a consistent reference point for the orientation of the actin filaments? When comparing across two different cells, it is unclear how the orientations are normalized. Perhaps it would be more informative to plot the difference or the range in angles? Or the distribution of the differences in angles? Another point that is a bit misleading is describing this analysis as "F-actin orientation" since the term "orientation" can has a specific meaning for polar filaments such as actin. For example, given resolution limitations of the imaging approaches used in this manuscript, the authors are reporting on the orientations of bundles/populations of actins and not orientations of individual filaments relative to one another within the bundle (e.g. anti-parallel vs parallel vs branched). The authors should clarify this in the text and also further expand on the utility of their F-actin orientation analysis and how it informs us on the mechanisms of actin-mediated viral infection.
3. For the majority of figures and findings, they report that between "22<n<50 cells" were analyzed. The authors should be more specific of the exact sample size for each experiment/figure panel displayed. In particular, it is unclear in a few figure panels showing exemplar images whether or not this is the full sample size (n=1) or just an exemplar image. I recommend reporting specifically in the figure legend and/or a supplemental table outlining the sample size and analysis used for each imaging experiment to add clarify to their quantitative analysis and strengthen their claims.
4. The actin filament network can assemble into different architectures that are dependent on subcellular location. For example, actin at the basal region of the cell closest to the coverslip often assembles into stress fibers, whereas the cortical actin network often forms astral, highly branched networks. It would be important to take this into account when comparing across different cellular conditions. It is unclear if the authors were consistent with the z-slice examined for the different cellular treatment/infection conditions. Were the analyses performed on individual z-stacks or max projection images?
5. Since a major impact of this paper is the first imaging-based characterization of actin filament assembly in response to infection, the authors should provide a more comprehensive display of the raw data images. For example, figure S2 provides a nice gallery of images of actin and viral M particles, however it should show separate image channels in gray scales and consistent scaling across all images. Furthermore, all figure panels showing distinct imaging experiments and quantitative results should be complemented with a supplemental figure showing a gallery of images. This would apply to actin nanostructure rings (Figure 3C/E), filopodia and cell-to-cell contacts (Figure 4A/D), treatment with remdesivir/PKN inihibitor (Figure 6B), and ER localization of M particles (Figure S5).
6. The results in Figure 3D are difficult to interpret. The images should be larger and labeled. Also, based on the 3D STED image in Figure 3D, it appears that the brightest actin signal is actually at the center portion of the viral M cluster. Does this contradict the TEM image and what is described in the text? For Figure 3E: a more relevant analysis might be line scans across multiple images showing how relative actin-M cluster intensity varies within the dimensions of the nanostructure to demonstrate more clearly a pattern of ring assembly of both M clusters and actin.
7. The authors should address the implications and significance of the described cellular morphological changes in the context of the more physiologically relevant tissue/organ system. How do the changes they observe upon infection in isolated cultured cells compare to when these cells are assembled into tissue/organs?
8. For Figure 6 and S5, the authors infected and treated cells with an inhibitor at the same time point and demonstrate that M cluster size and release is reduced to somewhat comparable levels as treatment with Remdesivir. The authors should expand their analyses for this experiment to include the other quantitative parameters outlined in the paper: F actin/M cluster nanostructures, cellular morphology, filopodia formation, orientation of actin, etc. Additionally, it would be more informative to treat cells post-infection to more closely mimic cellular conditions of infection/treatment.

Minor comments:

1. The individual data points should be overlaid on the violin plots for better interpretability of the variability in the data.
2. For Figure 3E: the images look "stretched" with an altered relative aspect ratio.
3. The authors should include a cartoon model figure highlighting both (1) how their results contribute to our knowledge of actin-mediated viral assembly/replication and (2) unknown portions of the pathway that need to be further probed to better understand the mechanistic underpinnings of this process.
4. There have been several high resolution cellular imaging studies using other complementary 3D volumetric imaging approaches (e.g. cryo-electron tomography and FIB/SEM) to characterize the subcellular ultrastructures of SARS-CoV-2 infection. The authors should include a brief discussion on how their study complement or compare to these reports, in particular noting whether or not actin filament assemblies were observed in these data.

Significance

Impact:

This manuscript provides the first characterization of the architecture of the actin filament network upon SARS-CoV-2 infection. Since actin filament remodeling is a mechanism used by several other viruses, there is considerable interest in targeting these assemblies for the development of therapeutics to prevent and treat infection. This manuscript lays the groundwork for more detailed analysis probing the mechanisms mediating actin-mediated viral entry, replication, and release. Furthermore, it establishes some quantitative tools to standardize how this process is studied and analyzed in future studies.

Audience:

I anticipate that this work will motivate future studies aimed at further ultrastructural characterization of actin and other cytoskeletal filaments by complementary, high-resolution imaging techniques, as well as studies aimed at screening for small molecule drugs to inhibit actin-mediated viral infection.

Field of expertise:

cellular cryo-electron tomography, quantitative imaging, cytoskeletal-based motility, functional cytoskeleton-organelle interactions. Insufficient expertise to evaluate RNAseq experiments.

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Reply to the reviewers

*Reviewers comments in italics *

We thank all reviewers for their positive and encouraging comments and criticisms to improve our work. Here we present a reviewed version of the manuscript according to the comments risen.

• Reviewer #1 (Evidence, reproducibility and clarity (Required)): This is an interesting paper that identifies Tns3 as a potential effector of oligodendrocytes differentiation based on an ingenious strategy comparing regulatory binding sites of known master regulators of differentiation, and then shows using in vivo genetics that this role is indeed correct. Next, a potential mechanism is identified by showing co-localization with beta 1 integrin, known to regulate apoptosis of newly-formed oligodendrocytes. The results are well illustrated and the experiments performed with appropriate power using a broad range of techniques that combine in silico, in vitro and in vivo work to great effect.

I think this represents an important contribution that will be of significant interest to neuroscientists - the mechanisms regulating oligodendrocytes generation remain poorly understood and the evidence that this contributes to adult learning (adaptive myelination) and CNS regeneration makes this a key question. I would suggest that the following are considered before publication: We thank the reviewer for this positive comments and critics to improve the manuscript. The work describing the KO mice that were not used as they proved unsuitable need not be described - it breaks the logical flow.*

In agreement with the reviewer comment, we have reduced this part to a sort paragraph indicating that our analyses of several Tns3 constitutive KO lines showed developmental lethality and possible genetic compensation in Tns3 expression, leading us to conclude them inappropriate tools to study Tns3 function in oligodendrogenesis. We have summarized the data in Fig. S7 and the description in the method section.

It would be useful to compare the extent of cell death in the Tns3 cKO mice with that described in the alpha6 integrin KO and the integrin beta1 cKO (the Colognato and Benninger papers). Do they match? If not (and I suspect the Tns3 cKO death is greater) could other mechanisms be downstream of the Tns3?

In agreement with the reviewer comment, we have added the following paragraph to the discussion:

‘Knockout mice for integrin-a6 present a 50% reduction in brainstem MBP+ OLs at E18.5, just before they die at birth, accompanied by an increase in TUNEL+ dying OLs (Colognato et al, 2002). Similarly, conditional deletion of integrin-b1 in immature OLs by Cnp-Cre also leads to a 50% reduction in cerebellar OLs at P5, with a parallel increase in TUNEL+ dying OLs (Benninger et al., 2006). Therefore, given that Tns3-induced deletion in postnatal OPCs also leads to 40-50% reduction in OLs in both grey and white matter regions of the postnatal telencephalon (this study), paralleled by similar increase in TUNEL+ apoptotic oligodendroglia, we suggest that Tns3 is required for integrin-b1 mediated survival signal in immature oligodendrocytes.’

I'm not sure why the authors argue that the activation of beta 1 would not be informative experiment? This will regulate actin dynamics just as it regulates other integrin signaling pathways. Indeed, I would argue that an integrin activation experiments would be a neat way to prove mechanism (as it would be predicted to rescue the Tns3 cKO phenotype).

In agreement with the reviewer comment, we have removed this sentence: ‘If so, exogenous activation of integrin a6b1 in cultured OPCs by Mn2+ (Colognato et al., 2004) would not be expected to increase oligodendrogenesis in Tns3-iKO oligodendroglia.’

In an effort, to understand Tns3 function by acute Tns3-deletion in postnatal OPCs, we have compared the transcriptome of Tns3-iKO oligodendroglia compared to control cells, and we present these results in figure 7 pinpointing deregulated genes leading to reduced oligodendroglial differentiation, integrin dysregulation, increase apoptosis, and conflicting cell cycle signaling, and leaving for further studies the full characterization how the loss of Tns3 leads to the deregulation of these processes.

Can the authors provide any data on GM oligos and their OPCs? Is the requirement for Tns3 the same, and if so what might the implications be in the adult where new oligodendrocytes are being generated throughout life?

Indeed, in our analyses of Tns3-iKO mice, we provide quantifications of the cortex as a grey matter territory, showing a similar 40-50% reduction in OLs as in white matter areas (corpus callosum and fimbria, and mixed regions such as the striatum.

I note in S13 that integrin beta1 is not highly expressed in human oligos at the time in question. Does this call into question the relevance for human disease?

We realize that scRNAseq plots are never easy to interpret but it is important to note that the levels of expression are coded by the intensity of the color scale, while the surface of the dot plots indicate the experimental sensitivity to detect transcript expression in a larger or smaller proportion of the cells in a given cluster/cell type (due to the drop out limitation of current single cell RNA-seq technologies). Considering this, please note that beyond a stronger expression in neural progenitor cells (NPCs, blue color), integrin-b1 (Itgb1) transcripts are expressed at medium to high levels (green to blue) in human immature OLs (Fig. S13B), similar to their pattern of expression in mouse oligodendroglia (Fig. S13A).

Reviewer #1 (Significance (Required)): See above

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

*In this article, the authors identify and characterise Tensin3 (Tns3) as a target of key oligodendroglial transcription factors driving differentiation in the mouse. They use multiple transgenic models to describe loss of function, and suggest Tns3's action through integrin B1 signalling, with the key function being oligodendroglial survival.

There is extensive and impressive work here, including identification of Tns3 by ChIPseq, expression of Tns3 in brain development, analysis of human (ES-derived) and mouse scRNAseq to infer timing of expression in the differentiation pathway, generation of V5-tagged Tns3-KI mice to overcome antibody limitations, identification of its expression in mouse remyelination, generation of a new Tns3KO mouse, in vivo Crispr Tns3KO in development, generation of a conditional KO, for deletion in adulthood, and finally some culture work to investigate potential mechanisms of actions. The bottom line is that Tns3 is required for survival of OPCs and immature oligodendrocytes in development/remyelination in mouse at least, and loss leads to apoptosis (through p53 increase and loss of integrin-B1 signalling), leading to a failure of proper differentiation.

The experiments are carefully done, convincing and the tools generated impressive. There is clearly more to be done on clarifying the mechanism of action of Tns3, but I do not think further experiments on this topic are needed for this paper - they can wait for the next.*

We thank the reviewer for the positive and encouraging reviewing comments. In an effort, to understand Tns3 function by acute Tns3-deletion in postnatal OPCs, we have compared the transcriptome of Tns3-iKO oligodendroglia compared to control cells, and we present these results in figure 7 pinpointing deregulated genes leading to reduced oligodendroglial differentiation, integrin dysregulation, increase apoptosis, and conflicting cell cycle signaling, and leaving for further studies the full characterization how the loss of Tns3 leads to the deregulation of these processes.

My only query is whether the expression of Tns3 is also in immature OLs in human brain (rather than human ES-derived OLs). This should be easily checked with interrogation of online Shiny apps from already published snRNAseq from various groups on human post mortem adult brain, but if not present then in also baby/fetal brain. This would be interesting and may well be different from the ES_derived cells which tend to be very immature and would add interest to the possible translational impact.

According to the suggestion of the reviewer, we analyzed 69,174 snRNAseq GW9-GW22 from fetal cerebellum,; Aldinger & Miller, 2021; https://doi-org.proxy.insermbiblio.inist.fr/10.1038/s41593-021-00872-y), which we present now in Figure S3, finding a cluster of cells expressing iOL markers, including NKX2-2, TNS3, ITPR2, and BCAS1, similar to the hiPSCs-derived iOL1/iOL2 clusters and mouse iOL1/iOL2 clusters shown in Fig. S2.

We also analyzed other datasets without finding iOLs given their age or numbers, including:

• Immunopanned PDGFRA+ cells from human cortex GW20-GW24 (2690 cells, Huang and Kriegstein, Cell 2020) finding OPCs but not iOLs.

-The recently published dataset from GW8-GW10 human forebrain oligodendroglia (van Brugen & Castelo-Branco, Dev Cell 2022; https://doi.org/10.1016/j.devcel.2022.04.016) containing OPCs but not iOLs.

-The GW17 to GW18 human cortex (40,000 cells, Polioudakis & Geschwind, 2019, https://doi.org/10.1016/j.neuron.2019.06.011) containing OPCs but not iOLs.

Reviewer #2 (Significance (Required)): This work extends our knowledge of oligodendroglial differentiation, links it to the ECM and provides interest in manipulating this in diseases including glioma. My expertise: myelin, oligodendroglia, remyelination, human neuropathology

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

see below Reviewer #3 (Significance (Required)): Using purified oligodendrocytes target genes of key regulators of oligodendrocyte differentiation were analyzed, which led to the identification of Tensin-3. The authors performed a detail characterization of Tensin-3 expression. They found that Tensin-3 is highly expressed in immature mouse and human oligodendrocytes. Interestingly, Tensin-3 is selectively enriched in immature oligodendrocytes, and not present at detectable levels in OPCs and mature oligodendrocytes. Subsequently, the authors characterized Tensin-3 function by a series of knockdown approaches in vitro and in vivo. These series of experiments revealed an essential function of Tensin-3 in supporting oligodendrocytes survival. In the absence of Tensin-3 a large fraction of oligodendrocytes undergo apoptosis while differentiating to mature oligodendrocytes. This is a remarkable study applying an impressive array of methods that led to an important discovery in the field of oligodendrocyte biology. The main advances for the field are: 1) identification of a novel marker for premyelinating oligodendrocytes, 2) elucidation of Tensin-3 as a pro-survival factor in oligodendrocytes differentiation, 3) evidence of link of Tensin-3-integrin signal in survival of oligodendrocytes. The data is well presented and organized, and the paper well written. I recommend publication with only minor suggestions for a revision:

• *

We thank the reviewer for this positive comments and critics to improve the manuscript.

In Figure 2, only images are shown, and the data is referred to as highly expressed or strong co-localization. Even if the data looks clear, the authors should provide some quantification of the data in the figure.

We thank the reviewer for his comment and we have now provided a quantification of the fraction of Tns3+ cells expressing different markers of oligodendrocyte lineage progression/stages, and the percentage of each stage expressing Tns3.

Figure 3 is given too much weight in the manuscript text. I would recommend to shorten the text in the result section, and to move this figure to the supplement as it does not advance the story. It mainly shows that the KO mice still express transcripts in the brain. Were the transcripts lost in peripheral tissue?

• *

As mentioned above, in agreement with the reviewers #1 and #3 comments, we have reduced this part to a sort paragraph indicating that our analyses of several Tns3 constitutive KO lines showed developmental lethality and possible genetic compensation in Tns3 expression, leading us to conclude them inappropriate tools to study Tns3 function in oligodendrogenesis. We have summarized the data in Fig. S7 and the description in the method section.

Page 11: the authors describe in the text how the floxed allele was generated. This should be shifted to the supplement.

According to reviewers suggestion, we have moved the description of Tns3 floxed allele generation to the Methods section. Page 16: the authors refer to Bcas1 as a problematic marker for immature oligodendrocytes, because the transcript is also expressed in mature oligodendrocytes. The authors are correct that the transcript is expressed in mature oligodendrocytes. However, the proteins changes its localization when oligodendrocytes mature. On protein level, it is valuable and a selective marker, as antibodies only label pre-myelinating and actively myelinating cells. In mature oligodendrocytes, antibodies against Bcas1 do not label the cell, only myelin. The text is misleading and needs to be corrected.

In agreement with reviewers comment we have modified the text as follows: ‘An optimized protocol for immunodetection using Bcas1-recognizing antibodies has been shown to label iOLs (Fard et al., 2017).’

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Referee #3

Evidence, reproducibility and clarity

see below

Significance

Using purified oligodendrocytes target genes of key regulators of oligodendrocyte differentiation were analyzed, which led to the identification of Tensin-3. The authors performed a detail characterization of Tensin-3 expression. They found that Tensin-3 is highly expressed in immature mouse and human oligodendrocytes. Interestingly, Tensin-3 is selectively enriched in immature oligodendrocytes, and not present at detectable levels in OPCs and mature oligodendrocytes. Subsequently, the authors characterized Tensin-3 function by a series of knockdown approaches in vitro and in vivo. These series of experiments revealed an essential function of Tensin-3 in supporting oligodendrocytes survival. In the absence of Tensin-3 a large fraction of oligodendrocytes undergo apoptosis while differentiating to mature oligodendrocytes.

This is a remarkable study applying an impressive array of methods that led to an important discovery in the field of oligodendrocyte biology. The main advances for the field are: 1) identification of a novel marker for premyelinating oligodendrocytes, 2) elucidation of Tensin-3 as a pro-survival factor in oligodendrocytes differentiation, 3) evidence of link of Tensin-3-integrin signal in survival of oligodendrocytes. The data is well presented and organized, and the paper well written.

I recommend publication with only minor suggestions for a revision:

In Figure 2, only images are shown, and the data is referred to as highly expressed or strong co-localization. Even if the data looks clear, the authors should provide some quantification of the data in the figure.

Figure 3 is given too much weight in the manuscript text. I would recommend to shorten the text in the result section, and to move this figure to the supplement as it does not advance the story. It mainly shows that the KO mice still express transcripts in the brain. Were the transcripts lost in peripheral tissue?

Page 11: the authors describe in the text how the floxed allel was generated. This should be shifted to the supplement.

Page 16: the authors refer to Bcas1 as a problematic marker for immature oligodendrocytes, because the transcript is also expressed in mature oligodendrocytes. The authors are correct that the transcript is expressed in mature oligodendrocytes. However, the proteins changes its localization when oligodendrocytes mature. On protein level, it is valuable and a selective marker, as antibodies only label pre-myelinating and actively myelinating cells. In mature oligodendrocytes, antibodies against Bcas1 do not label the cell, only myelin. The text is misleading and needs to be corrected.

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 article, the authors identify and characterise Tensin3 (Tns3) as a target of key oligodendroglial transcription factors driving differentiation in the mouse. They use multiple transgenic models to describe loss of function, and suggest Tns3's action through integrin B1 signalling, with the key function being oligodendroglial survival.

There is extensive and impressive work here, including identification of Tns3 by CHIPseq, expression of Tns3 in brain development, analysis of human(ES-derived) and mouse scRNAseq to infer timing of expression in the differentiation pathway, generation of V5-tagged Tns-KI mice to overcome antibody limitations, identification of its expression in mouse remyelination, generation of a new Tns3KO mouse, in vivo crispr Tns3KO in development, generation of a conditional KO, for deletion in adulthood, and finally some culture work to investigate potential mechanisms of actions. The bottom line is that Tns3 is required for survival of OPCs and immature oligodendrocytes in development/remyelination in mouse at least, and loss leads to apoptosis (through p53 increase and loss of integrinB1 signalling), leading to a failure of proper differentiation.

The experiments are carefully done, convincing and the tools generated impressive. There is clearly more to be done on clarifying the mechanism of action of Tns3, but I do not think further experiments on this topic are needed for this paper - they can wait for the next.

My only query is whether the expression of Tns3 is also in immature OLs in human brain (rather than human ES-derived OLs). This should be easily checked with interrogation of online Shiny apps from already published snRNAseq from various groups on human post mortem adult brain, but if not present then in also baby/fetal brain. This would be interesting and may well be different from the ES_derived cells which tend to be very immature and would add interest to the possible translational impact.

Significance

This work extends our knowledge of oligodendroglial differentiation, links it to the ECM and provides interest in manipulating this in diseases including glioma.

My expertise: myelin, oligodendroglia, remyelination, human neuropathology

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

This is an interesting paper that identifies Tns3 as a potential effector of oligodendrocytes differentiation based on an ingenious strategy comparing regulatory binding sites of known master regulators of differentiation, and then shows using in vivo genetics that this role is indeed correct. Next, a potential mechanism is identified by showing co-localization with beta 1 integrin, known to regulate apoptosis of newly-formed oligodendrocytes. The results are well illustrated and the experiments performed with appropriate power using a broad range of techniques that combine in silico, in vitro and in vivo work to great effect.

I think this represents an important contribution that will be of significant interest to neuroscientists - the mechanisms regulating oligodendrocytes generation remain poorly understood and the evidence that this contributes to adult learning (adaptive myelination) and CNS regeneration makes this a key question. I would suggest that the following are considered before publication:

The work describing the KO mice that were not used as they proved unsuitable need not be described - it breaks the logical flow.

It would be useful to compare the extent of cell death in the Tns3 cKO mice with that described in the alpha6 integrin KO and the integrin beta1 cKO (the Colognato and Benninger papers). Do they match? If not (and I suspect the Tns3 cKO death is greater) could other mechanisms be downstream of the Tns3?

I'm not sure why the authors argue that the activation of beta 1 would not be informative experiment? This will regulate actin dynamics just as it regulates other integrin signaling pathways. Indeed, I would argue that an integrin activation experiments would be a neat way to prove mechanism (as it would be predicted to rescue the Tns3 cKO phenotype).

Can the authors provide any data on GM oligos and their OPCs? Is the requirement for Tns3 the same, and if so what might the implications be in the adult where new olligodendrocytes are being generated throughout life?

I note in S13 that integrin beta1 is not highly expressed in human oligos at the time in question. Does this call into question the relevance for human disease?

Significance

See above

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

The manuscript by Tran et al. describes the mechanism by which IFNa treatment prevents the development of liver CRC metastasis in several mouse models. They show how continuous administration of IFNa strength liver vascular barrier by a direct effect on endothelial cells and avoids the trans-sinusoidal migration of tumour cells.

Major points:

1. Authors use an elegant orthotopic model of liver metastasis to confirm the effect of continuous IFNa on hepatic colonization (Fig.3). Although they extensively characterize the metastatic lesions, they do not show data on the potential impact of IFNa treatment in the primary caecum tumour. Authors should clarify if the described effects are taken place in the liver or/and in the caecum. It would be interesting to show if IFNa affects the primary tumour size, the extravasation of cancer cells and the immune infiltration since all these factors could have an impact in the number of liver lesions.

We thank the reviewer for acknowledging the importance of our results particularly in the context of the orthotopic mouse model we developed. We agree that displaying the results of continuous IFNα therapy on primary intracecal tumors, as well as the results pertaining to the few mice that develop microscopic or macroscopic liver metastasis, is important for the interpretation of our work. Thus, we evaluated the dimension of primary intracecal CRC lesions (Fig 3D,E) and we performed additional IHC characterization of the primary tumors (Fig S4A,B). The analysis showed that the dimension of the primary lesions and the markers we analyzed were non significantly modified by continuous IFNα therapy (Fig 3D,E and Fig S4A,B). These results favor the hypothesis that IFNα therapy does not modify the number of cells that spread from the primary tumors and seed into the liver, but it rather impinges on the intravascular containment of CRC cells circulating within the liver (Fig 3F). As said earlier, the data also highlight the possibility that CRC tumors may become refractory to IFNα or that the dose and schedule we adopted does not significantly affect the growth of established liver CRCs at late time points. The data are also consistent with results obtained with MC38Ifnar1_KO CRC cells indicating that continuous IFNα therapy does not require Ifnar1 expression by tumor cells to exert its antimetastatic function (Fig 4A,C-D). This is also in line with the high IFNα concentrations required to activate the "tunable" direct antiproliferative functions of this cytokine that exceed those achieved in our system (Catarinella et al, 2016; Schreiber, 2017). Text has been added in the revised manuscript at lines 175-197 and in the discussion lines 425-431.

1. Figure 3f right shows liver images without any obvious metastatic lesion. Since authors are analysing the effect of IFNa treatment in proliferation, vascularization and immune composition in liver tumours, they may show and quantify images with metastatic lesions and restrict the analysis to the tumour area.

Since the main finding of our manuscript regards the prevention of hepatic colonization by continuous IFNα therapy, we think that the original data presented in Fig 3G,H are representative of the overall efficacy of our strategy that confers protection in up to 60% of the mice carrying intramesenteric tumors of increasing dimensions (Fig 3H). We have thus maintained our original results, adding the quantification of all IHC data on groups of Sham control livers (n=6), as suggested. In any case, we also included the same IHC characterization of the few and small intrahepatic lesions that have bypassed the intravascular antimetastatic barrier (Fig S4C,D). Indeed, in agreement with the results observed in primary intracecal lesions, these metastatic lesions that developed in IFNαtreated mice showed similar markers of cell proliferation, neoangiogenesis, F4/80 macrophages and CD3+ T cells, as control lesions detected in NaCl-treated mice. Once again, the results highlight the possibility that CRC tumors, once established as micro/macroscopic metastases, may become refractory and resistant to IFNα therapy by downregulating the Ifnar1 in various components of the tumor microenvironment (Boukhaled et al., 2021; Katlinski et al., 2017). Text has been added in the revised manuscript at lines 175-197 and in the discussion lines 496-515.

1. Authors analyse the recombination efficiency of different mouse CRE lines by non-quantitative methods (PCR of hepatic genomic DNA and GFP expression by immunofluorescence in healthy liver). Since PDGFRβ-Cre/ERT2 and CD11c-Cre lines are used to exclude a role of IFNa on the targeted cells, authors should provide stronger evidences to support this. They may consider studding the ablation of Ifnar1 in FACS sorted fibroblasts and myeloid cells. Moreover, it would be important showing the proportion of GFP+ cells in the sorted populations to understand how broadly these stromal populations are targeted.

We thank the referee for raising this important issue, which is related to the relative efficiency of Ifnar1 recombination in each of the Cre-expressing mouse models we have used in the study. To this regard, we newly performed an extensive colocalization analysis quantifying the percentage of GFP+ cells that colocalize with cell specific markers (i.e., PDGFRβ, CD11c, F4/80 and CD31) of the various mouse models (PDGFRβCreERT2, CD11cCre and VeCadCreERT2, respectively) crossed with RosaZsGreen reporter mice. Colocalization analysis of GFP in the different systems was performed using the ImageJ “colocalization” algorithm developed by Pierre Bourdoncle (Institut Jacques Monod, Service Imagerie, Paris; 2003–2004). The method allows the generation of unsupervised profiles of co-localized pixels between two channels. This methodology has been included in the section Methods and Protocols, line 806-809. Of note, we observed an almost complete recombination in liver fibroblast (GFP+/PDGFRβ+), with about 98.2 ± 0.72% hepatic stellate cells that co-expressed GFP+ and PDGFRβ+ signals (see the new Fig S5E). Similarly, hepatic DCs (GFP+/CD11c+) had 94.17 ± 2.16% colocalization, while F4/80+ KCs or LCMs (GFP+/F4/80+) colocalized in 78.14 ± 5.03% (see the new Fig S5E). Finally, HECs, including LSECs, (GFP+/CD31+) showed 85.3 ± 5.03% colocalization (see the new Fig S5E,F), with no expression of GFP signals in cells other than CD31+. Note that these values indicate an almost complete colocalization of the Cre recombinase in the target cell types analyzed (see representative IF shown in Fig S5E). Text has been added in the revised manuscript at lines 225-233. Moreover, DEGs analysis between NaCl-treated VeCadIfnar1_KO and Ifnar1fl/fl HECs showed a significant downregulation of Ifnar1 expression in CD31+ VeCadIfnar1_KO cells, with a log2 fold-change of -0.387 and an adjusted p-value of 0.033, further confirming Cre recombination in HECs isolated from VeCadIfnar1_KO mice (as depicted in the heatmap of Fig 6B; the 12th gene of the Type I IFN response is Ifnar1). We have prepared all source images at higher dimension to better appreciate the colocalization within liver microvasculature. In addition, we performed several flow cytometry analyses to identify liver cell populations of Cre-recombinant mice that express Ifnar1. Unfortunately, the predicted low cellular surface expression of this molecule coupled with the experimental conditions needed to extract viable non-parenchymal cells from the liver have prevented us from obtaining informative results.

1. Ifnar1 ablation in VeCad+ cells prevents the effect of IFNa on tumour growth (Fig. 4d), suggesting the existence of anti-tumour mechanisms beyond the effects on hepatic colonization. Authors may consider checking proliferation, vascularization and immune infiltration in these tumours to enhance their conclusion.

We fully agree with the referee’s concern and as above mentioned, we have followed his/her suggestion and examined the existence of antitumor mechanisms beyond the effects on hepatic colonization in VeCadIfnar1_KO mice treated with NaCl or IFNα. To this end, 4 NaCl-Ifnar1fl/fl, 7 IFNα-Ifnar1fl/fl, 4 NaCl-VeCadIfnar1_KO and 4 IFNα-VeCadIfnar1_KO mice were intrasplenically injected with MC38 CRC cells (Fig S7A,B). Twenty-one days after injection, mice were euthanized and their livers analyzed for tumor size, proliferation, signs of angiogenesis (as denoted by CD34 staining) and immune infiltration (F4/80+ macrophages and CD3+ T cells). Consistent with data presented in Fig 4D, histological analysis showed that Ifnar1fl/fl mice did not develop liver metastases in IFNα-treated mice. Furthermore, metastatic lesions detected in VeCadIfnar1_KO mice treated or not with IFNα did not show significant differences in Ki67 positivity, CD34 staining or the amount of F4/80+ resident macrophages and CD3+ T cells. This further supports that the antimetastatic potential of IFNα therapy may be primarily depend on the inhibition of hepatic trans-sinusoidal migration, a limiting step in the metastatic cascade that could secondarily influence colonization and outgrowth (Chambers et al, 2002). Corresponding text has been added at lines 248-252.

1. Immune properties of LSECs are analysed in vivo by using a mouse CRE line that targets all endothelial cells, including those ones located in lymphoid organs, and evaluating T cell composition in the spleen. I found difficult to conclude that these properties are exerted directly by LSECs and not by other endothelial cells in vivo. To clarify the local effect of LSECs in modulating anti-tumour immunity, T cell composition and activation should be checked in tumours shortly after tamoxifen administration.

We thank the reviewer for pointing out this issue, which cannot not be tested directly because - as also mentioned by reviewer 2 - LSEC-specific Cre-recombinant driver mice do not exist . As also indicated in the cited literature, central memory T cells accumulate after peripheral priming in secondary lymphoid organs such as the spleen (Sallusto et al, 2004; Stone et al, 2009; Yu et al, 2019). To this end, the generation and regulation of antitumor immunity is a highly orchestrated multistep process involving the uptake of tumor-associated antigens by professional APCs, their time-consuming migration to draining lymph nodes and the generation of protective T cells. Unlike other APCs, HECs/LSECs do not need to migrate to draining lymph nodes to activate effector T cells, leading to a rapid intrahepatic CD8+ T cell activation. In this context, LSECs must not only efficiently uptake, process and present CRC-derived antigens coming from intravascularly contained tumor cells, but they also require the attraction and retention within the liver micro-vasculature of T cell populations necessary for the generation of effective antitumor immune responses, where chemokines play an important role (Lalor et al, 2002). As shown in Fig 6A-C, two prominent chemokines (Cxcl10 and Cxcl9) required for T cell recruitment to the liver are specifically upregulated only in HECs/LSECs from IFNα-treated Ifnar1fl/fl mice, whereas HECs from VeCadIfnar1_KO mice maintained low expression of these chemoattractants in both NaCl- and IFNα-treated mice. These data are also consistent with the in vitro cross-priming results (see Fig 7A,B) showing that in the absence of IFNα, HECs have a low capacity to prime naïve T cells (Katz et al, 2004), indicating that LSEC-primed by tumor-derived antigens coming from apoptotic intravascular CRC metastatic cells play an important role in inducing tolerance (Berg et al, 2006; Katz et al., 2004), especially when CRC cells quickly extravasate and position within the space of Disse, likely becoming less accessible to intravascular patrolling by naïve and effector T cells (Benechet et al, 2019; Guidotti et al, 2015). On the contrary, in IFNα-treated Ifnar1fl/fl mice, CRC cells are rapidly contained in the liver microvasculature (Fig 5A,B) with CRC-derived antigens that could be immediately taken up by LSECs due to their anatomical proximity and efficient endocytosis capacity, which is among the highest of all cell types in the body (Sorensen, 2020). Here, the continuous sensing of IFNα by LSECs upregulates several genes related to antigen processing and presentation pathways (Fig. 6B,D), leading to efficient cross-priming of tumor-specific CD8+ T cells to the same extent as professional APCs, such as splenic DCs (Fig 7B). Text has been added in the revised manuscript at lines 496-515. Finally, regarding the suggestion to analyze the role of HECs/LSECs in inducing antitumor T cell immunity shortly after tamoxifen administration, while we agree that it would be interesting to analyze HEC/LSEC-mediated T cell activation by treating NaCl- and IFNαtreated Ifnar1fl/fl and VeCadIfnar1_KO mice with tamoxifen after CRC cell injection, we would like to point out that tamoxifen treatment will not only induce Cre recombination and Ifnar1 loss on endothelial cells but it may also induce several “off-target” effects complicating the interpretation of the results. Indeed, tamoxifen is known to i) inhibit the in vitro proliferation of several CRC cell lines (Ziv et al, 1994), ii) impair the growth of CRC liver metastases in vivo (Kuruppu et al, 1998) and iii) modify matrix stiffness to reduce tumor cell survival (Cortes et al, 2019). Further, as IFNα modifies the hepatic vascular barrier and the accessibility of antigens by LSECs, the specific timing of tamoxifen treatment could also affect the immunological consequences of Ifnar1 deletion making these experiment impractical. For these reasons, we’d like not to perform the suggested experiment with tamoxifen.

Reviewer #1 (Significance):

The conclusions of this study are consistent with previously published literature and the biological insights are potentially useful to the cancer biology community.

Reviewer #2 (Evidence, reproducibility and clarity):

In this study Dr. Sitia's group investigated the effect of IFNα1 as perioperative agent preventing liver metastasis formation of colorectal carcinoma (CRC). To this end, various mouse models were used such as liver colonization models, i.e. intrasplenic and mesenterial injections of MC38 and CT26 CRC cell lines. Besides, spontaneous metastasis of CRC was analyzed by orthotopic injection of MC38 into the cecum. To study the influence of IFNα1 in these settings mini-osmotic pumps releasing IFNα1 were used. Moreover, conditional mouse models with a cell-type specific deficiency of Ifnar1 were compared. Altogether, the application of IFNα1 led to a reduction in liver colonization of CRC in all models studied. This was ascribed to decreased trans-sinusoidal migration of CRC and increased cross-priming by LSEC entailing in T cell activation.

Major comments:

Overall the study is well performed and the major conclusions seem to be drawn well. However, there are certain points I like to address:

• First, the authors started their experiments with MC38 and CT26 CRC cell lines. At the end they just applied MC38. The rational behind this should be clearly stated. Second, as in their previous publication (Catarinella et al, 2016) F1 hybrids of C57BL/6 x BALB/c mice were used for the experiments. However, I believe that the genetic heterogeneity might be strongly increased by this approach which might lead to difficult reproducibility of the results.

We thank the referee for raising this important issue; additional text describing the reason of our choice has been introduced at lines: 203-205. We respectfully disagree with the comment that CB6F1 hybrids may increase genetic heterogeneity and impair reproducibility of our results. Each CB6F1 hybrid individual is genetically identical to its littermates, sharing 50% of genes of each parental mouse line and being tolerant to reciprocal MHC-I genes (thus permitting the correct engraftment of both cell lines). We agree that the use of mismatched backcrosses after the F1 generation would increase genetic heterogeneity and thus may affect outcome. This is also the reason why we could not perform experiments with CT26 in the Ifnar1fl/fl conditional lines that are in C57BL/6 background and would have needed at least 10 generations of backcrossing in the BALB/c background before being suitable to such experiments. Finally, all experiments described in Fig 4, 5, 6 and 7 were performed in C57BL/6 mice using MC38 CRC cells with results that reproduced those obtained in CB6F1 hybrids, and very similarly to what we have previously reported with MC38 in C57BL/6 mice (see Fig 5 (Catarinella et al., 2016)).

• At page 16 the authors conclude that "patients suffering from chronic liver fibrotic disease... display lower incidence of hepatic metastases". In the community there is contradictory data (see Kondo et al, BJC, 2016, https://www.nature.com/articles/bjc2016155). This should be precisely discussed, otherwise this claim should be removed.

We thank the referee for raising this issue and modified the discussion accordingly. Text has been added in the revised manuscript at lines 455-457.

• In the discussion section the interplay of other cell types within the hepatic niche should be stated. For example, in Toyoshima's study a direct anti-tumoral effect of dendritic cells releasing IFNα1 was demonstrated (see Toyoshima et al, Cancer Immunol Res, 2019, https://aacrjournals.org/cancerimmunolres/article/7/12/1944/469540/IL6-Modulates-the-Immune-Status-of-the-Tumor). This further strengthens your data.

We agree with the reviewer's suggestion and added new text to recognized the interplay between different cell types such as dendritic cells within the hepatic niche (see new text at lines 505-515).

• Last, multiple times the authors write about data that is "not shown". Please either include these data in the manuscript or delete corresponding phrases because it is not possible for the reader to scrutinize it.

We fully agree with the referee’s concern and displayed all “not shown results” in Fig S1E and Fig S9C-I.

• Besides, I suggest additional experiments further substantiating the study:
• To see if this effect of IFNα1 is cell type-specific liver metastasis of other solid tumors such as breast cancer or melanoma should be investigated.

We agree with the reviewer's suggestion, as also indicated in our original discussion. We believe that additional experiments with other solid tumor cell lines would be important to generalize the potential of perioperative IFNα therapy. In particular, we believe that pancreatic ductal adenocarcinoma (PDAC), a highly lethal disease that most commonly metastasizes to the liver (Lambert et al, 2017), may benefit from our approach. It should be noted, however, that the pleotropic nature of IFNα allows this cytokine to inhibit tumor growth by several mechanisms. Above all, the ability of IFNα therapy to directly reduce tumor growth depends on the relative surface expression of Ifnar1 on each tumor cell and the ability to maintain such expression in the harsh tumor microenvironment during IFNα therapy. As the degradation of Ifnar1 by CRC tumors has been well described (Katlinski et al., 2017), it is possible that CRC tumors thus escaping the antitumor properties of endogenous type I interferons may respond less efficiently to therapeutic IFNα regimens such as those herein described. This notion is consistent with our data on primary orthotopic tumors (Fig. 3D,E), which are no longer responsive to continuous IFNα therapy as early as 7 days after implantation of CT26LM3 cells. In addition, the definition of the HEC/LSEC antimetastatic barrier has been possible only because CRC cells are not directly susceptible to the IFNα antiproliferative activity, which we observed in vitro at extremely high IFNα dosages (Catarinella et al., 2016) but not in vivo (as formally demonstrated by using MC38Ifnar_ko cells, Fig 4A). At any rate, we followed the reviewer’s suggestion and performed an additional experiment in which we intramesenterically injected the PDAC cell line Panc02 (H-2b, C57BL/6-derived) (Soares et al, 2014) into C57BL/6 mice 7 days after of NaCl or IFNα therapy initiation. As shown below, MRI analysis at day 21 showed that none of the IFNα-treated Panc02 challenged mice developed metastatic lesions, while NaCl controls displayed a high metastatic burden that required euthanization for ethical reasons of about 67% of these mice shortly after MRI analysis. These data indicate that perioperative IFNα therapy completely curbs metastatic development in IFNα-treated PDAC animals. The notion that these cells may be more IFNα-susceptible than CRCs may well depend on the relative capacity of the former cells to maintain Ifnar1 expression, as suggested by others (Zhu et al, 2014). Properly addressing the reviewer’s comment would thus require extensive investigations involving the establishment of new mouse models of metastases from other solid tumors, starting from the in vitro and in vivo regulation of surface Ifnar1 expression in each tumor cell. We strongly believe that this work has merit but we think that it should be reported separately.

• The authors applied a broad range of cell type-specific mice. However, a thorough characterization of the deletion of Ifnar1 in the corresponding cell types is missing. This is crucial for the manuscript.

We fully agree with the referee’s concern and as previously mentioned, we have improved the characterization of Ifnar1 deletion (see response to the same critique received from reviewer 1, comment 3).

• The capillarization of the hepatic vascular niche is a crucial point in this story. I believe that the hepatic endothelium should be further characterized by additional vascular markers.

In response to the reviewer’s suggestion, we have included in our analysis the characterization of Lyve-1, a marker of hepatic capillarization (Pandey et al, 2020; Wohlfeil et al, 2019). Indeed, IFNα treatment of Ifnar1fl/fl mice significantly increased the expression of Lyve-1, whereas IFNα treatment of VeCadIfnar1_KO mice showed no effect (Fig S9A,B), further corroborating our findings. Text has been added in the revised manuscript at lines 291-294. To better aid readers, we have prepared high-resolution images for each IF channel and have provided these data as source date for Fig S9A.

• Last, the data and methods appear adequately presented and experiments seem to be reproducible. Just in Figure 4 the exact number of mice and replicates are not clearly presented. Otherwise, everything is fine.

We thank the reviewer for raising this issue, which apparently was not properly described in our original submission. We have now included the exact number of mice in each experimental group in the figure legend to Fig 4.

Minor comments:

Overall the text and figures are accurately presented. However, I would like to add further minor comments:

• In Fig. 1 you present the IFNα dosing regimen. How do you explain the decrease in serum IFNα after day 2? Besides, the data points at day 0 should be excluded since measuring startet from day 2! Why did you decide to treat for seven days until the start of the experiment? One could think 2 days might already be enough.

We thank the reviewer for raising these important points. Regarding the pharmacokineticpharmacodynamic (PK-PD) behavior of our approach, we do not believe that MOP reduced its pumping efficacy after day 2 (Theeuwes & Yum, 1976), nor that counterregulatory mechanisms, such as the induction of anti-IFNα blocking antibodies, occurred in such a short time frame (Wang et al, 2001). It is neither feasible that IFNα treatment significantly downregulated Ifnar1 in the liver (as demonstrated by pSTAT1 activation after MOP treatment in Fig S1E). Rather, our results reflect the PK-PD behavior of other long-lasting formulations of IFNα, which depend on intrinsic pharmacological properties of IFNα already described in (Jeon et al, 2013). Text has been added in the revised manuscript at lines 110-112. We also corrected the figures in which we quantified serum IFNα. Indeed, blood was drawn one day before MOP implantation rather than on the same day of surgery to avoid additional blood loss, which could be a source of unnecessary stress for the animals. Therefore, we corrected the results section and Fig S1A-C and Fig 1A,B. The decision to start treatment 7 days rather than 2 days before seeding was made for several reasons: i) this study follows our previous gene/cell therapy approach, in which the time interval between reconstitution of the transduced bone marrow with Tie2-IFNα and tumor challenge was at least 7-8 weeks. We therefore thought that 7 days might be a sufficient/necessary time period to induce similar phenotypes in the liver after continuous IFNα administration; ii) 7 days is a time frame compatible with the perioperative period in humans (Horowitz et al, 2015). Furthermore, the side effects that patients may experience after IFNα therapy are generally limited to the first few days after administration, allowing patients to benefit from IFNα-induced vascular antimetastatic barriers at the time of surgery without potential side effects of IFNα. Because oncologic guidelines recommend starting adjuvant chemotherapy at least 4 weeks after surgery in stage 2-3 CRC patients at risk of later developing liver metastases (Engstrand et al, 2019; van Gestel et al, 2014), our proposed perioperative time frame does not even conflict with these indications (Van Cutsem et al, 2016). We have included additional text in the lines 131-132 to motivate the timing of our regimens.

• Fig. 2: Did you check for metastases in other organs than the liver at the timepoint of euthanization, e.g. lungs. In the discussion section you talk about a potential influence of IFNα1 on other organs. Therefore, I think that the mice should be thoroughly analyzed and the data presented. The manuscript will benefit from it.

We thank the reviewer for this valuable comment. Indeed, we always check for dissemination of CRC metastases on MRI analysis and necroscopy. As stated at lines 146-147 and 158 CRC tumors seeded in the liver vasculature after colonizing the liver do not spread to other organs such as the lungs. Indeed, CRC cells intravascularly seeded in the portal circulation, are trapped at the beginning of hepatic sinusoids because their diameter is bigger than that of liver sinusoids (Fig S8A,B). These micro-anatomic peculiarities are also thought to impede the spreading of tumor cells from periportal to centrilobular areas and to the general circulation (Catarinella et al., 2016; Vidal-Vanaclocha, 2008), and this is consistent with studies showing that in CRC patients undergoing surgery the majority of CRC-derived circulating tumor cells are found in the portal vein (Deneve et al, 2013).

• Overall, MRI pictures and pictures of IHC or IF are sometimes too small to see. Please provide pictures with larger magnification or enlarge the images.

We thank you for this suggestion and we have indeed increased the size of all MRI, IHC, and IF images to the maximum that will fit within the figure. In addition, we presented the images at the highest magnification available, without making digital enlargements that would significantly reduce resolution.

• Fig. 3 F, G: immune cell infiltration in the liver was analyzed. Please compare it to untreated, tumor-free wildtype liver tissue.

We appreciated the reviewer's suggestion and included the results of six Sham mice per each marker in our analysis. The text was added on the figure legends to Fig 3H and Fig S4B,D.

• Fig. 6: the graphs are too small to be read, especially the volcano plot and the gene names of the heatmap.

We increased the font size of genes in the volcano plots and heatmap in Fig 6A,B, as suggested.

• Fig. S6: Pictures of co-immunofluorescences are presented. For the reader it is really hard to distinguish the stainings and to identify colocalized areas. Please provide pictures with one channel to better compare the marker expression.

We thank the reviewer for pointing this out and we have tried to make each panel as large as possible to fit into a two-column figure. We have also prepared high magnification images of each channel for all immunofluorescence images, which we provide as source data. We hope that this is sufficient to help readers to interpret our results without increasing the number of main or supplementary figures.

• From page 8 onwards (section about transgenic mice) LSEC was used as kind of synonym for hepatic endothelial cells. Since there is still no LSEC-specific driver mouse, it should be stated "hepatic endothelial cells" instead.

We agree with this suggestion and thus have indicated that the results refer to HECs but include a large majority of LSECs. Indeed, LSECs make up the majority (~89%) of the total HEC population (Su et al, 2021). In addition, some SEM and TEM analyses were performed only on LSECs, as well as the IF analyses. Therefore, we believe that LSECs play an important role in this process. Although not specifically suggested, we have also changed the title of our manuscript to reflect the reviewer's suggestion. Thus, we propose "Continuous sensing of IFNα by hepatic endothelial cells shapes a vascular antimetastatic barrier" as new title.

• P. 11: there is a typo: Fig. Fig. S6G,H

We corrected this typo.

• P. 13: the authors describe Gata4 as inhibitor of subendothelial matrix deposition. This should be precisely written, since Gata4 originally is described as master-regulator of liver sinusoidal differentiation which leads to liver fibrosis development upon loss of Gata4.<br /> Besides, I came across a study of the same group that investigated the role of Notch signaling in hepatic CRC and melanoma metastasis (Wohlfeil et al, Cancer Res, 2019, https://aacrjournals.org/cancerres/article/79/3/598/638600/Hepatic-Endothelial-Notch-Activation-Protects). Similar to your study they tie the reduction in hepatic metastasis to capillarization of the hepatic microvasculature.

We agree with this suggestion and modified text accordingly. We are also glad that our results agree with previous reported literature that has now been correctly cited at lines 351-356 and in the discussion lines 474-476.

• The discussion reads like paraphrasing the results section. The manuscript would clearly benefit if the discussion section had been rewritten short and concisely.

We agree with this suggestion, and we have modified discussion accordingly. We are also willing to shorten the discussion by removing the schematic model that could possibly be used as a graphical abstract.

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Reviewer #2 (Significance):

• Since liver metastases of various tumor are tremendously hard to treat and mediates therapy resistance, the authors focus on a very important field of research - prevention of liver metastasis formation.
• This study adds insights into the mechanisms of action of IFNα1 in the hepatic microenvironment. It extends previous findings of Toyoshima who described anti-tumoral effects of IFNα1 released by dendritic cells in the liver.
• The study is well designed and will be of great interest for the scientific community. Besides, it will be appreciated by physicians, However, as mentioned in the discussion, further clinical studies by physicians are needed to translate its findings into the clinic.
• The author of this review works as physician and often deals with liver metastasis. It is one field of focus of her/his research.

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 study Dr. Sitia's group investigated the effect of IFNα1 as perioperative agent preventing liver metastasis formation of colorectal carcinoma (CRC). To this end, various mouse models were used such as liver colonization models, i.e. intrasplenic and mesenterial injections of MC38 and CT26 CRC cell lines. Besides, spontaneous metastasis of CRC was analyzed by orthotopic injection of MC38 into the cecum. To study the influence of IFNα1 in these settings mini-osmotic pumps releasing IFNα1 were used. Moreover, conditional mouse models with a cell-type specific deficiency of Ifnar1 were compared. Altogether, the application of IFNα1 led to a reduction in liver colonization of CRC in all models studied. This was ascribed to decreased trans-sinusoidal migration of CRC and increased cross-priming by LSEC entailing in T cell activation.

Major comments:

Overall the study is well performed and the major conclusions seem to be drawn well. However, there are certain points I like to address:

• First, the authors started their experiments with MC38 and CT26 CRC cell lines. At the end they just applied MC38. The rational behind this should be clearly stated. Second, as in their previous publication (Catarinella et al, 2016) F1 hybrids of C57BL/6 x BALB/c mice were used for the experiments. However, I believe that the genetic heterogeneity might be strongly increased by this approach which might lead to difficult reproducibility of the results.
• At page 16 the authors conclude that "patients suffering from chronic liver fibrotic disease... display lower incidence of hepatic metastases". In the community there is contradictory data (see Kondo et al, BJC, 2016, https://www.nature.com/articles/bjc2016155). This should be precisely discussed, otherwise this claim should be removed.
• In the discussion section the interplay of other cell types within the hepatic niche should be stated. For example, in Toyoshima's study a direct anti-tumoral effect of dendritic cells releasing IFNα1 was demonstrated (see Toyoshima et al, Cancer Immunol Res, 2019, https://aacrjournals.org/cancerimmunolres/article/7/12/1944/469540/IL6-Modulates-the-Immune-Status-of-the-Tumor). This further strengthens your data.
• Last, multiple times the authors write about data that is "not shown". Please either include these data in the manuscript or delete corresponding phrases because it is not possible for the reader to scrutinize it.
• Besides, I suggest additional experiments further substantiating the study:
• To see if this effect of IFNα1 is cell type-specific liver metastasis of other solid tumors such as breast cancer or melanoma should be investigated.
• The authors applied a broad range of cell type-specific mice. However, a thorough characterization of the deletion of Ifnar1 in the corresponding cell types is missing. This is crucial for the manuscript.
• The capillarization of the hepatic vascular niche is a crucial point in this story. I believe that the hepatic endothelium should be further characterized by additional vascular markers.
• Last, the data and methods appear adequately presented and experiments seem to be reproducible. Just in Figure 4 the exact number of mice and replicates are not clearly presented. Otherwise, everything is fine.

Minor comments:

Overall the text and figures are accurately presented. However, I would like to add further minor comments:

• In Fig. 1 you present the IFNα dosing regimen. How do you explain the decrease in serum IFNα after day 2? Besides, the data points at day 0 should be excluded since measuring startet from day 2! Why did you decide to treat for seven days until the start of the experiment? One could think 2 days might already be enough.
• Fig. 2: Did you check for metastases in other organs than the liver at the timepoint of euthanization, e.g. lungs. In the discussion section you talk about a potential influence of IFNα1 on other organs. Therefore, I think that the mice should be thoroughly analyzed and the data presented. The manuscript will benefit from it.
• Overall, MRI pictures and pictures of IHC or IF are sometimes too small to see. Please provide pictures with larger magnification or enlarge the images.
• Fig. 3 F, G: immune cell infiltration in the liver was analyzed. Please compare it to untreated, tumor-free wildtype liver tissue.
• Fig. 6: the graphs are too small to be read, especially the volcano plot and the gene names of the heatmap.
• Fig. S6: Pictures of co-immunofluorescences are presented. For the reader it is really hard to distinguish the stainings and to identify colocalized areas. Please provide pictures with one channel to better compare the marker expression.
• From page 8 onwards (section about transgenic mice) LSEC was used as kind of synonym for hepatic endothelial cells. Since there is still no LSEC-specific driver mouse, it should be stated "hepatic endothelial cells" instead.
• P. 11: there is a typo: Fig. Fig. S6G,H
• P. 13: the authors describe Gata4 as inhibitor of subendothelial matrix deposition. This should be precisely written, since Gata4 originally is described as master-regulator of liver sinusoidal differentiation which leads to liver fibrosis development upon loss of Gata4. Besides, I came across a study of the same group that investigated the role of Notch signaling in hepatic CRC and melanoma metastasis (Wohlfeil et al, Cancer Res, 2019, https://aacrjournals.org/cancerres/article/79/3/598/638600/Hepatic-Endothelial-Notch-Activation-Protects). Similar to your study they tie the reduction in hepatic metastasis to capillarization of the hepatic microvasculature.
• The discussion reads like paraphrasing the results section. The manuscript would clearly benefit if the discussion section had been rewritten short and concisely.

Significance

• Since liver metastases of various tumor are tremendously hard to treat and mediates therapy resistance, the authors focus on a very important field of research - prevention of liver metastasis formation.
• This study adds insights into the mechanisms of action of IFNα1 in the hepatic microenvironment. It extends previous findings of Toyoshima who described anti-tumoral effects of IFNα1 released by dendritic cells in the liver.
• The study is well designed and will be of great interest for the scientific community. Besides, it will be appreciated by physicians, However, as mentioned in the discussion, further clinical studies by physicians are needed to translate its findings into the clinic.
• The author of this review works as physician and often deals with liver metastasis. It is one field of focus of her/his research.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Tran et al. describes the mechanism by which IFNa treatment prevents the development of liver CRC metastasis in several mouse models. They show how continuous administration of IFNa strength liver vascular barrier by a direct effect on endothelial cells and avoids the trans-sinusoidal migration of tumour cells.

Major points:

1. Authors use an elegant orthotopic model of liver metastasis to confirm the effect of continuous IFNa on hepatic colonization (Fig.3). Although they extensively characterize the metastatic lesions, they do not show data on the potential impact of IFNa treatment in the primary caecum tumour. Authors should clarify if the described effects are taken place in the liver or/and in the caecum. It would be interesting to show if IFNa affects the primary tumour size, the extravasation of cancer cells and the immune infiltration since all these factors could have an impact in the number of liver lesions.
2. Figure 3f right shows liver images without any obvious metastatic lesion. Since authors are analysing the effect of IFNa treatment in proliferation, vascularization and immune composition in liver tumours, they may show and quantify images with metastatic lesions and restrict the analysis to the tumour area.
3. Authors analyse the recombination efficiency of different mouse CRE lines by non-quantitative methods (PCR of hepatic genomic DNA and GFP expression by immunofluorescence in healthy liver). Since PDGFRβ-Cre/ERT2 and CD11c-Cre lines are used to exclude a role of IFNa on the targeted cells, authors should provide stronger evidences to support this. They may consider studding the ablation of Ifnar1 in FACS sorted fibroblasts and myeloid cells. Moreover, it would be important showing the proportion of GFP+ cells in the sorted populations to understand how broadly these stromal populations are targeted.
4. Ifnar1 ablation in VeCad+ cells prevents the effect of IFNa on tumour growth (Fig. 4d), suggesting the existence of anti-tumour mechanisms beyond the effects on hepatic colonization. Authors may consider checking proliferation, vascularization and immune infiltration in these tumours to enhance their conclusion.
5. Immune properties of LSECs are analysed in vivo by using a mouse CRE line that targets all endothelial cells, including those ones located in lymphoid organs, and evaluating T cell composition in the spleen. I found difficult to conclude that these properties are exerted directly by LSECs and not by other endothelial cells in vivo. To clarify the local effect of LSECs in modulating anti-tumour immunity, T cell composition and activation should be checked in tumours shortly after tamoxifen administration.

Significance

The conclusions of this study are consistent with previously published literature and the biological insights are potentially useful to the cancer biology community.

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Referee #2

Evidence, reproducibility and clarity

The authors use soft X-ray tomography to examine cell structure following infection by herpes simplex virus-1 (HSV-1). This imaging method can provide 3D images of cryo-preserved intact cells without chemical fixation or staining. The authors find several morphological differences between uninfected and infected cells, including changes in the number and size of vesicles and in the size and shape of mitochondria.

This is a well-done study with careful and extensive analysis that in general produces convincing images to support the authors' conclusions. The procedures are clearly described and reproducible, and the authors have examined an impressive number of images and have performed appropriate statistical analyses.

I had two comments / suggestions regarding the findings about changes in morphology after infection. First, in the Discussion, the authors consider the possibility of Golgi fragmentation. Can the authors test this by counting Golgi before and after fragmentation? Second, in the Results the authors report that they did not observe a change in lipid droplets after infection. However, the late-stage image in Fig. 5A seems to show such a change, with the lipid droplets becoming larger and darker relative to the early stage or uninfected cells. Maybe this is just the particular image that was selected, but perhaps it is worth looking at more images by eye just in case the segmentation procedure somehow missed this change.

Minor comments:

Line 127 - As I understand it, the alignment by fiducial markers corrects primarily for small inaccuracies in tilting of the stage. Hopefully there are not significant vibrations in the microscope because this would also lead to loss of resolution during the exposure of each tilt angle.

Line 145 - "electron light" Is this common usage? To me it seems more accurate to just say electrons because light to me means photons.

Line 390 - detection OF ("of" is missing)

Line 564 - Fig. 2 legend. "partial retention in the nucleus of U2OS cells". I am not sure where the nucleus is in the images. To me, it looks like there is almost no stain for ICP0 in hTERT at stage 1 and stage 3, and then cytoplasmic stain at stage 2 and stage 4. In contrast, for U2OS, the stain looks mostly nuclear until stage 4 when it is partially cytoplasmic. This all needs to be better explained, and perhaps arrows added to the images such that the reader does not have to guess.

Line 585 - The authors could consider rotating the images by 180{degree sign} in panel A (late) in order to maintain the same orientation of nucleus and cytoplasm. This would make it easier for readers to see the point.

Line 614 - I could not find the length of the scale bar in the legend.

Significance

The significance of the study is two-fold. First, it is a nice technical demonstration of what can be accomplished using soft X-ray tomography. I am qualified to evaluate this, since my expertise is in biological applications of this technique. The second significant aspect of the study is the demonstration of morphological changes in mitochondria and vesicles. I am not a virologist, so I do not know the literature on this point with regard to virus infection, but I find it interesting that the authors were able to detect such changes.

I believe the authors should cite a couple of papers:

10.1016/j.cell.2015.11.029 which looks at HSV infection and reports viral particles between the inner and outer nuclear membrane. 10.1016/j.jsb.2011.11.025 which also reports nuclear membrane separations or bulges by soft X-ray tomography.

Regarding these nuclear membrane bulges, there are a number of papers that show they can also arise from mutations in nuclear-lamin associated proteins like nesprin and SUN (see for example https://doi.org/10.1093/hmg/ddm338). This is perhaps something interesting for the authors to think about, but not necessary for the current manuscript.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their careful and constructive analysis of our work. Our manuscript aims to exemplify the use of cryo-soft-X-ray tomography (cryoSXT) as a technique to study the dynamic changes to host-cell morphology that accompanies virus infection. This emerging method has several strengths when compared to other ultrastructural analysis techniques. Specifically, cryoSXT does not require the addition of contrast agents and therefore samples can be prepared via plunge cryopreservation alone, allowing us to capture them in a near-native state. Furthermore, the penetrating power of soft X rays and large field of view in cryoSXT allow rapid data acquisition, facilitating quantitative analysis of 10s to 100s of individual cells. We combined high-throughput cryoSXT data collection with semi-automated tomogram segmentation and fluorescence cryo-microscopy to study a recombinant herpes simplex virus (HSV)-1 that produces a pattern of fluorescence indicative of the stage of the infection in a single cell (‘timestamp’ HSV-1) and quantitatively monitored changes in lipid droplet, vesicle and mitochondrial morphology as HSV-1 infection progresses. In response to the reviewers’ comments, we have expanded our analysis of lipid droplet morphology, identifying a transient increase in the size of lipid droplets at early stages of HSV-1 infection, and completed additional fluorescence microscopy analysis to support our statements about the changes to microtubule, mitochondrial and Golgi morphology that accompany infection. Furthermore, we have included additional discussion on the relative merits of cryoSXT versus other ultrastructural analysis techniques like transmission electron microscopy, electron cryo-microscopy and electron cryotomography. We believe that our study serves as a powerful example of how cryoSXT can be used for quantitative cell biology and will be of broad interest to an audience of cell biologists and colleagues who study infection processes.

1. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

The authors have performed an explorative study, investigating morphological changes that occur in cells upon infection with Herpes Simplex Virus 1 (HSV-1) by the use of cryo soft X-ray tomography (cryoSXT). cryoSXT is an emerging technique for imaging of biological material, that allows for 3D imaging of significant volumes of cells under near-native conditions, without the need for sectioning or sample preparation other than rapid freezing. Reference (Groen et al. 2019) provides a nice list of examples from various biological samples. By the use of cryoSXT, the authors confirm findings that they have previously published by use of light and expansion microscopy (ref 16 from manuscript), namely an enrichment of small vesicles close to the nucleus and elongation and branching of mitochondria into interconnected networks in infected cells.

Infection experiments were done in two different cell types in this study (HFF and U2OS), and a timestamp reporter virus that allows to distinguish between early and late stages of infection was used to provide more context to the observed morphological changes in the cells.

Major comments

It is a bit difficult to follow the main message throughout the manuscript, as the topics brought up in the introduction, results and discussion sections are not very coherent. The introduction gives some background on the virus and the timestamp reporter system, and further focuses on cryoSXT as a method and how this can overcome sample preparation artefacts that might be introduced by chemical fixation and sample processing. The results do not contain any direct comparisons between cryoSXT and other methods or sample preparations (light microscopy or EM-based), and the discussion only to a small extent comes back to the advantages brought by cryoSXT compared to other methods. Rather the discussion largely revolves around the possible involvement of microtubules in generating the observed morphological changes, and the possible meaning of elongated mitochondria in infected cells. Both of these topics are barely introduced, and not at all experimentally interrogated in the case of microtubules. There is also some discussion about Golgi fragmentation, although this is also not directly interrogated by cryoSXT in the current manuscript.

We thank the reviewer for these comments. We have: - Updated the introduction to enunciate more clearly the aims of our study - Included a substantial comparison of the relative merits of cryoSXT versus other ultrastructural analysis techniques (TEM, cryoEM and cryoET) in the discussion - Updated the introduction to introduce the concepts of microtubule and mitochondrial morphology changes during infection that are covered in depth in the discussion - Included additional microscopy experiments, including super-resolution structured illumination microscopy (SIM), to demonstrate the changes in Golgi (Figures 6 and 7), microtubule (Figure 8) and mitochondrial (Suppl. Figure 4) morphology that accompany HSV-1 infection. These additional experiments support the hypotheses presented in the submitted manuscript, namely that microtubule organising centres are disrupted, Golgi membranes dispersed, and mitochondria redistributed as HSV-1 infection progresses.

The authors perform imaging with a 40nm or a 25nm zone plate, where the 25nm zone plate provides improved resolution of a smaller volume compared to the 40nm zone plate. The authors do not really make use of the improved resolution offered by the 25nm zone plate in the results, so the motivation for turning to this (and therefor also changing cell line) is a bit unclear. The reason for the U2OS cell line to better preserved during X ray imaging is also not discussed, maybe it has to do with the thickness of the cells (as the U2OS cells are very flat). Furthermore, images from the 25 nm zone plate are not compared side by side to neither the 40nm zone plate nor standard TEM, which makes it hard to judge what the increased resolution really brings.

Only one zone plate can be installed at any one time in the microscope and altering the zone plates requires extensive hardware changes that are outside the control of beamline users. We agree that this was not clearly discussed in the text. We have included additional text in the results (lines 207–208) and methods (lines 633–638) explaining this operational limitation and clarifying which zone plate was used for which experiment. In this study we observed that tomograms acquired with the 25 nm zone plate did not provide significantly more biological information than with the 40 nm zone plate, and thus both are suitable for characterisation of overarching cellular ultrastructural changes that accompany infection. We have added a sentence to this effect to the discussion (lines 410–412). Like U2OS cells, HFF-hTERT cells are also very flat. They appear more robust compared to HFFs when used for protracted exposures to soft X-rays and less likely to suffer from heat deposition after an extensive data collection round. We can speculate at this point that this could conceivably be due to the particular chemical composition of the intracellular environment in different cell lineages but it is impossible to offer anything other than speculation and therefore we have refrained from commenting further on this in the manuscript.

The switch from a 40 to a 25nm zone plate required a switch in the model system, as mentioned above. The chosen cell types are not linked to biological relevance however (neurons and epithelial cells are mentioned as relevant cell types in the introduction), and it is therefor a bit unclear what the relevance is of keeping results from both cell types and comparing the two, rather than sticking to the one that works with cryoSXT. The results from the U2OS cells could still be compared by LM to the HFF cells if this contributes to the aim of the study.

U2OS cells were chosen because they have been used previously for studies of HSV-1 infection (references 55–56) and are known to be well suited to cryoSXT analysis (references 32–33). We have added a sentence to this effect to the results (lines 208–211).

The distribution of the viral proteins of the timestamp reporter virus is used to categorize infected HFF cells into 4 infection stages. In the U2OS cells the protein distribution is a bit different, which only allows them to be categorized into early (stage 1+2) and late (stage 3+4) stage of infection. Although this is what the authors state in the text, all 4 stages are included in Fig.2 for the U2OS cells, so it is not clear how this subdivision is performed and it does not seem like an accurate representation of the data. Furthermore, the uninfected population is not included in the timecourse, and there is not really a gradual change in infection states over the different timepoints as one could have expected. Therefor it is a bit hard to see the relevance of the timecourse. In the paper where the reporter virus is published (ref 16), shorter infection times were used, which leads to a more gradual change in infection stages.

We thank the reviewer for pointing out these omissions. We have updated Figure 2A to only show the categories early (stage 1+2) and late (stage 3+4) for the U2OS cells. Furthermore, we have repeated the infection time course experiment, quantitating uninfected cells in addition to infected cells and including additional time points (2-, 4- and 6-hours post-infection). This new data (Figure 2B) demonstrates that the temporal profiles of infection progression are similar in HFF-hTERT and U2OS cells. Furthermore, it supports our choice of 9 hours post-infection as a suitable time point for plunge freezing of samples in order to obtain a mixture of cells at early and late stages of infection.

There is a lot of importance given to the morphological changes of mitochondrial networks in infected cells. However, the quantification represented in Fig.5B is a bit unclear. The mitochondria are classified into different groups, but there is no specific description of the definition and cutoff values of each group. The name of some groups is also confusing, such as "short and long" mitochondria. Furthermore, there are large differences between replicates (suppl. fig. 2). The authors state that some mitochondria are swollen, which they interpret as a sign of apoptosis. They find these swollen mitochondria in 75% of the tomograms of uninfected cells in replicate number 3. If this is indeed cell death this replicate is not healthy.

We apologise that the categorisation of mitochondria was not sufficiently clear in the submitted manuscript. The categories were percentage of tomograms that had the different mitochondrial morphologies present, not percentages of mitochondria. Thus, tomograms with both short and long mitochondria were classified as “short and long”. We have re-generated Figure 5C and Suppl. Figure 2C as a Venn diagram to illustrate this point more clearly. We have also updated the legend of Figure 5C (lines 845–850) to state clearly that the diagram shows percentage of tomograms with the relevant mitochondrial morphologies. The categorisation was performed manually and we have included examples of each category in Figure 5A. Manual classification can be subjective but, given the large number of tomograms analysed and the clear distinction between morphology in uninfected vs early- and late-stage infected cells, we are confident that our results are robust. We note that we have deposited all of the source tomograms in the Apollo repository at the University of Cambridge (https://doi.org/10.17863/CAM.78593); the data we used for this analysis are thus freely available for inspection and re-analysis by interested colleagues. We note that the swollen mitochondria were observed in multiple samples of uninfected and infected cells. This suggests that, regardless of infection, this is a common phenotype of U2OS cells. Others have observed this morphology by EM in the context of apoptosis and suggest it may represent porous mitochondria (reference 61). Although the proportion of tomograms containing these swollen mitochondria were higher in the uninfected sample of replicate 3, the other 25% contained typical mitochondrial morphologies that we could include in our analysis. The presence of inter-cell morphological variability such as this highlights the importance of imaging multiple cells within a population and performing several distinct biological replicates, as we have done in this study, to ensure project-relevant information is captured and delineated from the background structural variability inherent within a cell population. Previous cryoSXT studies had observed (but did not specifically comment on) a similar swollen mitochondrial morphology (reference 59). However, out of an abundance of caution we excluded all tomograms with swollen mitochondria from our analysis of mitochondrial branching (Figure 5C). Moreover, Tukey tests were performed per replicate for each pair of conditions in Figure 5C and statistical significance was reported only if it was observed independently in all three replicates. We are thus confident that any sampling error in replicate 3 that may arise from excluding tomograms will not have meaningfully altered our conclusions.

Minor comments

Results section 1, line 115-117: Where the authors state that it is unclear whether "naked" HSV-1 capsids would be visible by cryoSXT, it would be useful to refer to literature where these are observed by TEM, or to compare to TEM in their own experiments.

We have included references to previous TEM studies in the results (lines 128–129), as requested. However, we note that TEM and cryoSXT are fundamentally different as TEM uses contrast agents whereas contrast in cryoSXT arises from differential elemental densities (in particular the density of oxygen versus carbon or phosphorous). We have updated the results (lines 129–131) to clarify this point.

Results line 143: The authors state that it's hard to observe the perinuclear viruses with TEM, but there are several examples of this in the literature that could be referenced, e.g. (Skepper et al. 2001; Leuzinger et al. 2005; Baines et al. 2007; Johnson and Baines 2011), although this does not mean that they are not hard to find or that 3D is not advantegous.

We thank the reviewer for these references and we have added them to the manuscript.

Fig.4: It is unclear why all the vesicles are open-ended

This is due to the differential path-length of carbon rich (and thus high contrast) membrane traversed by the X-rays for the membranes normal or parallel to the incident X-ray beam. We have clarified this point in the results (lines 290–301).

Some places in the manuscript PFU per cell is used, other places MOI

Thank you for pointing this out. For consistency, we have changed all instances of PFU per cell to MOI.

If some specific adjustments to the methods had to be implemented for bio safely reasons (virus work), this should be stated in the methods.

We have added a section on biosafety measures to the methods (lines 562–568).

Access to the synchrotron should also be described

We have expanded the synchrotron access attribution the Acknowledgments section (lines 737– 738).

Discussion line 320: "consistent with previous research" - there is a reference missing.

Thank you for spotting this. We have now added the reference.

The quantifications are based on a limited number of tomograms, but there is no statement as to how the specific tomograms were selected. With a variability between replicates and tomograms, a random selection is important.

We included all tomograms collected for the relevant experimental condition in all our analyses unless otherwise stated. For the vesicle segmentation we chose four reconstructed tomograms from each condition at random (lines 690–691). For lipid droplet volume analysis and mitochondrial branching analysis we included all tomograms that matched our quality-control criteria. We have added a few sentences to the Segmentation and Graphs and Statistics sections of the methods (lines 691–694 and 724–733) describing our selection criteria for the lipid droplet, vesicle and mitochondrial branching analysis, respectively.

If gold fiducials are visible in the tomograms it could be useful to indicate, as they can look similar to lipid droplets to a non-expert reader.

We have indicated gold fiducials Figure 1 H, the only figure in which they are visible, with a gold star as requested.

Suppl. Fig.2: For clarity it would be good not to use the same color arrows to indicate different things in A and B.

Suppl. Figure 2B has been removed in response to another reviewer request.

Reviewer #1 (Significance):

The authors of this study demonstrate that cells infected by HSV-1 virus can be investigated by the use of cryoSXT, and use this to show that infected cells have more elongated and interconnected mitochondria, and an enrichment of small vesicles close to the nucleus. They thereby also show that cryoSXT offers a nice resolution for characterizing morphological changes in significant volumes of near native-state cells, and that the method offers a promising throughput for screening of large amounts of cells. However, the study does not really present new biological or technical advances compared to previously published literature, see e.g. Müller et.al. 2012, Duke et.al 2014, Perez Berna et.al. 2016, Groen et.al. 2019, Weinhardt et.al. 2020, Loconte et.al. 2021 (not cryo but demonstrates the advantage of capillaries), Kounatidis et.al. 2020, Scherer 2021 (ref 16 from paper), some of which are also referenced in the current study. The study could thus have profited from a more defined focus and possibly further experiments (live-cell imaging, CLEM, TEM, microtubules or more mechanistically focused) depending on the main interest of the authors. The advantage with the current broad focus (assuming that the main concerns are addressed) is that the study could interest a larger audience, ranging from virology, cell biology and immunology to microscopy and methods development.

We thank the reviewer for recognising the broad audience that will be interested in our manuscript. We believe that our analysis highlights the broad applicability of cryoSXT for analysing cell ultrastructure and changes that occur in response to infection. Furthermore, we think that our use of robust numerical analysis to quantitate the phenotypes we observe highlights the strength of cryoSXT as a high throughput technique for ultrastructural analysis. Our study is the first to investigate HSV-1 infection using cryoSXT and, in addition to confirming previous ultrastructural changes observed using other methods, we present new biological insight in organelle architecture and distribution such as that lipid droplets undergo a transient size increase during early stages of infection. We believe that we have demonstrated the robust utility of cryoSXT as a tool to study ultrastructural changes in response to insults, such as infection by intracellular pathogens, and hope that our manuscript will act as inspiration for others seeking to use cryoSXT to image cellular ultrastructure.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors use soft X-ray tomography to examine cell structure following infection by herpes simplex virus-1 (HSV-1). This imaging method can provide 3D images of cryo-preserved intact cells without chemical fixation or staining. The authors find several morphological differences between uninfected and infected cells, including changes in the number and size of vesicles and in the size and shape of mitochondria.

This is a well-done study with careful and extensive analysis that in general produces convincing images to support the authors' conclusions. The procedures are clearly described and reproducible, and the authors have examined an impressive number of images and have performed appropriate statistical analyses.

We thank the reviewer for their positive comments.

I had two comments / suggestions regarding the findings about changes in morphology after infection. First, in the Discussion, the authors consider the possibility of Golgi fragmentation. Can the authors test this by counting Golgi before and after fragmentation?

We did not frequently observe well-defined Golgi apparatuses in our tomograms, consistent with previous cryoSXT studies (reference 61). We therefore performed new experiments using SIM microscopy to demonstrate the disruption of Golgi apparatus and trans-Golgi network in fixed U2OS cells stained with the markers GM130 and TGN46, respectively. These new results are presented in Figures 6 and 7 and in the results (lines 342–355).

Second, in the Results the authors report that they did not observe a change in lipid droplets after infection. However, the late-stage image in Fig. 5A seems to show such a change, with the lipid droplets becoming larger and darker relative to the early stage or uninfected cells. Maybe this is just the particular image that was selected, but perhaps it is worth looking at more images by eye just in case the segmentation procedure somehow missed this change.

We thank the reviewer for suggesting we re-visit the properties of lipid droplets. Based on this suggestion we segmented the lipid droplets from 94 tomograms and found a robust change in the median volume of lipid droplets at early stages of infection. We have included this new data in Figure 4C, Suppl Figure 2 and the text of the results (lines 302–312). The observation that lipid droplet volumes change is particularly interesting as another group recently observed similar changes in lipid droplets in response to HSV-1 infection of astrocytes and they postulate that this may modulate the cellular immune response (reference 85). Our data support and extend their conclusions, as described in the discussion (lines 476–494).

Minor comments:

Line 127 - As I understand it, the alignment by fiducial markers corrects primarily for small inaccuracies in tilting of the stage. Hopefully there are not significant vibrations in the microscope because this would also lead to loss of resolution during the exposure of each tilt angle.

Thank you, we have corrected “vibrations” to “small inaccuracies in tilting of the microscope stage”.

Line 145 - "electron light" Is this common usage? To me it seems more accurate to just say electrons because light to me means photons.

Thank you, we have corrected “electron light” to “electrons”.

Line 390 - detection OF ("of" is missing)

Thank you, we have made the correction.

Line 564 - Fig. 2 legend. "partial retention in the nucleus of U2OS cells". I am not sure where the nucleus is in the images. To me, it looks like there is almost no stain for ICP0 in hTERT at stage 1 and stage 3, and then cytoplasmic stain at stage 2 and stage 4. In contrast, for U2OS, the stain looks mostly nuclear until stage 4 when it is partially cytoplasmic. This all needs to be better explained, and perhaps arrows added to the images such that the reader does not have to guess.

We agree and have added a silhouette around each nuclei in Figure 2 to make this clearer. We have also added arrows to indicate the gC-mCherry enriched juxtanuclear compartment in cells at stage 3 (HFF-hTERT) or a late stage (U2OS) of infection.

Line 585 - The authors could consider rotating the images by 180{degree sign} in panel A (late) in order to maintain the same orientation of nucleus and cytoplasm. This would make it easier for readers to see the point.

Done as requested.

Line 614 - I could not find the length of the scale bar in the legend.

We apologise for omitting this – is has now been added.

Reviewer #2 (Significance):

The significance of the study is two-fold. First, it is a nice technical demonstration of what can be accomplished using soft X-ray tomography. I am qualified to evaluate this, since my expertise is in biological applications of this technique. The second significant aspect of the study is the demonstration of morphological changes in mitochondria and vesicles. I am not a virologist, so I do not know the literature on this point with regard to virus infection, but I find it interesting that the authors were able to detect such changes.

We thank the reviewer for their positive assessment of our work.

I believe the authors should cite a couple of papers:

10.1016/j.cell.2015.11.029 which looks at HSV infection and reports viral particles between the inner and outer nuclear membrane.

We have included a citation to this work as requested (lines 162–165).

10.1016/j.jsb.2011.11.025 which also reports nuclear membrane separations or bulges by soft X-ray tomography.

We have elaborated on this section and incorporated the reference as requested (lines 265– 276).

Regarding these nuclear membrane bulges, there are a number of papers that show they can also arise from mutations in nuclear-lamin associated proteins like nesprin and SUN (see for example https://doi.org/10.1093/hmg/ddm338). This is perhaps something interesting for the authors to think about, but not necessary for the current manuscript.

Thank you for this comment. We did consider studying the breakdown of the nuclear lamina during HSV-1 infection, as this has been shown in previous studies [e.g. 10.1101/2021.06.02.446771]. However, we could not robustly resolve the nuclear lamina from the nuclear envelope in uninfected cells. The nuclear lamina is quite thin (30–100 nm in width) and this may have confounded its identification.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The manuscript by Nahas et al. describes the structural studies performed in U2OS cells infected with a recombinant HSV-1 virus that enables tracing the stage of the infection using fluorescent markers. This system was used to determine major structural changes in HSV-1 infected cells using cryo-soft X ray tomography (cryo-SXT) on near native-state samples. The data presented complement previous studies (particularly ref.16) using similar reagents but different microscopy techniques. While the data are generally well presented and discussed, they do not provide any substantially novel information on the structural changes in HSV-1. Nevetheless, they constitute an interesting technical achievement.

We thank the reviewer for supporting the technical quality of the analysis. In response to the comments of another reviewer we have extended our analysis and documented new biological information for this system relating to lipid droplet re-shaping and distribution in response to HSV-1 infection; all our new findings are included in the updated manuscript.

Major comments:

There are no major concerns on the data, although some of the statements could be revised for a more realistic interpretation of the results.

• In Figure 1F and lines 152-156 it is stated that a bulging of the nuclear envelope occurs around some of the putative particles, while in lines 243-244 and lines 625-628, it is stated that bulging occurs both in mock and infected cells. This should be clarified to avoid confusion. It is possible that authors differentiate both situations and this should be more clearly stated.

Many thanks for identifying a possible area of confusion. We have updated the results to clearly distinguish the expansion of the perinuclear space that accompanies virus nuclear egress (lines 160–175) from the bulges of the nuclear envelope that are observed in uninfected and infected cells (lines 265–276).

• The statistical tests are different for different hypothesis testing throughout the manuscript. The authors should justify in the methods section the use of one or another test. This will contribute to clarity in the hypothesis that is being test and will clarify the reason for the selected test.

We have significantly expanded the Graphs and Statistics section of the methods (lines 703– 734) to further justify the statistical tests used throughout our study.

• Sentence: "Our observation..." in lines 349-352. Even though the sentence is in the Discussion it is wildly speculative. The authors could use different approaches to tackle experimentally the question of whether active fusion or faulty fission is involved, but this is not the main subject the manuscript. Please revise the sentence or address experimentally, this would provide new insight into the impact of HSV-1 infection on mitochondrial network morphology. This sentence could be qualified as "speculative".

We agree that this section of the discussion strayed into speculative territory and have removed it from the updated manuscript.

• Although ref.16 provides evidence supporting Golgi fragmentation and mitochondrial elongation after HSV-1_timestamp virus infection in HFF cells, it would be important to show confocal microscopy data in U2OS cells, which were used for cryo-SXT, particularly since the authors refer differential virus kinetics and subcellular distribution of viral antigens in these cells. These would greatly contribute to support the statements regarding these two phenomena. It is very likely that the authors already have the data and could easily show them.

We have included new microscopy experiments to demonstrate changes in mitochondrial (Suppl. Figure 4) and Golgi (Figures 6 and 7) morphology that accompany HSV-1 infection, and these new experiments are now included in the results (lines 335–310 and 342–355).

-Line 269: Apposition of lipid droplets and mitochondria is not thoroughly described. This statement requires quantitation. Optimally, confocal imaging using Mitotracker and bodipy493/503 or superresolution imaging using specific antibodies may also contribute to strengthen the statement.

We agree with the reviewer that we do not at this stage have adequate data to support this assertion and have therefore removed it from the manuscript.

• It would be of great interest to document the budding events observed by cryo-SXT using higher resolution techniques and the kinetic resolution provided by the fluorescent infection fiducials. This would confirm the nature of the particles (using immunogold) and would demonstrate the the usefulness of the cryo-SXT data. This by itself would justify the use of cryo-SXT to temporally locate events that are difficult to visualize otherwise (as stated by the authors).

We agree with the reviewer that a correlative imaging strategy involving cryoSXT and fluorescence microscopy could aid in identifying features of infection, and have highlighted this interesting future direction in the discussion (line 406–409). However, performing such analysis will be a substantial experimental commitment in its own and is outside the scope of our current manuscript.

Minor comments:

• Given that the software used for segmentation (Contour) is not published, a minimal comparative description between manual and semi-automated segmentation may be shown in the supplementary, to illustrate the robustness of the new method and the reliability of the measurements.

We have now published a preprint (recently accepted in the journal Biological Imaging) that describes Contour in detail, which we have referenced in the updated manuscript: Nahas, K. L., Ferreira Fernandes, J., Crump, C., Graham, S. C. & Harkiolaki, M. (2021) Contour, a semi-automated segmentation and quantitation tool for cryo-soft-X-ray tomography. http://biorxiv.org/lookup/doi/10.1101/2021.12.03.470962

• Lines 278-280: statistical test and p value are not shown.

We have updated the text to include details of the statistical test and p value as requested (lines 326–330 of the updated manuscript).

• After line 376: It would be interesting to mention that transient elongation of mitochondria is observed during dengue virus infection (https://doi.org/10.1016/j.chom.2016.07.008) and that this has also consequences for innate immunity against viruses.

We thank the reviewer for this suggestion, which we have incorporated into the discussion (lines 522–523).

• Given that HSV-1 is a BSL-2 level virus and that a recombinant version (GMO) has been used in the study, the authors should describe the biosafety measures taken to image non-inactivated infectious samples by cryo-SXT. The authors should state that a biosafety committee has reviewed these activities.

We have included a Biosafety Measures section to the methods (lines 562–568) that details the biosafety measures used and their approval by the relevant committees.

Reviewer #3 (Significance):

This study constitutes an incremental technical advance in the study of HSV-1 infection. The broad context and the quasi-native structure of the cells enables documenting events that are difficult to observe thin sections for TEM.

This study is one of the few examples of the use of cryo-SXT for infected cell imaging. Other examples of the literature are cited as well as previous structural studies performed with higher resolution techniques.

The manuscript may be suitable for HSV-1 specialists and cell biologists interested in using near-native samples for gross cellular imaging and documentation of low-resolution maps revealing alterations in large subcellular structures.

We thank the reviewer for highlighting that ours is one of only a few comprehensive studies using cryoSXT, illustrating how it can be used to image cellular processes that are hard to ‘catch’ using techniques that require ultra-thin sectioning, and as such that it will be of interest to cell biologists studying infection processes in cellulo.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript by Nahas et al. describes the structural studies performed in U2OS cells infected with a recombinant HSV-1 virus that enables tracing the stage of the infection using fluorescent markers. This system was used to determine major structural changes in HSV-1 infected cells using cryo-soft X ray tomography (cryo-SXT) on near native-state samples. The data presented complement previous studies (particularly ref.16) using similar reagents but different microscopy techniques. While the data are generally well presented and discussed, they do not provide any substantially novel information on the structural changes in HSV-1. Nevetheless, they constitute an interesting technical achievement.

Major comments:

There are no major concerns on the data, although some of the statements could be revised for a more realistic interpretation of the results.

• In Figure 1F and lines 152-156 it is stated that a bulging of the nuclear envelope occurs around some of the putative particles, while in lines 243-244 and lines 625-628, it is stated that bulging occurs both in mock and infected cells. This should be clarified to avoid confusion. It is possible that authors differentiate both situations and this should be more clearly stated.
• The statistical tests are different for different hypothesis testing throughout the manuscript. The authors should justify in the methods section the use of one or another test. This will contribute to clarity in the hypothesis that is being test and will clarify the reason for the selected test.
• Sentence: "Our observation..." in lines 349-352. Even though the sentence is in the Discussion it is wildly speculative. The authors could use different approaches to tackle experimentally the question of whether active fusion or faulty fission is involved, but this is not the main subject the manuscript. Please revise the sentence or address experimentally, this would provide new insight into the impact of HSV-1 infection on mitochondrial network morphology. This sentence could be qualified as "speculative".
• Although ref.16 provides evidence supporting Golgi fragmentation and mitochondrial elongation after HSV-1_timestamp virus infection in HFF cells, it would be important to show confocal microscopy data in U2OS cells, which were used for cryo-SXT, particularly since the authors refer differential virus kinetics and subcellular distribution of viral antigens in these cells. These would greatly contribute to support the statements regarding these two phenomena. It is very likely that the authors already have the data and could easily show them. -Line 269: Apposition of lipid droplets and mitochondria is not thoroughly described. This statement requires quantitation. Optimally, confocal imaging using Mitotracker and bodipy493/503 or superresolution imaging using specific antibodies may also contribute to strengthen the statement.
• It would be of great interest to document the budding events observed by cryo-SXT using higher resolution techniques and the kinetic resolution provided by the fluorescent infection fiducials. This would confirm the nature of the particles (using immunogold) and would demonstrate the the usefulness of the cryo-SXT data. This by itself would justify the use of cryo-SXT to temporally locate events that are difficult to visualize otherwise (as stated by the authors).

Minor comments:

• Given that the software used for segmentation (Contour) is not published, a minimal comparative description between manual and semi-automated segmentation may be shown in the supplementary, to illustrate the robustness of the new method and the reliability of the measurements.
• Lines 278-280: statistical test and p value are not shown.
• After line 376: It would be interesting to mention that transient elongation of mitochondria is observed during dengue virus infection (https://doi.org/10.1016/j.chom.2016.07.008) and that this has also consequences for innate immunity against viruses.
• Given that HSV-1 is a BSL-2 level virus and that a recombinant version (GMO) has been used in the study, the authors should describe the biosafety measures taken to image non-inactivated infectious samples by cryo-SXT. The authors should state that a biosafety committee has reviewed these activities.

Significance

This study constitutes an incremental technical advance in the study of HSV-1 infection. The broad context and the quasi-native structure of the cells enables documenting events that are difficult to observe thin sections for TEM.

This study is one of the few examples of the use of cryo-SXT for infected cell imaging. Other examples of the literature are cited as well as previous structural studies performed with higher resolution techniques.

The manuscript may be suitable for HSV-1 specialists and cell biologists interested in using near-native samples for gross cellular imaging and documentation of low-resolution maps revealing alterations in large subcellular structures.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors have performed an explorative study, investigating morphological changes that occur in cells upon infection with Herpes Simplex Virus 1 (HSV-1) by the use of cryo soft X-ray tomography (cryoSXT). cryoSXT is an emerging technique for imaging of biological material, that allows for 3D imaging of significant volumes of cells under near-native conditions, without the need for sectioning or sample preparation other than rapid freezing. Reference (Groen et al. 2019) provides a nice list of examples from various biological samples. By the use of cryoSXT, the authors confirm findings that they have previously published by use of light and expansion microscopy (ref 16 from manuscript), namely an enrichment of small vesicles close to the nucleus and elongation and branching of mitochondria into interconnected networks in infected cells.

Infection experiments were done in two different cell types in this study (HFF and U2OS), and a timestamp reporter virus that allows to distinguish between early and late stages of infection was used to provide more context to the observed morphological changes in the cells.

Major comments

It is a bit difficult to follow the main message throughout the manuscript, as the topics brought up in the introduction, results and discussion sections are not very coherent. The introduction gives some background on the virus and the timestamp reporter system, and further focuses on cryoSXT as a method and how this can overcome sample preparation artefacts that might be introduced by chemical fixation and sample processing. The results do not contain any direct comparisons between cryoSXT and other methods or sample preparations (light microscopy or EM-based), and the discussion only to a small extent comes back to the advantages brought by cryoSXT compared to other methods. Rather the discussion largely revolves around the possible involvement of microtubules in generating the observed morphological changes, and the possible meaning of elongated mitochondria in infected cells. Both of these topics are barely introduced, and not at all experimentally interrogated in the case of microtubules. There is also some discussion about Golgi fragmentation, although this is also not directly interrogated by cryoSXT in the current manuscript.

The authors perform imaging with a 40nm or a 25nm zone plate, where the 25nm zone plate provides improved resolution of a smaller volume compared to the 40nm zone plate. The authors do not really make use of the improved resolution offered by the 25nm zone plate in the results, so the motivation for turning to this (and therefor also changing cell line) is a bit unclear. The reason for the U2OS cell line to better preserved during X ray imaging is also not discussed, maybe it has to do with the thickness of the cells (as the U2OS cells are very flat). Furthermore, images from the 25 nm zone plate are not compared side by side to neither the 40nm zone plate nor standard TEM, which makes it hard to judge what the increased resolution really brings.

The switch from a 40 to a 25nm zone plate required a switch in the model system, as mentioned above. The chosen cell types are not linked to biological relevance however (neurons and epithelial cells are mentioned as relevant cell types in the introduction), and it is therefor a bit unclear what the relevance is of keeping results from both cell types and comparing the two, rather than sticking to the one that works with cryoSXT. The results from the U2OS cells could still be compared by LM to the HFF cells if this contributes to the aim of the study.

The distribution of the viral proteins of the timestamp reporter virus is used to categorize infected HFF cells into 4 infection stages. In the U2OS cells the protein distribution is a bit different, which only allows them to be categorized into early (stage 1+2) and late (stage 3+4) stage of infection. Although this is what the authors state in the text, all 4 stages are included in Fig.2 for the U2OS cells, so it is not clear how this subdivision is performed and it does not seem like an accurate representation of the data. Furthermore, the uninfected population is not included in the timecourse, and there is not really a gradual change in infection states over the different timepoints as one could have expected. Therefor it is a bit hard to see the relevance of the timecourse. In the paper where the reporter virus is published (ref 16), shorter infection times were used, which leads to a more gradual change in infection stages.

There is a lot of importance given to the morphological changes of mitochondrial networks in infected cells. However, the quantification represented in Fig.5B is a bit unclear. The mitochondria are classified into different groups, but there is no specific description of the definition and cutoff values of each group. The name of some groups is also confusing, such as "short and long" mitochondria. Furthermore, there are large differences between replicates (suppl. fig. 2). The authors state that some mitochondria are swollen, which they interpret as a sign of apoptosis. They find these swollen mitochondria in 75% of the tomograms of uninfected cells in replicate number 3. If this is indeed cell death this replicate is not healthy.

Minor comments

Results section 1, line 115-117: Where the authors state that it is unclear whether "naked" HSV-1 capsids would be visible by cryoSXT, it would be useful to refer to literature where these are observed by TEM, or to compare to TEM in their own experiments.

Results line 143: The authors state that it's hard to observe the perinuclear viruses with TEM, but there are several examples of this in the literature that could be referenced, e.g. (Skepper et al. 2001; Leuzinger et al. 2005; Baines et al. 2007; Johnson and Baines 2011), although this does not mean that they are not hard to find or that 3D is not advantegous.

Fig.4: It is unclear why all the vesicles are open-ended

Some places in the manuscript PFU per cell is used, other places MOI

If some specific adjustments to the methods had to be implemented for bio safely reasons (virus work), this should be stated in the methods.

Access to the synchrotron should also be described

Discussion line 320: "consistent with previous research" - there is a reference missing.

The quantifications are based on a limited number of tomograms, but there is no statement as to how the specific tomograms were selected. With a variability between replicates and tomograms, a random selection is important.

If gold fiducials are visible in the tomograms it could be useful to indicate, as they can look similar to lipid droplets to a non-expert reader.

Suppl. Fig.2: For clarity it would be good not to use the same color arrows to indicate different things in A and B.

Significance

The authors of this study demonstrate that cells infected by HSV-1 virus can be investigated by the use of cryoSXT, and use this to show that infected cells have more elongated and interconnected mitochondria, and an enrichment of small vesicles close to the nucleus. They thereby also show that cryoSXT offers a nice resolution for characterizing morphological changes in significant volumes of near native-state cells, and that the method offers a promising throughput for screening of large amounts of cells. However, the study does not really present new biological or technical advances compared to previously published literature, see e.g. Müller et.al. 2012, Duke et.al 2014, Perez Berna et.al. 2016, Groen et.al. 2019, Weinhardt et.al. 2020, Loconte et.al. 2021 (not cryo but demonstrates the advantage of capillaries), Kounatidis et.al. 2020, Scherer 2021 (ref 16 from paper), some of which are also referenced in the current study. The study could thus have profited from a more defined focus and possibly further experiments (live-cell imaging, CLEM, TEM, microtubules or more mechanistically focused) depending on the main interest of the authors. The advantage with the current broad focus (assuming that the main concerns are addressed) is that the study could interest a larger audience, ranging from virology, cell biology and immunology to microscopy and methods development.

Reviewers expertise

Electron microscopy, volume EM, CLEM, light microscopy, host-pathogen interactions

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Reply to the reviewers

1. General Statements [optional]

We would like to thank the reviewers for their helpful and constructive comments.

2. Point-by-point description of the revisions

Reviewer #1

This reviewer thought our findings would be of interest to a broad range of scientists from both the centrosome and mitosis fields, but noted some important aspects for improvements.

Additional Experiments (we number these points for ease of discussion).

1. • Figure 3. The reviewer points out that because our analysis of Ana2-∆CC and Ana2-∆STAN mutant proteins was conducted in the presence of endogenous WT protein, we should be more cautious in our interpretation.* We agree and apologise for overstating these findings. We have now rewritten the title and text of this section to be more cautious (p11, para.2)

2. Figure 5A. The reviewer wonders whether the reduced recruitment of Sas-6 in the presence of Ana2(12A) is due to reduced binding, and they request we test this biochemically. This is our favoured interpretation, but we have been unable to test this biochemically for two reasons. First, although we have successfully purified several recombinant Sas-6 and/or Ana2 fragments (Cottee et al., eLife, 2015), the full-length proteins are poorly behaved (tending to precipitate, likely due to their inherent ability to self-oligomerise). Thus, we have been unable to reconstitute their interaction in vitro*. Second, as we show here, the proteins are normally expressed in embryos at surprisingly low concentrations (~5-20nM), and we can detect no interaction between them in coimmunoprecipitation experiments from embryo extracts (not shown). Indeed, this concentration is so low that Sas-6 does not even appear to form a homo-dimer in the embryo, even though Sas-6 clearly functions as a homo-dimer in centriole assembly (new Figure S4A). We now explain these points, and state that our favoured hypothesis that Ana2(12A) has reduced affinity for Sas-6 (or other core duplication proteins) remains to be tested (p22, para.2).

3. The Reviewer wonders if all 12 of the potential Cdk1 phosphorylation sites that we mutate in Ana2(12A) are important in vivo, and whether we have tested whether mutating fewer sites (e.g. the two sites [S284/T301] that we show are phosphorylated by Cdk1/Cyclin B in vitro) might be sufficient to recapitulate the Ana2(12A) phenotype. *We have now tested this by mutating just the S284/T301 sites to Alanine [Ana2(2A)], but the results were not very informative (Reviewer Figure 1 [RF1]). Whereas Ana2(12A) is recruited to centrioles for a longer period and to higher levels than WT Ana2 (Figure 4A), Ana2(2A) is recruited to centrioles for a normal period but to lower levels (RF1A,B). The interpretation of this result is complicated because western blots show that Ana2(2A) is also present at lower-levels than normal (RF1B). Thus, it is clear that Ana2(2A) does not recapitulate well the behaviour of Ana2(12A). We have decided not to present this data as it is difficult to interpret and it does not change any of our conclusions.

4. Figure 6. The reviewer asks whether the 12A mutations impair the interaction with Plk4, influence Plk4’s kinase activity or the ability of Plk4 to phosphorylate Ana2. These are excellent questions but, for the same reasons described in point 2 above, we cannot address them biochemically as we cannot purify well-behaved recombinant full-length Ana2 or active Plk4 in vitro, and both proteins are present at such low levels in the embryo that we cannot detect any interaction between them in embryo extracts. We are working hard to reconstitute in vitro* systems to probe these important points, but it may be sometime before we are able to do so.

5. Figure 7. The reviewer suggests that the 12D/E phosphomimetic substitutions introduce more negative charge than the putative phosphorylation of Ser/Thr residues and they ask if the Ana2(2D/E) [stated as Ana2(3D/E)] is, like the Ana2(12D/E) mutant, not efficiently recruited to centrioles.* This is a fair comment, but we have not analysed an Ana2(2D/E) mutant because, as described in point 3 above, the Ana2(2A) mutant did not recapitulate well the Ana2(12A) phenotype.

Minor comments

1. • Figure S1. The reviewer requests that we show that the mNG tag on its own is not recruited to centrioles.* We do not show this (as it would create a lot of white space in this Figure), but now state that mNG and dNG do not detectably localise to centrioles (p7, para.1).
2. • Figure S4C.* We have included the missing error bars (now Figure S4B).
3. • Figure S5A. The reviewer asks about the expression levels of the Ana2(12A) mutant, which are not shown in this Figure. They also state that the expression levels of the transgenes shown in Figure 5A are not similar.* The expression level of Ana2(12A) is shown in Figure S9, as this data was analysed independently of the other mutant proteins shown in Figure S5. We agree that it was overly simplifying the situation to state that the expression levels of WT Ana2-mNG, eAna2(∆CC)-mNG and eAna2(∆STAN)-mNG were “similar” (Figure S5), and we now specifically mention the differences between them (p11, para.3). Reviewer #2

This reviewer found this a rigorous study that advances our understanding of the regulation of centriole duplication, but raised some minor points.

Minor Points

The reviewer requests that we mention the literature describing how Ana2/STIL can influence the abundance and centriolar localisation of Plk4. We apologise for this omission, and have amended our description of this literature in the Introduction to include this point (p3, para.2).

The reviewer notes that we interpret the ability of the Ana2(12A) mutant to keep incorporating into the centrioles for a longer period as being consistent with our idea that rising levels of Cdk activity during S-phase normally reduce the ability of WT Ana2 to bind to the centriole. They ask us to show how Cdk activity increases over this time-course, and to test whether dampening Cdk has the same effect on Ana2 recruitment (i.e. allows Ana2 to be recruited for a longer period). The time-course of Cdk activation in these embryos has been reported previously (Deneke et al., Dev. Cell, 2016; we present the relevant data from this paper in RF#2A [black line]). This reveals how Cdk activity rises throughout S-phase, which is crucial for our model. To assess the effect of dampening Cdk activity in these embryos we have now analysed the effect of halving the genetic dose of Cyclin B (RF#2B). This perturbation extends S-phase length, but has a complicated effect on the recruitment dynamics of Ana2 (RF#2B). As we would predict, Ana2 is recruited to centrioles for a longer period in these embryos, but it is also recruited more slowly (so it accumulates to lower levels). This is consistent with our hypothesis that Cdk1 activity might first stimulate and then ultimately inhibit the centriolar recruitment of Ana2. The interpretation of this experiment is not straightforward, however, as dampening Cdk1 activity alters Ana2 recruitment dynamics (and many other processes in the embryo) in complicated ways, so we have decided not to include it in the manuscript.

The reviewer suggests that it would be valuable to show that all 12 of the potential Cdk1 phosphorylation sites in Ana2 can be phosphorylated by Cdk1 in vitro. We think this would not be particularly informative as our hypothesis does not rely on all 12 sites being phosphorylated to generate the Ana2(12A) phenotype. We simply mutate all 12 sites because we don’t know which, if any, are relevant. Thus, showing that some/all of the 12 sites can/cannot be phosphorylated in vitro does not test any hypothesis and would not change any of our conclusions. We now explain our thinking on this in more detail (p12, para.2)

Other points

Figure 3. We have corrected the amino-acid numbering mistakes.

Figure 5Aii. We have changed the x-axis (time) labelling in this and all other Figures.

Figure Legends. We have tried to eliminate the typos from the Figure legends, and apologise that these errors made it through to the final submitted version of our manuscript.

Reviewer #3

This reviewer thought our manuscript would be of great interest to not only the centrosome field but also to cell biologists more generally. Although they had no major concerns, they made a number of suggestions for improvements.

1. As the reviewer suggests, we now explicitly state that although the Ana2(12A) mutant appears to be largely functional, the overall conformation of the protein may be altered, changing its function in ways we do not appreciate (p21, para.2).

2. The reviewer suggests we include a multiple sequence alignment of Ana2/STIL proteins to provide more context about the distribution and conservation of the 12 S/T-P sites mutated in Ana2(12A).* This is an excellent idea, and we now include this in a new Figure S6, where we also provide more information about which of these sites have been shown to be phosphorylated in embryo or S2-cell extracts

3. The reviewer is confused as to why the 12A and 12D/E mutants rescue the ana2-/- mutant flies so well, which suggests that the mechanism we propose here cannot be essential for centriole duplication. We understand this confusion and we now make this point more clearly and explain why we think this occurs in more detail (e.g. p22, para.1). We propose that Cdk normally phosphorylates Ana2 to inhibit its ability to promote centriole duplication, but this phosphorylation does not entirely block this function. So, if all other elements of the system are functional, Ana2(12A) is recruited to centrioles for longer than normal, but this does not dramatically perturb centriole duplication because the many other factors that regulate centriole duplication (such as the pulse of Plk4 recruitment to centrioles [Aydogan et al., Cell, 2020]) still occur normally and are sufficient to ensure that centrioles still duplicate normally. When Ana2 phosphorylation is mimicked [Ana2(12D/E)], the ability of Ana2 to promote centriole duplication is perturbed (but not abolished). This perturbation is lethal in the early embryo—where the centrioles must duplicate in just a few minutes to keep pace with the rapid nuclear divisions. In somatic cells S-phase is much longer, so these cells can still duplicate their centrioles (as we observe) even though Ana2(12D/E) does not function efficiently. As we now explain, this phenotype (being lethal in the early embryo, but not in somatic cells) is a common feature of mutations that influence the efficiency* of centriole and centrosome assembly (p17, para.2).

4A. The reviewer asks us to comment in more detail on why centrioles do not seem to be elongated in the Ana2(12A) mutant wing disc cells (now Figure S8C), even though we show that Ana2(12A) (Figure 4A), and also Sas-6 (Figure 5), are recruited to centrioles for an abnormally long period. This is an excellent question and, although we do not know the answer, we now discuss this interesting point in more detail (p16, para.1). We think this is likely due to the “homeostatic” nature of centriole growth: in our hands, almost any perturbation that makes centrioles grow for a longer/shorter period, also makes them grow more slowly/quickly, so that they tend to grow to a similar size (Aydogan et al., JCB, 2018; Cell, 2020). This is fascinating, but poorly understood. When we perturb the system by expressing Ana2(12A), both Ana2(12A) and Sas-6 incorporate into centrioles for a longer period, as we predict (Figure 4A and 5A). Unexpectedly, however, Sas-6 is also recruited to centrioles much more slowly. Thus, as so often happens, when we perturb the system so the centrioles grow for a longer time, the centrioles “adapt” by growing more slowly. We do not currently understand why this occurs (although we speculate that Ana2 may also be regulated by Cdk/Cyclins to help recruit Sas-6 to centrioles in early S-phase). In the embryo, where S-phase is very short, this homeostatic compensation is not perfect, and the centrioles appear to actually be shorter than normal. In somatic wing-disc cells, where S-phase is much longer, we suspect that there is more scope for homeostatic compensation and so the centrioles grow to the correct size.

4B. In this point (also labelled [4] by the reviewer, so we have retained this numbering but labelled the points A and B) the reviewer asks why levels of Ana2(12A) eventually decline at centrioles once the embryos actually enter mitosis. The reviewer notes our rheostat theory, but suggests a discussion of other mechanisms might be interesting. This is a good point, and we agree that the observation that Ana2(12A) levels ultimately still decline at centrioles during mitosis is likely to be important in explaining why centriole duplication is not more dramatically perturbed by Ana2(12A). We now expand our discussion of this point, highlighting that other mechanisms must help to ensure that Ana2 is not recruited to centrioles during M-phase, and discussing the possibility that the receptors that recruit Ana2 to centrioles are themselves inactivated during mitosis by high levels of Cdk activity (p15, para.1). In such a model, the rapid drop in WT Ana2 centriolar levels is due to a combination of switching off Ana2’s ability to bind to centrioles (as we propose here) and switching off the ability of the centrioles to recruit Ana2. For Ana2(12A), only the latter mechanism would operate, so Ana2(12A) levels would start to drop later in the cycle (as the inflexion point at which Ana2 recruitment and loss balances out would be moved to later in the cycle), and these levels would drop more slowly—as we observe.

• The reviewer is confused to how the Ana2(12D/E) mutant can rescue the mutant phenotype when it is recruited to centrioles so poorly. Ana2(12D/E) is indeed recruited very poorly to centrioles in the experiment shown in Figure 7. However, this experiment had to be conducted in the presence of WT untagged Ana2—as the embryos do not develop in the presence of only Ana2(12D/E). We would predict that WT Ana2 would bind more efficiently to centrioles than Ana2(12D/E) (which appears to behave as if it has been phosphorylated by Cdk/Cyclins, and so cannot be recruited to centrioles efficiently). Thus, in the experiment we show in Figure 7, the Ana2(12D/E) protein is probably being “outcompeted” for binding to the centriole by the WT protein. In somatic cells expressing only* Ana2(12D/E) presumably sufficient mutant protein can be recruited to centrioles to support normal centriole duplication (as it no longer has to compete with the WT protein). We now explain our thinking on this point (p18, para.1).

• The reviewer wonders whether Ana2(12D/E) may be unable to homo-oligomerize, and this may explain why the protein is not recruited to centrioles efficiently even in the presence of WT protein. This is indeed a possibility, but we think it unlikely as it is widely believed that Ana2/STIL proteins must multimerize to be functional (Arquint et al., eLife, 2015; Cottee et al., eLife, 2015; Rogala et al., eLife, 2015; David et al., Sci. Rep., 2016). As Ana2(12D/E) strongly restores centriole duplication in ana2-/-* mutant somatic cells, it seems unlikely that it cannot multimerize. Nevertheless, we now specifically highlight that the 12D/E (and 12A) mutations might alter the ability of Ana2 to multimerise (p21, para.2).

We thank the reviewers again for their thoughtful and constructive comments. We hope they will agree that the revised manuscript is now improved and would be appropriate for publication in The Journal of Cell Biology.

With best wishes,

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Referee #3

Evidence, reproducibility and clarity

The manuscript entitled "Centriole growth is not limited by a finite pool of components, but is limited by the Cdk1/Cyclin-dependent phosphorylation of Ana2/STIL" by Steinacker et al. nicely demonstrates that centriole growth in Drosophila embryos is not limited by a finite pool of core centriole components as in other systems. In contrast, they unveiled a specific elevated cytoplasmic diffusion rate of Ana2/STIL towards the end of the S-phase, correlating with the rise of Cdk1/Cyclin activity, that they hypothesize is important for the abrupt stop of centriole growth before mitosis (end of S phase). They found using an Ana2 mutant (12A) that cannot be phosphorylated by Cdk1/Cyclin that this elevated diffusion rate is abrogated, demonstrating that this kinase is involved in this process. The authors further conclude that daughter centrioles grow at a slower rate for an extended period (as followed by SAS-6 incorporation at centrioles in the context of the 12A mutant). Thus, the authors conclude that this novel mechanism ensures that daughter centrioles stop growing at the correct time and propose that it could be part of the explanation why centriole duplication does not occur during mitosis.

Overall, this is a solid study that is well written and easy to follow. The text and figures are well presented and the quality of the data is convincing. This manuscript would be of great interest not only to the centrosome field but also more generally to cell biologists.

I do not have major concerns regarding the experiments. However, I would like to propose some minor comments/clarification in order to further improve the manuscript.

Suggestions for additional improvements:

My main comments are related to the phosphorylated mutants of Ana2 (12A) and (12D/E).

1. To study the impact of Cdk1 on Ana2, the authors generated a mutant where 12 potential Cdk1 sites have been replaced by Alanine (12A). Although I acknowledge that all controls were properly done on this mutant and that the 12A protein is functional since it rescues the ana2-/- mutant phenotype, one can still wonder whether this could not affect somehow the overall protein conformation, or structure. Maybe this could simply be stated somewhere in the manuscript.
2. The authors mentioned that there is evidence that 10 Cdk1 sites in Ana2 are phosphorylated in vivo and they further demonstrate convincingly that 2 of the most conserved sites can be phosphorylated in vitro by Cdk1/CyclinB (Figure S6). Could the authors include the alignment showing the potential phosphorylation residues and highlight the 12 that were mutated and show the overall conservation of these sites? It would be easier to find the residues as from the scheme of Fig. 3A it is not easy to find which residues are mutated (although the information can be found in the method section p. 32).
3. My main confusion regarding the phosphorylation mutants 12A or 12D/E comes from the fact that both can rescue the ana2-/- mutant phenotype, which indicates that the mutant protein is functional and that somehow these sites are not fully important for centriole duplication or are not solely responsible for this type of regulation. Is this interpretation correct, this is somehow what I take from the end of the discussion p.21? if true maybe it should be a bit more emphasized.
4. Moreover, I would have expected since centriole growth does not stop abruptly (one could talk about "prolonged" centriole growth) in the 12A mutant that centrioles would be longer. However, this is not the case as shown in Figure S7. One possible explanation would be that even though the centriole growth is extended (looking at SAS6 as a proxy), the slope/rate of incorporation is lower. Could you please comment on this more? I think this is an important point of discussion/interpretation of the results.
5. The authors nicely show that the 12A mutant, despite similar expression levels as the taggedAna2WT, continued to accumulate at centrioles till NEBD (consistent with the hypothesis that Cdk1 cannot phosphorylate it and thus stops its recruitment). But how can the 12A levels decline at centrioles in mitosis where Cdk1 activity is the highest? This would mean that Cdk1 activity/level regulates Ana2 differentially over time or that other mechanisms might be at play. The authors mention in the discussion the attractive hypothesis of the "rheostat" (p. 20) but maybe a further discussion on an alternative mechanism could be also interesting. Could the fact that the 12A level decreases in mitosis also explain the lack of centriole phenotype if we would imagine that levels at centrioles would stay high? Could the authors comment on this? They mention it briefly (p.14 and p.21) but if they could expand a bit would be great.
6. I was a bit confused about how the 12D/E mutant that is not recruited efficiently to centrioles could rescue the ana2-/- mutant centrioles? Could the authors comment on this, please?
7. p.16 still about the 12D/E that is not properly recruited to centrioles even in presence of one WT copy of Ana2 (untagged): The authors conclude that "phosphorylation at one or more of these S/T sites inhibits, but does not completely block, Ana2 recruitment to and/or maintenance at centrioles". Could the mutation also prevent Ana2 homo-oligomerization? In other words, could this result suggest that the 12D/E cannot interact with untagged Ana2WT and be recruited to centrioles? Is it a possibility?

Significance

In this manuscript, the authors address two major fundamental questions:

1. the mechanism that restricts strict cell cycle regulation of centriole duplication
2. How daughter centrioles grow to the correct size. These questions are very important and this study provides some clues on the mechanisms that can be at play, among which Cdk1/cyclin seems to be involved.

In addition, this paper raises an interesting point in showing that the core centriole duplication components concentration is as low in human cells as in fast-dividing Drosophila embryos in the range of 5-20nM. This is very interesting as it was commonly thought that embryos would have a stockpile of core components to ensure fast and numerous centriole duplication cycles. Furthermore, they found that these concentrations remained constant using FCS or Pecos, demonstrating that core centriole components concentrations are not rate-limiting for centriole duplication (over time) in this system. Instead, they propose an alternative hypothesis whereby Cdk1/Cyclin phosphorylation of Ana2/STIL would be important to regulate centriole growth and ensured timely duplication (ie no duplication in mitosis, when Cdk1 activity is high).

In this context, this study would certainly have a broad interest and impact on cell biologists.

Reviewer's expertise: Centrioles, microtubules, microscopy, cell biology.

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Referee #2

Evidence, reproducibility and clarity

Centriole growth is not limited by a finite pool of components, but is limited by the Cdk1/Cyclin-dependent phosphorylation of Ana2/STIL

Authors: Thomas L. Steinacker, Siu-Shing Wong, Zsofia A. Novak, Saroj Saurya, Lisa Gartenmann, Eline J.H. van Houtum, Judith R. Sayers, B. Christoffer Lagerholm, Jordan W. Raff

Centriole biogenesis is a tightly regulated process that occurs once per cell cycle. Defects in this process can lead to the acquisition of abnormal centriole numbers which has been linked to several human diseases. Centriole duplication starts with the assembly of a procentriole on the mother centriole in early S-phase followed by procentriole growth during G2 phase. A big question in the centrosome field is how new procentrioles assemble at the right time and acquire the correct final size.

In this manuscript, Wong et al. analyse whether the cytoplasmic concentration of several proteins changes during centriole assembly (Asl, Plk4, Ana2, Sas-6, and Sas-4). The authors show that the cytoplasmic concentration of these proteins remains constant during centriole duplication, indicating they are not limiting components for procentriole assembly. Nevertheless, the authors found that Ana2/STIL's cytoplasmic diffusion rate increases before the onset of mitosis, concurrent with an increase in Cdk1/Cyclin activity. Mutation of 10 putative phosphorylation sites in Ana2 prevented the diffusion rate change and enabled centrioles to grow for a longer period. This suggests that phosphorylation of Ana2/STIL by Cdk1/Cyclin could control the period of centriole growth.

Minor points:

In the introduction, the authors describe how PLK4 is required to recruit STIL and Sas-6 to promote the formation of the cartwheel during centriole duplication. However, there is also literature describing a role for STIL in regulating PLK4 abundance and localization pattern (i.e ring or dot) at the centriole.

The authors note that the levels of the Ana2(12A) mutant keep increasing until the onset of mitosis. The authors claim that this phenotype is consistent with the timing of increased Cdk1 activity. It would be interesting to show the increase in Cdk1 kinase activity over the same time-course and test whether dampening Cdk1 has the same effect on Ana2 recruitment.

While I appreciate detecting in vivo phosphorylation sites can be very challenging, It would be valuable to show the 10 Ana2 phosphorylation sites can be phosphorylated by Cdk1, at least in vitro.

Other points:

Figure 3: Amino acids numbers for CC domain are not the same in the figure and in the figure legend.

Figure 5Aii, the x-axis should be changed to minutes for easier comparison with other figures.

There are some typos in the figure legends.

Significance

This study attempts to address a central question in the centrosome field: how centriole growth is controlled. Although the paper does not provide a detailed mechanistic advance, the authors do provide some evidence against a limited pool of centriole components controlling centriole length, and they are careful not to overstate conclusions. The manuscript is well written and easy to follow. While it is not clear at present how phosphorylation of Ana2 alters its diffusion rate or limits centriole growth, I feel the study will be of interest to members of the centriole community and will stimulate new lines of investigation. Given that the cartwheel stops elongating in S phase in mammalian systems, it is not clear if the mechanism proposed would be conserved. That notwithstanding, I found this to be a rigorous study that advances our understanding of the regulation of the centriole duplication.

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Referee #1

Evidence, reproducibility and clarity

Centriole duplication is a conserved pathway that need to be tightly regulated. The key enzyme of centriole assembly is Plk4 which is recruited to the centrioles and undergoes dynamic re-localization from a ring-like pattern around a centriole to a dot-like morphology at the daughter centriole assembly site. This event is central for inducing centriole biogenesis. Plk4 then phosphorylates Ana2/STIL which allows recruitment of Sas-6 to form the cartwheel structure for centriole assembly.

In the present study, Steinacker, Wong et al. monitor how cytoplasmic concentrations of the key proteins in centriole assembly, Plk4, Asl/Cep152, Ana2/STIL, Sas-6 and Sas-4/CPAP change during the centriole assembly process in the Drosophila embryo by using fluorescence correlation spectroscopy (FCS) and Peak Counting Spectroscopy (PeCoS). They find that their concentrations remain constant with exception of Ana2/STIL of which cytoplasmic diffusion rate increased at the end of S-phase and is dependent on phosphorylation by Cdk1/CyclinB. Phosphorylated Ana2/STIL blocks centriole duplication thus preventing premature initiation of centriole duplication in mitosis.

Major comments

The manuscript is interesting and very well written. Most of the experiments are carefully performed. However, there are some important aspects for improvements that are listed below

Additional experiments:

• Figure 3: the transgenic flies that were generated here, CC and STAN, still contain wild-type Ana2. So, the authors therefore need remove or dampen their claim that the change in Ana2's cytoplasmic diffusion does not depend on its interaction with Sas-6 (page 11).
• Figure 5A: is the observed reduced recruitment of Sas-6 by Ana2(12A) due to a decrease in binding affinity? This should also be shown by analyzing protein-protein interactions between Ana2(12A) and Sas-6 biochemically.
• The authors use an Ana2(12A) mutant which comprises putative Cdk1 phosphorylation sites that have been identified in Mc Lamarrah et al. JCB 2018. However, only three of them were phosphorylated by Cdk1/cyclin B in vitro (Fig. S6). Are all these 12 putative Cdk1 phosphorylation sites important in vivo? Did the authors generate the Ana2(3A) or the S284A/T301A mutants to see whether it can rescue the ana2-/- mutant phenotype similar to the 12A mutant? These might be sufficient to observe the phenotype.
• Figure 6: is the interaction between Plk4 and Ana2(12A) impaired? Similarly, Plk4 activity and phosphorylation of Ana2(12A) by Plk4
• Figure 7: Phosphomimetics, in this case 12 amino acid changes, have the disadvantage of introducing more negative charge than the phosphorylated residue. The Ana2/(12D/E)-mNG is not efficiently recruited to centrioles. Is effect also observed for the Ana2/(3D/E) mutant?

Minor comments

Figure S1: only mNG-tagged centriolar proteins are shown. An empty mNGtag or an mNG-tagged non-centriolar protein should be shown to exclude that the tag by itself shows centriolar localization or somehow affects the localization

S4C: Sas6-mNG CPM error bars are missing for the 10min time point

S5A: What are the expression levels of the Ana2(12A) mutant? The expression levels shown in this Figure are not similar.

Significance

Centriole duplication normally begins at the G1/S phase transition. An important question in the field is how premature centriole duplication in mitosis is prevented. The authors used fluorescence correlation spectroscopy (FCS) and Peak Counting Spectroscopy (PeCoS) to study the major conserved proteins in the centriole assembly pathwayq and found that only Ana2/STIL's cytoplasmic diffusion increases at the end of S-phase. It is known from the literature that Cdk1 prevent Plk4-STIL complex assembly in centriole biogenesis by directly competing with Plk4 for the CC domain of Ana2/STIL (Zitouni et al. Curr Biol 26, 1127-1137 (2016). However, Ana2/STIL can also bind to Plk4 via its conserved C-terminal region of STIL (Ohta et al., Cell Reports 11, 2018; McLamarrah et al., J Cell Biol 2018, 217, 1217-1231). The work by Steinacker, Wong et al. suggest that at least in fly embryos, growth of the daughter centriole is regulated though phosphorylation of Ana2 by Cdk1/CyclinB rather than binding. The findings described in this manuscript are interesting for a broad range of scientists from both the centrosome and mitosis fields

Expertise of the reviewer: centriole biogenesis, structural and numerical centrosomal aberrations in disease

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Reply to the reviewers

Point-by-point description of the revisions

Black: Comments from reviewers

Green: Answers

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

Yamamoto and colleagues have investigated the interplay between microtubules (MTs) and actin in positioning the MTOC at "the cell centre". They have developed a novel experimental setup akin to a synthetic cell to study this question. Essentially a cell-sized (15 µm) microwell that is coated in lipid and then tubulin/actin added and the positioning of a MTOC proxy is studied by microscopy. This is a well executed study. These complicated biochemical reconstitutions are the hallmark of Blanchoin and Théry's group, but even so, it's clear that the exact conditions (e.g. tubulin concentration) are fiddly and critical for these experiments to work. The data are clear, well analysed and presented. In brief, the conditions for centring a cytoskeletal network and decentring/polarising it are recapitulated. This is a short, straightforward paper and I found the results to be clear and the authors' interpretation to be well supported by the data.

Two questions occurred to me as I read the paper: 1. While the setup is reminiscent of a cell, I suspect that the edge/wall of the microwell is much stiffer than the plasma membrane. So a MT that encounters the wall may behave differently in the cell. This would affect the non-actin conditions but possible also the conditions where an actin mesh is present. Maybe my intuition is not even correct, but I think this issue should be discussed in the paper as a potential limitation of the system.

Author response: We thank the reviewer for this wise comment. Indeed, the deformation of the container may impact the organization of the MT network, the force balance and the final position of the MTOC. We commented this limitation in the revised discussion (page 10 line 31). However, it should be noted that in the presence of a cortical actin network, MTs are much less capable of deforming the cell than in a vesicle or a in cell treated with actin drugs, so our conditions with a cortical actin network are physiologically relevant although the container can not be deformed.

1. The graphs in 3C and 4G (lesser extent Fig 1) show nicely that the aMTOC position has apparently rested at a steady state. Some representative trajectories are shown in some figures, but not mentioned much in the text. How does the pathlength (cumulative distance) over time compare to the "distance to centre" measurement? Is there more or less travel under the different conditions? From the supplementary videos it looks like there is a difference. An apparent resting position may still represent significant motion, e.g. circling the centre. What does an analysis of tracklength tell us, if anything?

Author response: We appreciated reviewer’s comment and followed his/her advice. We measured the pathlength (cumulative distance moved) based on the data shown in Figure 3C and 4G. The analysis confirmed that the MTOC was static in the presence of bulk actin network (shown in the new Supplementary Figure 6B). Interestingly, it also showed that the final position adopted by the MTOC in conditions where it could move more freely was also static, as revealed by the saturation of the pathlength after 1 hour. These analyses are shown in the new Supplementary Figure 6B for the centering in the absence of cortical actin, for the non-centering with long microtubules in Supplementary Figure 7E and for the centering with long MTs and a cortical actin network in Supplementary Figure 7E.

Very minor clerical point: - the first two sentences of the abstract could be clearer. "The position of centrosome, the main microtubule-organizing center (MTOC), is instrumental in the definition of cell polarity. It is defined by the balance of tension and pressure forces in the network of microtubules (MTs)." In the second sentence, "it" and "defined" are confusing. Are you talking about the position of the centrosome or cell polarity?

Author response: We thank the reviewer for this comment. As the reviewer suggested, this was a confusing description. Accordingly, we corrected the sentence in the abstract for :

The orientation of cell polarity depends on the position of the centrosome, the main microtubule-organizing center (MTOC). It is determined by the balance of tension and pressure forces in the network of microtubules (MTs).

Reviewer #1 (Significance (Required)):

As I see it, the main advance here is in novel experimental setup which has real potential in the field. Existing methods such as MTs inside lipid bubbles are limited, whereas as the microwell method with fabrication methods allows the shape of the "synthetic cell" to be carefully modulated. Tying the results together with cytosim simulations is also a powerful combination. There is a lot of interest in bottom-up reconstitution of cell biological phenomena, especially those that underlie specialised cell processes, e.g. polarity. My expertise: microtubules in a cellular context with limited experience of MT reconstitution assays.

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

Summary: This manuscript describes the use of an elegant in vitro reconstitution system to study the effect of variations in the organization of the actin network on the positioning of a microtubule organizing center (MTOC) within the cell. By using a reconstituted system the authors are able to specifically study the contribution of the "pushing" forces generated by microtubule (MT) growth, without the confounding influence of other factors, like pulling forces from MT motors. The authors find that a bulk actin networks at sufficient density can impair MTOC displacement, likely a result of the large viscous drag of the MTOC. Next they show that MTOC centering more resilient to changes in microtubule length. Finally they show that an asymmetric actin network can cause asymmetric positioning of the MTOC.

Major comments: 1) The model the authors put forth is that the growth of long MTs leads to decentering as a result of the MTs slipping along the well edge. The presence of a cortical actin mesh prevents this slipping. Their argument would be strengthened with and analysis of the MT behaviors in the various conditions. For example when discussing MTOC in well without actin...

"As they grew, they first ensured a proper centering but after an hour, MT elongation and slippage along microwell edges broke the network symmetry and MTs pushed aMTOC away from the center (Figure 1I, J and Supplementary Movie 2)"

In this movie I don't see evidence of MTs hitting the cortex and sliding on the "short" side of the well relative to the MTOC. An analysis of the behavior of MTs in various circumstances would help link the behavior of MTs to the movement of the MTOC for all of their conditions. What fraction of MTs hit the cortex and remain relatively motionless, what fraction slide, what fraction catastrophe, what fraction turn and follow the curve of the well? And how does this behavior change for microtubules that end up on the short side vs. the long side of the MTOC? This type of analysis would solidify their model for how centering/decentering occurs in the various conditions they test.

Author response: This is a fair criticism. The possibility to perform fine analysis of MT dynamics is technically limited by the fluorescent background due to free tubulin dimers. It is the reason why classical in vitro assays are monitored in TIRF microscopy, which is not possible here since MTOCs move in 3D in the microwells. In addition, working with higher laser power to increase the signal to noise ratio generates severe photodamages on MTs. Nevertheless, we could visualize MT dynamics and displacements near the edge of the microwells and describe their behavior more precisely than in the previous version of our manuscript. New images and tracking of MT behavior are now reported in the new Figure 4E, 4F and 5G, as well as the new supplementary Figure 4C, 4D, 7B, and 7C. We also replaced the supplementary movie 2 and Figure 1I in order to show more clearly MTs hitting and slipping along the well boundary. In addition, we also characterized the pivoting of MTs around the MTOC and near the edge of the microwell in order to better characterize the effect of cortical actin. This is now shown in the new Figure 4G and 4H as well as in the new Supplementary Figure 7C-D). We found that the changes in MT orientation and position, at the centrosome and at the contact with the microwell, were clearly prevented by the presence of cortical actin.

2) The authors use simulations to support their in vitro findings. However, their simulations have many more microtubules emanating from the MTOC than their experiment (Looks like about 50 in the cytosim and they state they are aiming for 15-20 in the aMTOCs). Do the simulations still reproduce the behavior of the in vitro system with a similar number of MTs?

Author response: This is another fair criticism. We addressed this point by performing simulations with 10~30 microtubules (the number of MTs is variable because of MT dynamics) which are more similar to the number of MTs that we obtained in our experimental conditions. Results were consistent with previous simulations with higher number of MTs and are now shown in the new supplementary figures 6E-F, 7G and 8I).

3) When the actin networks are asymmetric, the authors see decentering of the MTOC towards the side with less actin. However there is still actin on the side where the MTOC will move to and in some of their images it looks pretty think. Is the actin on that side not dense enough to prevent MT sliding along the "cortex"? If so, can they generate less dense, but uniform actin networks on the "cortex", where MTs can slide. Again descriptions of MT behaviors would be useful in understanding what is happening.

Author response: We thank the reviewer for asking this important question. We followed reviewer’s advice and generated homogeneous and less dense cortex by working at lower concentration of actin (0.5 mM). In such conditions, we could not see the centering effect that was observed with dense cortex. These new data are now shown in the new Supplementary Figure 7I. This effect was also tested with numerical simulations (new Supplementary Figure 7J) which were consistent with the key role played by actin network density for MT network positioning by cortical friction.

Minor Comments: 1)Title - the current title implies that actin is balancing the forces generated by the MTs. I'm not sure this is a good description of what is shown in the paper.

Author response: We thank the reviewer for pointing at this issue. We revised the title to:

Reconstitution of centrosome positioning by the production of pushing forces in microtubules growing against the actin network.

2)The discussion would benefit from more explanation about how the results of this paper relate to the classic examples of MTOC positioning they cite. How do they envision the actin and MTs interacting in these systems and what new insight have we gained from the experiments in this manuscript.

Author response: This is a good suggestion. We added some comments in our discussion about the actin network asymmetry in several classical examples of cell polarization and explained how our observations suggest some new interpretation on the role of this asymmetry in the reorganization of forces in the MT network and on the consequential peripheral positioning of the MTOC.

Reviewer #2 (Significance (Required)):

Overall, this work is a significant advance in our understanding of the potential mechanisms of MTOC movement in cells via pushing by MT growth. The experimental system they have developed is powerful advance, allowing meaningful MTOC reconstitution experiments to be performed in chambers of approximately cellular size. This is an important contribution to understanding the interaction between microtubule pushing and the actin cortex.

Reviewer expertise: Cell biology of MTOC assembly and positioning. I do not have the expertise to assess the parameters used to generate their cytosim models.

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

Review of "The architecture of the actin network can balance the pushing forces produced by growing microtubules" by Yamamoto et al.

The means by which cells maintain their characteristic cytoskeletal architectures is not well understood. This is in part because there is considerable variation in such architectures with, for example, fibroblasts, neurons, and epithelial cells. It is also in part because the microtubule, actin and intermediate filaments engage in a wide range of mechanical and signaling crosstalk mediated by a wealth of proteins and signaling networks, which further complicates the picture.

In the current study, Yamamoto take the welcome step of developing a simplified system for assessing the mutual contributions of microtubules and F-actin for general cytoskeletal organization in vitro (specifically, in lipid-lined microwells). This allows them to define basic principles of microtubule-F-actin interactions in the absence of the various confounding factors alluded to above. Using their model, they show that artificial MTOCs (aMTOCs) alone will center but as a complex function of microtubule length (controlled by varying tubulin concentrations). That is, the aMTOCs are randomly positioned with short microtubules, stably centered with intermediate length microtubules, and randomly oriented with very long microtubules (following symmetry breaking).

They then assess the contributions of F-actin to the centering process. In low concentrations of "bulk" F-actin (ie F-actin distributed throughout the droplet) there is no effect on centering whereas at higher concentrations of bulk F-actin, centering is impaired as is the translocation of the aMTOCs. In the presence of uniform peripheral F-actin, in contrast, aMTOC centering is enhanced, and rendered less sensitive to variations in microtubule length. Finally, when the authors contrive a situation in which the peripheral F-actin is non-uniform (by lowering the concentration of actin and adding alpha-actinin, which creates a peripheral ring of F-actin with (I think) relatively less F-actin within the ring), the aMTOCs position themselves within the ring.

Finally, the authors extend their results with simulations that indicate that the various behaviors can be explained by a combination of friction, pushing and slippage.

This study is fascinating and will be of general interest to anyone who seeks to understand the contributions of mechanical forces to cytoskeletal organization in a minimal system. I have only minor concerns; these are listed below.

1. Some of the terminology was a little confusing. The authors introduce the term "inner zone" (pg. 8) without defining it. From the context, it seems like they are talking about the approximate center of the ring of peripheral F-actin. If so, why not just do away with the term "inner zone" and refer to the ring center. If it isn't the ring center, then more explanation is needed as to what the inner zone actually is.

Author response: We apologize for this confusion and appreciate reviewer’s comment. We coined earlier the term “actin inner zone” to define the central cytoplasmic region in cells that is devoid of actin filament (Jimenez et al., Current Biology, 2021). Because it was a confusing point, we clarified this in the revised version of the manuscript (Page 8, Line 20). What we would like to call the “inner zone” is the region inside of the actin cortex. The definition of this zone and of its geometrical reference points were also pictured more precisely in the new Supplementary Figure 9B.

1. It is not clear from the text or the images if the region within the F-actin ring has less F-actin, more F-actin, or the same amount of F-actin as the region outside the F-actin ring. This point should be clarified, as it makes a big difference in the interpretation of the findings.

Author response: We apologize for this lack of clarity. In the revised version of our manuscript, we plotted a line scan intensity profile of the actin fluorescence (new Supplementary Figure 9B). It showed that the region within the actin inner zone contained much less actin than in the cortex. This is consistent with our interpretation of a region-selective pattern of friction acting on microtubules.

1. Ideally, the authors would include manipulations in which the high concentration of peripheral F-actin is combined with alpha-actinin because, as currently presented, the authors are drawing conclusions from changing two variables at once (ie going from a high concentration of peripheral F-actin to a lower concentration with added alpha-actinin). Thus, the authors cannot cleanly distinguish between effects that arise from F-actin asymmetry versus the presence of an F-actin crosslinker. Since the crosslinking is likely to change the mechanical properties of the peripheral F-actin network, this point should at least be addressed in the text, if not by experiments.

Author response: We are not sure to fully understand the reviewer’s point. We don’t understand how the crosslinking of a symmetric actin network could break the symmetry of the MT network and force its off-centering. The opposite is clearer to us. A homogeneous and loose actin network can allow MT gliding and MTOC off-centering (like in in Supplementary Figure 7J). The mechanical reinforcement of this network by crosslinkers could indeed resist gliding. But the consequence of this resistance would be similar to the consequence of a dense network: a more robust centering (like in Figure 4). So we don’t understand how the crosslinking by alpha-actinin, rather than the asymmetry of the actin network, could be at the origin of the off-centering we observed. In addition the off-centering of the MTOC was systematically aligned with the asymmetry of the actin network, so both parameters were clearly connected.

Reviewer #3 (Significance (Required)):

This is an elegant, well-designed study that provides a clear description of how basic mechanical forces can contribute to cytoskeletal organization in a simplified model system.

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Referee #3

Evidence, reproducibility and clarity

Review of "The architecture of the actin network can balance the pushing forces produced by growing microtubules" by Yamamoto et al.

The means by which cells maintain their characteristic cytoskeletal architectures is not well understood. This is in part because there is considerable variation in such architectures with, for example, fibroblasts, neurons, and epithelial cells. It is also in part because the microtubule, actin and intermediate filaments engage in a wide range of mechanical and signaling crosstalk mediated by a wealth of proteins and signaling networks, which further complicates the picture.

In the current study, Yamamoto take the welcome step of developing a simplified system for assessing the mutual contributions of microtubules and F-actin for general cytoskeletal organization in vitro (specifically, in lipid-lined microwells). This allows them to define basic principles of microtubule-F-actin interactions in the absence of the various confounding factors alluded to above. Using their model, they show that artificial MTOCs (aMTOCs) alone will center but as a complex function of microtubule length (controlled by varying tubulin concentrations). That is, the aMTOCs are randomly positioned with short microtubules, stably centered with intermediate length microtubules, and randomly oriented with very long microtubules (following symmetry breaking).

They then assess the contributions of F-actin to the centering process. In low concentrations of "bulk" F-actin (ie F-actin distributed throughout the droplet) there is no effect on centering whereas at higher concentrations of bulk F-actin, centering is impaired as is the translocation of the aMTOCs. In the presence of uniform peripheral F-actin, in contrast, aMTOC centering is enhanced, and rendered less sensitive to variations in microtubule length. Finally, when the authors contrive a situation in which the peripheral F-actin is non-uniform (by lowering the concentration of actin and adding alpha-actinin, which creates a peripheral ring of F-actin with (I think) relatively less F-actin within the ring), the aMTOCs position themselves within the ring.

Finally, the authors extend their results with simulations that indicate that the various behaviors can be explained by a combination of friction, pushing and slippage.

This study is fascinating and will be of general interest to anyone who seeks to understand the contributions of mechanical forces to cytoskeletal organization in a minimal system. I have only minor concerns; these are listed below.

1) Some of the terminology was a little confusing. The authors introduce the term "inner zone" (pg. 8) without defining it. From the context, it seems like they are talking about the approximate center of the ring of peripheral F-actin. If so, why not just do away with the term "inner zone" and refer to the ring center. If it isn't the ring center, then more explanation is needed as to what the inner zone actually is.

2) It is not clear from the text or the images if the region within the F-actin ring has less F-actin, more F-actin, or the same amount of F-actin as the region outside the F-actin ring. This point should be clarified, as it makes a big difference in the interpretation of the findings.

3) Ideally, the authors would include manipulations in which the high concentration of peripheral F-actin is combined with alpha-actinin because, as currently presented, the authors are drawing conclusions from changing two variables at once (ie going from a high concentration of peripheral F-actin to a lower concentration with added alpha-actinin). Thus, the authors cannot cleanly distinguish between effects that arise from F-actin asymmetry versus the presence of an F-actin crosslinker. Since the crosslinking is likely to change the mechanical properties of the peripheral F-actin network, this point should at least be addressed in the text, if not by experiments.

Significance

This is an elegant, well-designed study that provides a clear description of how basic mechanical forces can contribute to cytoskeletal organization in a simplified model system.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript describes the use of an elegant in vitro reconstitution system to study the effect of variations in the organization of the actin network on the positioning of a microtubule organizing center (MTOC) within the cell. By using a reconstituted system the authors are able to specifically study the contribution of the "pushing" forces generated by microtubule (MT) growth, without the confounding influence of other factors, like pulling forces from MT motors. The authors find that a bulk actin networks at sufficient density can impair MTOC displacement, likely a result of the large viscous drag of the MTOC. Next they show that MTOC centering more resilient to changes in microtubule length. Finally they show that an asymmetric actin network can cause asymmetric positioning of the MTOC.

Major comments:

1) The model the authors put forth is that the growth of long MTs leads to decentering as a result of the MTs slipping along the well edge. The presence of a cortical actin mesh prevents this slipping. Their argument would be strengthened with and analysis of the MT behaviors in the various conditions. For example when discussing MTOC in well without actin...

"As they grew, they first ensured a proper centering but after an hour, MT elongation and slippage along microwell edges broke the network symmetry and MTs pushed aMTOC away from the center (Figure 1I, J and Supplementary Movie 2)"

In this movie I don't see evidence of MTs hitting the cortex and sliding on the "short" side of the well relative to the MTOC. An analysis of the behavior of MTs in various circumstances would help link the behavior of MTs to the movement of the MTOC for all of their conditions. What fraction of MTs hit the cortex and remain relatively motionless, what fraction slide, what fraction catastrophe, what fraction turn and follow the curve of the well? And how does this behavior change for microtubules that end up on the short side vs. the long side of the MTOC? This type of analysis would solidify their model for how centering/decentering occurs in the various conditions they test.

2) The authors use simulations to support their in vitro findings. However, their simulations have many more microtubules emanating from the MTOC than their experiment (Looks like about 50 in the cytosim and they state they are aiming for 15-20 in the aMTOCs). Do the simulations still reproduce the behavior of the in vitro system with a similar number of MTs?

3) When the actin networks are asymmetric, the authors see decentering of the MTOC towards the side with less actin. However there is still actin on the side where the MTOC will move to and in some of their images it looks pretty think. Is the actin on that side not dense enough to prevent MT sliding along the "cortex"? If so, can they generate less dense, but uniform actin networks on the "cortex", where MTs can slide. Again descriptions of MT behaviors would be useful in understanding what is happening.

Minor Comments:

1) Title - the current title implies that actin is balancing the forces generated by the MTs. I'm not sure this is a good description of what is shown in the paper.

2) The discussion would benefit from more explanation about how the results of this paper relate to the classic examples of MTOC positioning they cite. How do they envision the actin and MTs interacting in these systems and what new insight have we gained from the experiments in this manuscript.

Significance

Overall, this work is a significant advance in our understanding of the potential mechanisms of MTOC movement in cells via pushing by MT growth. The experimental system they have developed is powerful advance, allowing meaningful MTOC reconstitution experiments to be performed in chambers of approximately cellular size. This is an important contribution to understanding the interaction between microtubule pushing and the actin cortex.

Reviewer expertise: Cell biology of MTOC assembly and positioning. I do not have the expertise to assess the parameters used to generate their cytosim models.

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Referee #1

Evidence, reproducibility and clarity

Yamamoto and colleagues have investigated the interplay between microtubules (MTs) and actin in positioning the MTOC at "the cell centre". They have developed a novel experimental setup akin to a synthetic cell to study this question. Essentially a cell-sized (15 µm) microwell that is coated in lipid and then tubulin/actin added and the positioning of a MTOC proxy is studied by microscopy. This is a well executed study. These complicated biochemical reconstitutions are the hallmark of Blanchoin and Théry's group, but even so, it's clear that the exact conditions (e.g. tubulin concentration) are fiddly and critical for these experiments to work. The data are clear, well analysed and presented. In brief, the conditions for centring a cytoskeletal network and decentring/polarising it are recapitulated. This is a short, straightforward paper and I found the results to be clear and the authors' interpretation to be well supported by the data.

Two questions occurred to me as I read the paper: * While the setup is reminiscent of a cell, I suspect that the edge/wall of the microwell is much stiffer than the plasma membrane. So a MT that encounters the wall may behave differently in the cell. This would affect the non-actin conditions but possible also the conditions where an actin mesh is present. Maybe my intuition is not even correct, but I think this issue should be discussed in the paper as a potential limitation of the system. * The graphs in 3C and 4G (lesser extent Fig 1) show nicely that the aMTOC position has apparently rested at a steady state. Some representative trajectories are shown in some figures, but not mentioned much in the text. How does the pathlength (cumulative distance) over time compare to the "distance to centre" measurement? Is there more or less travel under the different conditions? From the supplementary videos it looks like there is a difference. An apparent resting position may still represent significant motion, e.g. circling the centre. What does an analysis of tracklength tell us, if anything?

Very minor clerical point: * the first two sentences of the abstract could be clearer. "The position of centrosome, the main microtubule-organizing center (MTOC), is instrumental in the definition of cell polarity. It is defined by the balance of tension and pressure forces in the network of microtubules (MTs)." In the second sentence, "it" and "defined" are confusing. Are you talking about the position of the centrosome or cell polarity?

Significance

As I see it, the main advance here is in novel experimental setup which has real potential in the field. Existing methods such as MTs inside lipid bubbles are limited, whereas as the microwell method with fabrication methods allows the shape of the "synthetic cell" to be carefully modulated. Tying the results together with cytosim simulations is also a powerful combination. There is a lot of interest in bottom-up reconstitution of cell biological phenomena, especially those that underlie specialised cell processes, e.g. polarity.

My expertise: microtubules in a cellular context with limited experience of MT reconstitution assays.

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Referee #3

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Referee #2

Evidence, reproducibility and clarity

Summary

Dantas and colleagues use mechanical confinement assays to demonstrate that both mitotic entry and the timing of prophase are sensitive to mechanical perturbations. They identify a novel mechanism that fine tunes the dynamics of cyclin B1 nuclear import during prophase whereby acto-myosin contractility leads to nuclear membrane unfolding, cPLA2 recruitment and cyclinB1 nuclear import. They show how mechanical confinement can accelerate this mechanism by independently inducing nuclear unfolding, and that this can go on to induce defects in mitotic spindle assembly and chromosome segregation.

Major

This work contains an impressive amount of data including some technically challenging experiments. The conclusions are convincing and for the most part well supported by experimental evidence (for exceptions see below). Appropriate controls are presented and statistical analysis is adequate. The methods are mostly described well but some important details are omitted (see below). The methods and figure legends would benefit from expansion, particularly in describing how the images presented relate to quantification in graphs. Although generally the manuscript is well written, there are parts when both the experimental logic and conclusions are hard to follow, particularly in the description of figures 1 and 5 (see below for details). With a large amount of data, including important experiments relegated to supplementary figures, this work would benefit from expansion into a longer article format to allow for more clarity. Particularly:

• Figure 1A-C: here the authors show that non-adherent cells only enter mitosis when confined. There is some key information lacking here, including the experimental timeframe. How long were the cells plated on pll-peg before imaging and for how long were they imaged? In 1C, 80% of confined cells enter mitosis, which implies that cells were filmed for a relatively long time (given an average cell cycle length of 20-24 hours). Unless of course cells were previously synchronised in G2 but the authors do not state that this is the case. In the legend it states that images were acquired every 20s. Imaging cells for 20+ hours every 20s with multiple zs is likely to have a very deleterious effect on cells and to disrupt mitotic entry itself. The authors need to explicitly explain the experimental set-up used to generate the graphs in figure 1. In 1C, it would also be good to see the equivalent adherent control included in the graph (ie % cells that enter mitosis on fibronectin in the same timeframe). The authors use the data in 1A-C to claim that 'the G2-M transition requires contact with external stimuli'. However they haven't shown this, only that non adherent cells don't enter mitosis. To show that the G2/M transition is affected, they need to look at the cell cycle phase of cells on PLL-PEG and show that cells become arrested specifically in G2.
• Figure 5: The explanation of the conclusions here was hard to follow. It's not immediately clear why a faster prophase would lead to chromosome attachment delays in metaphase or segregation errors in anaphase since these events occur only after NEP. I think the authors' hypothesis is that a faster prophase results in less time for centrosome separation and that this is responsible for later spindle defects but this is not very clearly stated. If this is the case, then one might expect cells in which centrosome separation is delayed to also be the cells with lagging chromosomes. Did the authors observe such a correlation? It's also not clear why the authors expected confinement to rescue the spindle defects imposed by STLC treatment (supp figure 5). An alternative hypothesis that the authors neglect to mention is that faster cyclinB1 entry into the nucleus could also induce defects through changes to nuclear events such as chromosome condensation? Did they also see any changes to the rate of chromosome condensation in the confined prophase? Either way, the authors should explain more clearly in the text what they think is happening here.

Minor

• No reference is cited for the endogenous tagged CyclinB1 RPE1 line nor are any details about its construction given. Has this cell line been previously published by the Pines lab? Are one or both alleles tagged? N or C terminus?
• Figure 1C: presumably n in this case is number of experiments, not cells. How many cells were analysed in each case?
• Figure 1H. Why do the graphs have different scales on the x axis? Where does 101+-12s for confined cyclin B translocation mentioned in the text come from? From the graph, it looks longer than this?
• Figure 3 J, K. Confinement is able to rescue the effect of Y27 on cyclin B dynamics but not shROCK1. Why this difference? The authors should discuss this discrepancy in the text.

Significance

This work identifies a novel mechanical mechanism that regulates the timing of cyclin B1 nuclear import in early mitosis. The role of nuclear unfolding in controlling cyclinB1 import is particularly interesting. How important this new mechanism will be in controlling the duration of prophase or mitotic fidelity in a 'normal' mitosis within a tissue is not yet clear. However, it raises many intriguing questions about how cells' mechanical environment could impact mitotic entry, which could be relevant to disease situations where mechanics is altered such as fibrosis or cancer. The work is likely to be of interest to a wide range of cell and molecular biologists including those interested in cell cycle, mitosis, mechano-biology and nuclear biology.

I am a cell biologist working on mitosis and the cell cycle.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Dantas and colleagues report that confinement is sufficient to restore G2/M transition in cells than can't adhere to their matrix. Exploring further the mechanisms involved, they show that confinement (dynamic cell compression) stimulates nuclear import of cyclin B1 and nuclear envelope permeability using cells in 2D culture. The authors observed that actomyosin contractility increases NE tension in cells preparing for prophase, leading to an increase in nuclear translocation of cyclin B1. However, a few inconsistencies between the data and the conclusion make the current report too preliminary for publication. It may require significant additional work to consolidate the authors' model.

• The specific contribution of Nuclear Envelope tension. The authors conclude that confinement acts through increasing NE tension, although confinement may affect cytoplasmic signaling, which could contribute to G2/M transition. The authors should test whether compressing the nucleus versus compressing the cytoplasm have distinct effects on cyclin B1 nuclear translocation and G2/M, as it has been done by others when addressing nuclear mechanosensitive mechanisms (Elosegui-Artola et al. or Lomakin et al.). To consolidate their model, the authors should also test whether decreasing NE tension (independently of actomyosin tension) has opposite effect on G2/M (for example using LBR overexpression). Increase in nuclear membrane tension has been shown to trigger cPLA2 recruitment to the NE (Enyeidi et al, 2013; Lomakin et al. 2020), although the authors show here that confinement does not induce cPLA2 recruitment (but still increases NE tension figure 4G) in the absence of Rock activity or when the LINC complex is disrupted. This is surprising considering that confinement should increase NE tension independently of actomyosin contractility and should increase cPLA2 recruitment at the NE, unless in this case cPLA2 recruitment is not mediated by an increase in NE tension.
• NPC transport versus NE permeability. The authors suggest that confinement increases cyclin B1 transport via NPC-mediated transport and rule out that confinement may affect NE permeability based on the absence of NE rupture using the INM marker lap2. However, the sample size for this observation is missing and NE permeability could be altered even in the absence of major INM rupture observed by confocal. The authors should use a reporter of nuclear permeability (fluorescent cytoplasmic marker or nuclear marker as previously used by Denais et al or, 2016 or Raab et al., 2016) to make sure that NE permeability is not affected by confinement. In addition, NPC function should be tested in parallel with other fluorescent reporter (such as NLS-GFP constructs) to test whether global NPC-mediated transport is changed during prophase (with or without confinement).
• Effect of confinement on cyclin B transport (NEP) in adherent cells. In figure 1D, we can see that confinement enhances cyclin B1 nuclear translocation in cells adhering on fibronectin. Although it is unclear whether confinement has a significant effect in other figures, for example in figure 2F: DMSO is not significantly different from confiner+CDKi (same thing in 3i and 3j with Rock inhibitor and Kash construct). In these figures the untreated+confiner (or control in 3j) is missing, and the absence of difference between treated+confiner and control is puzzling. Either there is no difference between confiner and CDKi+confiner and it means there is no difference between control and confiner (surprising considering figure 1D); or there is a difference between CDKi+confiner and confiner, indicating that CDK inhibition affects confinement-induced cyclin B import. Both possibilities suggest that the authors should significantly revisit their model. In any case, all control (untreated, treated +/- confiner should be in all figures to avoid any misunderstanding).
• Consequences of cPLA2 recruitment at the NE. The authors state that "Active cPLA2 then stimulates actomyosin contractility creating a positive feedback loop" But the NE is already unfolded and distance between NPR is increased before cPLA2 recruitment. Does PLA2 inhibition affect nuclear irregularity (or distance between NPC)? Or does cPLA2 impact cyclin B1 transport via a distinct mechanism? Did the author analyze CDK1 phosphorylation in presence of PLA2 inhibitor?
• Robustness of the main observation. On page 4, the authors report that cells enter mitosis after 140 sec (+/- 80 sec) of confinement, although in the example showed in figure 1b, the cell enters at least 420 sec min after confinement, as we can see that the cell is already confined -420 sec (compressed shape) and NEP occurs at 0. Did the author showed a cell that was not included in their statistics? This would be very surprising considering the very low sample size used for this experiment (n=6 and 10). In addition, many observations have been made on small sample size (n=6 for figure 1) or/and not from independent experiments. The authors should increase their sample size and compare results from independent experiments to consolidate their model.
• 2h shows nuclear signal (cyclin in grayscale), while 2e does not, why?
• starting point to quantify cyclin entry is the lowest intensity, which may depend on many factors (and could be affected by experimental design). It would be necessary to have synchronized cells to homogenize the starting point of these experiments.
• DN-KASH have been transiently transfected for single cell experiments, how does the authors unsure that cell observed are transfected? Does it have a fluorescent tag, if so which one?
• "requires contact with external stimuli" or "that mechanical confinement is sufficient to overcome the lack of external stimuli." (page 4): external stimuli is vague here and it could be better to replace it with a more specific description

Significance

While the physiological relevance of these findings remain to be determined, the authors report an interesting observation that could have a significant impact in the field. The authors do not comment the potential overlap of their findings with other reports involving the LINC complex (Booth et al., ELife) or CDK-mediated actin remodeling (Ramanathan et al., NCB 2015) during prophase.

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Reply to the reviewers

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

Unlike other cell organelles, mitochondria contain a small fraction of their genetic information. However, most of the genetic information about mitochondrial proteins is still in the cell's nucleus and the localization of the respective proteins to mitochondria is facilitated by localized translation of their mRNAs. In turn, the mRNA localization to the mitochondria is partly due to the co-translational association, via the mitochondrial target sequence (MTS) of the nascent peptide.

The manuscript "Mitochondrial mRNA localization is governed by translation kinetics and spatial transport" investigates the mechanisms of mRNA transport and attachment to mitochondria. Concerning mitochondria-localized mRNAs, two types of mRNAs have been distinguished before: mRNAs that are always attached to the mitochondrium (called "constitutively binding" by the authors) and mRNAs that become "sticky" only under certain conditions (called "conditionally binding" by the authors). Modeling the corresponding cellular processes biophysically, the authors infer that yeast cells exercise control over the localization of mRNA (and consequently over their metabolism) in two ways: via varying the mitochondrial volume fraction, and via varying the speed of translation elongation. Data from previously published genome-wide measurements of mRNAs that localize constitutively and conditionally via their MTS in budding yeast S. cerevisiae were used to investigate these mechanisms.

The manuscript is very well written and the analysis is of high quality. It starts with an introduction that thoroughly reviews many facets around the conducted research and briefly, but self-consistently, summarizes the current knowledge regarding mitochondrial localization of mRNAs. Next, the consequences of the modeling work (presented in the "methods"-section) are explored in the "Results"-section, which contains meaningful and instructive figures and explanations. The manuscript concludes with a comprehensive evaluation of the consequences of the conducted research. All in all, there are only very few minor changes that could be considered.

Content-wise, we suggest:

The modeling of translation kinetics is pretty coarse-grained, using only an average elongation rate per amino acid. Much work in this field was done using totally antisymmetric exclusion principle (TASEP)-based models (e.g. MacDonald, J.H. Gibbs, A.C. Pipkin: Kinetics of biopolymerization on nucleic acid templates; Duc, Saleem, Song: Theoretical analysis of the distribution of isolated particles in totally asymmetric exclusion processes: Application to mRNA translation rate estimation). Perhaps this work can be mentioned, and furthermore, the consequences of inhomogeneity of elongation rate for different codons and amino acids could be explored or at least discussed. In particular, this could shed light into the question if ribosome interference and tRNA charging times have any impact on mitochondrial mRNA localization.

Thank you to the reviewer for pointing us to these relevant papers. As suggested, we have added a paragraph to our Discussion that mentions this work and discusses the possible implications of inhomogeneous elongation along mRNA sequences. We find this suggestion (and the similar one made by the other reviewer) to explore inhomogeneous elongation particularly encouraging, because we are in the early stages of actively pursuing such work. We feel that beyond discussion, exploring the consequences of inhomogeneous elongation is beyond the scope of this work because significant further experimental work would be needed to quantify the impact of specific sequences on translation progress.

To our Discussion, we have added the following paragraph.

"In this work our quantitative model assumed uniform ribosome elongation rates along mRNA transcripts. In the presence of ribosome interactions, such dynamics can lead to both uniform and non-uniform ribosome densities and effective elongation rates along the transcript (MacDonald et al., 1968; Duc et al., 2018). With these uniform ribosome elongation rates, previous theoretical results suggest that collisions will be rare (Duc et al., 2018). However, elongation may not be homogeneous along an mRNA transcript, due to factors such as tRNA availability (Varenne et al., 1984), boundaries between protein regions (Thanaraj and Argos, 1996), amino acid charge (Charneski and Hurst, 2013), and short peptide sequences related to ribosome stalling (Sabi and Tuller, 2017). We have found that slow (homogeneous) elongation facilitates mitochondrial mRNA localization, by providing time for MTS maturation, diffusive search, and to maintain binding-competent MTS-mediated mRNA binding to mitochondria. We expect that inhomogeneities in elongation rate along mRNA could either enhance or reduce mitochondrial mRNA localization, controlled by whether slower elongation is in regions that favor longer MTS exposure. For example, a ribosome stall site following full MTS translation could provide more time for MTS maturation and facilitate mitochondrial localization. Future experimental work could identify such stalling sequences and point towards how modeling can improve understanding of sequence impact on localization."

Ribosome occupancy data from Arava used to infer translation parameters. But there are more recent data sets based on ribosome profiling. Any reason for not using the more recent data?

We thank the reviewer for bringing up this important point. Our text describing the origin of data for ribosome occupancy in the inset of Figure 2A lacked a citation to the dataset used, and we agree that more recent ribosome occupancy datasets are more appropriate. For the cumulative distributions of ribosome occupancy shown in the inset of Figure 2A, we used the ribosome occupancy data from Zid and O'Shea from 2014. The Arava data from 2003 was used for the cumulative distributions of Figure S1, to show that the similarity between conditional and constitutive genes in the inset of Figure 2A was present in more than a single dataset.

We have clarified the origin of the ribosome occupancy data in the text.

In the text description of the inset of Figure 2A, we now include a direct citation of Zid and O'Shea from 2014.

"These measurements (Zid and O'Shea, 2014) indicate that conditional and constitutive genes have similar distributions of ribosome occupancy (Fig. 2A, inset; see Fig. S1 for similar distributions of conditional and constitutive gene ribosome occupancy derived from (Arava et al., 2003))."

We also added a citation of Zid and O'Shea to the caption describing the inset of Figure 2A.

"Inset is cumulative distribution of ribosome occupancy (Zid and O’Shea, 2014), showing ribosome occupancy and β have similar distributions. "

To determine the translation parameters in our quantitative model, we applied the datasets of Couvillion et al from 2016 for relative protein per mRNA measurements and Zid and O'Shea from 2014 for ribosome occupancy measurements, combined with individual measurements from Morgenstern et al from 2016 and Riba et al from 2019. How these datasets and measurements are used is described in the Methods subsection “Calculation of translation rates”. In addition to the citations in the methods, we have added citations to the briefer description in the Results section.

"Using protein per mRNA and ribosome occupancy data (Couvillion et al., 2016; Morgenstern et al., 2017; Zid and O’Shea, 2014; Riba et al., 2019), we estimated the gene specific initiation rate kinit and elongation rate kelong for 52 conditional and 70 constitutive genes (see Methods)."

The effect of the mitochondrial volume fraction on mRNA localization is investigated with a diffusive model. However, the authors make a two dimensional Ansatz for the cell and mitochondrion while it would seem more natural to assume diffusion in three spatial dimensions, as the cell and mitochondria are both three dimensional objects and diffusion strongly depends on the number of dimensions it occurs in. Why was that Ansatz made and why is it justified?

Our diffusion model is in fact three-dimensional, rather than two dimensional. Specifically, we treat the search process as occurring in a three-dimensional cylinder, whose cross-section is shown in Figure 1D. We have added to Figure 1D to further describe how three-dimensional cylinders represent the mitochondrial proximity in the cell.

In the Results, we now write:

“Specifically, we treat the geometry as a sequence of concentric three-dimensional cylinders, each representing an effective region surrounding a tubule of the mitochondrial network. Figure 1D shows a two-dimensional cross-sectional view of these cylinders. The innermost cylinder represents a mitochondrial tubule…”

We have also clarified the caption of Figure 1D to include:

"Schematic of mRNA diffusion in spatial model, shown in cross-section. The cytoplasmic space is treated as a cylinder centered on a mitochondrial cylinder: the three dimensional volume extends along the cylinder axis (not shown)."

The range of variability in the localized fraction +/- CHX is smaller in the experiment compared to the model (Fig. 4B, C). What could be the rationale?

We agree that the variability in localized fraction from applying CHX is smaller in the experiment (Figure 4C) in comparison to the model (Figure 4B). Our model uses translation parameters (initiation and elongation rates) that are derived from experimental measurements that are expected to be quite noisy. We expect that this noise in the model parameters will expand the range of localization changes predicted by the model for CHX application.

In l. 417, the authors remark that "constitutively localized mRNAs are on average longer [...] than conditionally localized mRNAs." Yet constitutively localized mRNAs seem to have higher localized fraction than conditionally localized mRNAs. This is somewhat surprising. While it's clear that a higher diffusivity would be compatible with a faster response time of shorter, conditionally-localized mRNAs, it is not clear how the longer, less diffusive mRNAs would have a higher localization fraction. Perhaps the authors can clarify this point.

The reviewer is correct that experimental measurements show that constitutively-localized genes are, on average, longer than conditionally-localized genes. In our quantitative model, we assume the mRNA of all genes have the same diffusivity. We have used the same diffusivity for different genes because experimental measurements suggest that mRNA length and the number of translating ribosomes on an mRNA do not substantially impact mRNA diffusivity. In our Methods section, we have added citations to papers indicating lack of dependence of mRNA diffusivity on mRNA length.

"Simulated mRNA have a diffusivity of 0.1 𝜇m2/s. This diffusivity remains constant across genes and mRNA states, consistent with experimental measurements showing little dependence of mRNA diffusivity on mRNA length (Calderwood et al., 2016) or number of translating ribosomes (Wang et al., 2016)."

We have additionally clarified the part of our Discussion where we explain the distinction of our results from proposals based on differential mRNA diffusion speed.

"Lower occupancy was proposed to drive mRNA localization through increased mRNA mobility of a poorly loaded mRNA (Poulsen et al., 2019), as more mobile mRNA could more quickly find mitochondria when binding competent, increasing the localization of these mRNA. By contrast, our results imply an alternate prediction – that translational kinetics lead to enhanced localization of longer mRNAs, due to the increased number of loaded ribosomes bearing a binding-competent MTS. Indeed, constitutively localized mRNAs are on average longer than conditionally localized mRNAs."

Minor formal changes would be:

Setting the expressions of the fraction in the binding-competent state in l. 118 and the faction of the mRNA-accessible volume in l. 123 in normal math-environments instead of the inline-environment since they are of key importance to the following discussion.

These two equations (now equations (1) and (2)) are set as distinct equations that are now referred to by their equation numbers later in the manuscript.

l. 414 contains the verb "vary" twice

Thank you to the reviewer for pointing out this redundancy, the sentence now reads

"Translation kinetics can widely vary between genes ... "

l. 438 lacks an "h" in the word mitochondria

Thank you to the reviewer for pointing this out, this spelling error has been corrected. The sentence now reads "all mRNA transcripts studied would be highly localized to mitochondria in all conditions."

Reviewer #1 (Significance (Required)):

All in all, this is a strong manuscript that contains solid, simple but meaningful and by no means oversimplified models with impactful consequences on the understanding of mitochondrial mRNA localization. Furthermore, it is likely that the approach applies to other cellular compartments like the ER. The research is explained in a remarkably clear and focussed style which makes it easy to follow and meanwhile succeeds in not omitting any details.

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

Summary:

Arceo et al. have developed a stochastic, quantitative model of mitochondrial targeting sequence (MTS)-mediated mRNA localization to mitochondria in yeast. They use this model to investigate the role of translation- and diffusion kinetics in controlling mitochondrial mRNA localization of conditional as well as constitutional genes.

Most importantly, they find that neither mRNA diffusivity nor ribosome density alone are sufficient to account for the differences in localization that were experimentally observed for the two types of genes. Therefore, they implement an MTS maturation time into their model and find that they can now predict gene specific localization rates. Based on these observations, the authors conclude that yeast cells can regulate the localization of mRNAs to mitochondria through (controlling mitochondrial volume fractions and) differences in translation kinetics, which adjust the exposure time and numbers of mature MTSs that are presented on the mRNP and convey binding-competence.

Major comments:

Overall, the manuscript is well written and the conclusions are convincing. The underlying assumptions of the model make sense, but I have no background in modelling and can therefore only comment on the RNA biology aspects and general comprehensibility of the work.

• The authors calculate gene-specific translation initiation and elongation rates to model localization on different transcript classes. In this context,

(i) They use a single decay rate to estimate trajectory lifetime and this decay rate is such (1 nt / 600 s) that it would take the average yeast mRNA (~ 1400 nt; Smith et al., JCB, 2015) 10 days to be turned over. This is not consistent with physiological decay rates and as a consequence, they are essentially not accounting for mRNA turnover. This should be explained in the Methods.

The reviewer has highlighted a lack of clarity in our model description. The mRNA decay rate in the model is (1/600) inverse seconds per entire mRNA molecule, rather than (1/600) inverse seconds per nucleotide. This leads the typical mRNA lifetime to be 600 seconds. The sentence in the Methods section describing the decay timescale now reads "The mRNA decay rate is set to kdecay = 0.0017 s-1 per mRNA molecule, such that the typical decay time for an mRNA molecule is 600 s. This decay time is consistent with measured average yeast mRNA decay times ranging from 4.8 minutes (Chan et al., 2018) to 22 minutes (Chia and McLaughlin, 1979)."

(ii) Translation and decay are intrinsically linked and translation machinery also recruits decay enzymes. What is more, decay rates differ greatly for different mRNA transcripts. I cannot judge how feasible this is, but it might benefit the model if variable decay rates (i.e. modelled based on translation efficiency?) could be included.

We appreciate this suggestion from the reviewer. We have added a supplemental figure (Figure S4) to explore how mRNA decay rate can impact mitochondrial localization of mRNA. While longer decay rates have little impact on localization, if the decay rate is sufficiently high, the mRNA will have limited opportunity for translation to initiate and a binding-competent MTS to develop, substantially reducing localization. This analysis does not consider how the mRNA lifetime might be coupled with translational effects (such as ribosome stalling). Accounting for the impact of such more complex decay mechanisms would require substantial expansion of the model and extensive additional experiments to parameterize the coupling effects; we believe this extension would be beyond the scope of this manuscript.

To our Discussion, we have added

"While we have focused on how variation in translational kinetics between genes can impact mitochondrial mRNA localization, there is also significant variation in mRNA decay timescales (Chia and McLaughlin, 1979; Chan et al., 2018). Our model suggests (see Fig. S4) that the mRNA decay timescale has a limited effect on mitochondrial mRNA localization, unless the decay time is sufficiently short to compete with the timescale for a newly-synthesized mRNA to first gain binding competence. We leave specific factors thought to modulate mRNA decay, such as ribosome stalling (Mishima et al., 2022), as a topic of future study."

(iii) Along the same lines: Rare codons as well as specific stalling sequences, are known to slow down translation elongation on many transcripts (and will effectively increase MTS exposure time). Can the authors identify transcripts with such signal sequences (on a global scale, apart from TIM50) and incorporate in their model?

We find this suggestion (and the similar one made by the other reviewer) to explore stalling sequences particularly encouraging, because we are in the early stages of actively pursuing such work. We feel that beyond discussion, exploring the consequences of inhomogeneous elongation is beyond the scope of this work because significant further experimental work would be needed to quantify the impact of specific sequences on translation progress.

To our Discussion, we have added the following paragraph.

"In this work our quantitative model has applied uniform ribosome elongation rates along mRNA transcripts, which with ribosome interactions can lead to both uniform and non-uniform ribosome densities and effective elongation rates along the transcript (MacDonald et al., 1968; Duc et al., 2018). With these uniform ribosome elongation rates, previous theoretical results suggest that collisions will be rare (Duc et al., 2018). However, elongation may not be homogeneous along an mRNA transcript, due to factors such as tRNA availability (Varenne et al., 1984), boundaries between protein regions (Thanaraj and Argos, 1996), amino acid charge (Charneski and Hurst, 2013), and short peptide sequences related to ribosome stalling (Sabi and Tuller, 2017). We have found that slow (homogeneous) elongation facilitates mitochondrial mRNA localization, by providing time for MTS maturation, diffusive search, and maintains a binding-competent MTS-mediated mRNA binding to mitochondria. We expect that inhomogeneities in elongation rate along mRNA could either enhance or reduce mitochondrial mRNA localization, controlled by whether slower elongation is in regions that favor longer MTS exposure. For example, a ribosome stall site after the MTS is fully translated could provide more time for MTS maturation and facilitate mitochondrial localization. Future experimental work could identify such stalling sequences and point towards how modeling can improve understanding of sequence impact on localization."

• Reduced mature MTS exposure time is presented as one of the determining factors that regulate mitochondrial localization of conditionally localized transcripts. For my background, the underlying mechanisms that determine MTS maturation are insufficiently explained. I understand how chaperone recruitment can contribute to MTS maturation. However, it is not obvious to me how receptor binding would account for such long maturation times as the 40 s used here (Fig. 3, 4). I would appreciate if the authors could elaborate and possibly point to directions that their model could be used to study those.

We agree with the reviewer that the diffusive search time for a chaperone to find a newly-synthesized MTS would be very short (a small fraction of the proposed 40-second MTS maturation time), and we expect that this maturation period is largely controlled by chaperone and co-chaperone interaction timescales. There is a wide range of timescales for newly-synthesized (or misfolded) proteins to productively interact with a chaperone, and the literature provides examples of timescales comparable to 40 seconds, which we now cite.

To our Discussion, we have added

"While the diffusive search for a newly-synthesized MTS by chaperones is expected be very fast ( 100 seconds for human chaperone-mediated folding (Wu et al., 2020)."

We feel that modeling chaperone facilitation of MTS folding, to determine the timescale of this process, is very distinct from the topics covered in our manuscript, and thus beyond the scope of this work.

• One of the two main conclusions (at least according to the abstract) from the work is that yeast cells modulate mitochondrial volume fractions to regulate mRNA localization to mitochondria. This is a fact, not a novel finding. The other main conclusion, which is that cells use different translation dynamics to control mRNA localization, is intriguing and deserves more attention. It would be great if the authors could suggest/discuss an experimental approach (i.e. a single mRNA imaging experiment quantifying mitochondrial co-localization and translation kinetics of different reporter constructs) to test this hypothesis.

We appreciate the reviewer raising the point that yeast cells modulate mitochondrial volume fraction to regulate mitochondrial mRNA localization. While we previously showed this relationship between mitochondrial volume fraction and localization, we used experimental techniques (mutations, nutrient sources) that changed many other factors beyond mitochondrial volume fraction. In this work we have used a quantitative model, lacking those extraneous factors, to demonstrate that a change to mitochondrial volume fraction alone can lead to a change in mitochondrial mRNA localization. This work supports our interpretation of those previous experimental results.

To our Discussion we have added the sentence

"Previous experimental work suggested that changing mitochondrial volume fraction could control mitochondrial mRNA localization (Tsuboi et al., 2020) --- our quantitative modeling work provides further support for this mechanism of regulating mRNA localization."

The reviewer also requests a discussion of an experimental approach to test how cells use translational dynamics to control mRNA localization. With the advent of combined mRNA imaging and live translational imaging it would be interesting to directly measure translation in live cells to correlate localization with a time delay. Unfortunately there are currently no published live translational imaging studies in yeast, and thus such a measurement would require the development of the technique in yeast.

To our Discussion, we have added

"Experimentally testing our proposal for translation-controlled localization would involve using combined mRNA and live translational imaging (as yet undeveloped in yeast), to directly measure translation and correlate localization with a time delay, presenting a fruitful pathway for future study."

Minor comments:

• Figure 1: X axis labels between panel E and F are not consistent. Inset in panel F is mainly and first discussed in text. Please do not show data as tiny inset but as separate panel.

We have changed the axis label of Figure 1E to match the axis label of Figure 1G (previously Figure 1F). The inset of the old Figure 1F is now the new Figure 1F, and the old Figure 1F is now the new Figure 1G. We have adjusted the Figure 1 caption and the text description of Figure 1 to match these changes.

Elongation rates of 250 aa per second are not physiological. In mammalian cells elongation has been quantified to proceed between 1 and app. 20 aa per second (Wang et al, 2016; Wu et al., 2016; Yan et al., 2016; Morisaki et al., 2016).

The reviewer is correct that the elongation rates of 50/s and 250/s too large to be physiological. These large values have been deliberately selected to probe the nonequilibrium behavior of the quantitative model to test the prediction of the simpler four-state model, rather than represent physiological behavior.

To the text in the Results section discussing Figure 1F, we have added the following sentence.

"We include unphysiologically high elongation rates to compare to the expected behavior from the 4-state model."

Panel E: elongation rate range does not match Fig 1F nor median in Fig 3A.

The reviewer is correct that the elongation rate parameter range of Figure 1E does not match the elongation rates of Figure 1F or the median in Figure 3A. In Figure 1E, we aimed to show that the physiological range of translation parameters can produce a wide range of both MTSs per mRNA and mRNA binding competence for mitochondria.

We have expanded the description of Figure 1E in the text.

"By exploring the physiological range of translation parameters, many orders of magnitude of the mean number of translated MTSs per mRNA (β, see Eq. 5) are covered, which also covers the full range of mRNA binding competence (Fig.1E). We find that, for any set of physiological translation parameters, the number of binding-competent MTS sequences (β) is predictive of the fraction of time (fs) that each mRNA spends in the binding competent state (Fig.1E)."

• Figure 2A and S1: Please explain how ribosome occupancy is defined here and why it is so different between figures

We have inserted a citation for Zid 2014, to distinguish that the ribosome occupancy measurements in Figure 2A (Zid and O’Shea) and Figure S1 (Arava et al) come from two different techniques. Zid and O’Shea used ribosome profiling to obtain a relative, rather than absolute measurement. While Arava used a technique where they fractioned mRNAs based on the absolute number of ribosomes loaded across 14 fractions of a sucrose gradient, and measured the relative amount of mRNA in each fraction by microarray. So while ribosome occupancy in each paper was calculated in a very distinct manner, the comparison between conditional and constitutively localized mRNAs shows a very similar trend without significant differences in ribosome occupancy between these two classes of mRNAs with either measurement of ribosome occupancy.

To the caption of Figure S1, we have added

"These ribosome occupancy values cover a distinct range, in comparison to those of Fig. 2A, due to distinct experimental measurement techniques."

• Figure 2C: please show experimental data along with model prediction (in the same graph) so that conclusion becomes immediately apparent from figure not just main text. Label clearly (in figure) when experimental and when model data is shown (maybe by using consistent color scheme?)

We have added experimental data to Figure 2C. Throughout the manuscript, we have kept a consistent color scheme for data for mitochondrial localization for ATP3, TIM50, conditional, and constitutive mRNA, whether from model or experimental data. We have applied distinct line types (e.g. solid for model vs. dot-dashed with circles for experimental).

• Figure 4B and C: clearly indicate in figure which are experimental and which are modelled data

In Figures 4B and 4C, we have clarified which data is experimental and which is modeled by adding to the labels for each violin plot. Violin plot labels for model data now read "Model Conditional" or "Model Constitutive" and labels for experimental data now read "Expt Conditional" or "Expt Constitutive".

• Figure 4D: show experimental vs. model data in same graph (at same axis scaling) for comparability

We have added the experimental data, previously in the inset of Figure 4D, to the main part of Figure 4D.

• Line 305: "constitutive" mRNA

Thank you to the reviewer for pointing out this redundancy, the sentence now reads

"Figure 3C shows how the localization for the prototypical conditional and constitutive mRNA varies with the maturation time."

• Line 334: "other changes, such as diffusivity, are unable to separate the two gene groups" - what other changes? The authors only show diffusivity (Fig S3).

Thank you to the reviewer for pointing this out. We have revised this sentence to only refer to diffusivity changes.

"While introduction of this maturation time distinguishes the mitochondrial localization of conditional and constitutive gene groups (Fig. 4A vs Fig. 2B), changes to diffusivity are unable to separate the two gene groups (Fig. S3)."

• Line 403-405: maybe useful to argue against lower ribosome occupancies as drivers of nascent chain complex mobilities: Wang at el, Cell, 2016; single translation site imaging experiments indicating that ribosome occupancy is not the main determinant of mRNP mobility.

We thank the reviewer for the direction to this paper, which indeed indicates that ribosome occupancy has limited impact on mRNA diffusivity.

We now cite this paper in our Methods section.

"Simulated mRNA have a diffusivity of 0.1𝜇m2/s. This diffusivity remains constant across genes and mRNA states, consistent with experimental measurements showing little dependence of mRNA diffusivity on mRNA length (Calderwood et al., 2016) or number of translating ribosomes (Wang et al., 2016)."

• Line 601-607: include experimental references to explain how measures (25 nm vs 250 nm) were determined/selected.

The reviewer raises a valuable point, as it is important to motivate these lengthscales used in the model.

Microscopy with visible light has a lateral resolution limit of approximately 250 nm, often known as the Abbe limit. Accordingly, we assume that mRNA within 250 nm of mitochondria will be measured as adjacent to mitochondria. To the Methods section, we now include a short explanation and a citation.

Unlike the 250-nm diffraction limit, there is no widely-used reaction range for mRNA binding to intracellular substrates, nor a measurement of the required proximity for an MTS-bearing mRNA to bind to mitochondria. We estimate the 25-nm distance for mRNA binding to mitochondria from the following contributions:

• The yeast ribosome is 25 - 28 nm in diameter, or 13 - 14 nm in radius.
• Yeast MTSs have a length of up to 70 amino acids, with 20 estimated yeast MTS lengths having a mean of 31 amino acids. The MTS forms an amphipathic helix (an alpha helix), which has a pitch of 0.54 nm and 3.6 amino acids per turn, so the 31 amino acids will be approximately 5 nm long
• The MTS will be attached to the ribosome/mRNA by other peptide regions, expected to typically be a few nanometers in length So overall we estimate a 25 nm range for an MTS-bearing mRNA to bind to mitochondria.

To our methods, we have added this reasoning and accompanying citations.

"We estimate the 25-nm binding distance by combining several contributions. The yeast ribosome has a radius of 13 - 14 nm (Verschoor et al, 1998). The MTS region, up to 70 amino acids long, forms an amphipathic helix (Bacman et al., 2020) a form of alpha helix. With an alpha helical pitch of 0.54 nm and 3.6 amino acids per turn, a 31 amino acid MTS (the mean of 20 yeast MTS lengths (Dong et al., 2021)) is approximately 5 nm in length. An additional few nanometers of other peptide regions bridging the MTS to the ribosome provides an estimate of 25 nm for the range of an MTS-bearing mRNA to bind mitochondria. The 250-nm imaging distance is based on the Abbe limit to resolution with visible light (Georgiades et al., 2016)."

Reviewer #2 (Significance (Required)):

My field of expertise is the development of single mRNA imaging methods to quantify translation/decay dynamics in living mammalians systems. Thus, I cannot judge the significance of this work with respect to the modelling that is presented here.

However, I do appreciate that one of the main conclusions of this work, which is that cells might use different translation dynamics to control mRNA localization, is truly exciting and could be applied to other types of transcripts (this is exactly what SRP does for ER-targeted mRNAs) as well. Because mechanisms that regulate translation in a transcript-specific manner and in different subcellular localizations have only been described for a handful of cases, I think that this observation is worth following up on and should be appreciated by a broad scientific audience.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Arceo et al. have developed a stochastic, quantitative model of mitochondrial targeting sequence (MTS)-mediated mRNA localization to mitochondria in yeast. They use this model to investigate the role of translation- and diffusion kinetics in controlling mitochondrial mRNA localization of conditional as well as constitutional genes.

Most importantly, they find that neither mRNA diffusivity nor ribosome density alone are sufficient to account for the differences in localization that were experimentally observed for the two types of genes. Therefore, they implement an MTS maturation time into their model and find that they can now predict gene specific localization rates. Based on these observations, the authors conclude that yeast cells can regulate the localization of mRNAs to mitochondria through (controlling mitochondrial volume fractions and) differences in translation kinetics, which adjust the exposure time and numbers of mature MTSs that are presented on the mRNP and convey binding-competence.

Major comments:

Overall, the manuscript is well written and the conclusions are convincing. The underlying assumptions of the model make sense, but I have no background in modelling and can therefore only comment on the RNA biology aspects and general comprehensibility of the work.

• The authors calculate gene-specific translation initiation and elongation rates to model localization on different transcript classes. In this context,
  • (i) They use a single decay rate to estimate trajectory lifetime and this decay rate is such (1 nt / 600 s) that it would take the average yeast mRNA (~ 1400 nt; Smith et al., JCB, 2015) 10 days to be turned over. This is not consistent with physiological decay rates and as a consequence, they are essentially not accounting for mRNA turnover. This should be explained in the Methods.
  • (ii) Translation and decay are intrinsically linked and translation machinery also recruits decay enzymes. What is more, decay rates differ greatly for different mRNA transcripts. I cannot judge how feasible this is, but it might benefit the model if variable decay rates (i.e. modelled based on translation efficiency?) could be included.
  • (iii) Along the same lines: Rare codons as well as specific stalling sequences, are known to slow down translation elongation on many transcripts (and will effectively increase MTS exposure time). Can the authors identify transcripts with such signal sequences (on a global scale, apart from TIM50) and incorporate in their model?
• Reduced mature MTS exposure time is presented as one of the determining factors that regulate mitochondrial localization of conditionally localized transcripts. For my background, the underlying mechanisms that determine MTS maturation are insufficiently explained. I understand how chaperone recruitment can contribute to MTS maturation. However, it is not obvious to me how receptor binding would account for such long maturation times as the 40 s used here (Fig. 3, 4). I would appreciate if the authors could elaborate and possibly point to directions that their model could be used to study those.
• One of the two main conclusions (at least according to the abstract) from the work is that yeast cells modulate mitochondrial volume fractions to regulate mRNA localization to mitochondria. This is a fact, not a novel finding. The other main conclusion, which is that cells use different translation dynamics to control mRNA localization, is intriguing and deserves more attention. It would be great if the authors could suggest/discuss an experimental approach (i.e. a single mRNA imaging experiment quantifying mitochondrial co-localization and translation kinetics of different reporter constructs) to test this hypothesis.

Minor comments:

• Figure 1: X axis labels between panel E and F are not consistent. Inset in panel F is mainly and first discussed in text. Please do not show data as tiny inset but as separate panel. Elongation rates of 250 aa per second are not physiological. In mammalian cells elongation has been quantified to proceed between 1 and app. 20 aa per second (Wang et al, 2016; Wu et al., 2016; Yan et al., 2016; Morisaki et al., 2016). Panel E: elongation rate range does not match Fig 1F nor median in Fig 3A.
• Figure 2A and S1: Please explain how ribosome occupancy is defined here and why it is so different between figures
• Figure 2C: please show experimental data along with model prediction (in the same graph) so that conclusion becomes immediately apparent from figure not just main text. Label clearly (in figure) when experimental and when model data is shown (maybe by using consistent color scheme?)
• Figure 4B and C: clearly indicate in figure which are experimental and which are modelled data
• Figure 4D: show experimental vs. model data in same graph (at same axis scaling) for comparability
• Line 305: "constitutive" mRNA
• Line 334: "other changes, such as diffusivity, are unable to separate the two gene groups" - what other changes? The authors only show diffusivity (Fig S3).
• Line 403-405: maybe useful to argue against lower ribosome occupancies as drivers of nascent chain complex mobilities: Wang at el, Cell, 2016; single translation site imaging experiments indicating that ribosome occupancy is not the main determinant of mRNP mobility.
• Line 601-607: include experimental references to explain how measures (25 nm vs 250 nm) were determined/selected.

Significance

My field of expertise is the development of single mRNA imaging methods to quantify translation/decay dynamics in living mammalians systems. Thus, I cannot judge the significance of this work with respect to the modelling that is presented here. However, I do appreciate that one of the main conclusions of this work, which is that cells might use different translation dynamics to control mRNA localization, is truly exciting and could be applied to other types of transcripts (this is exactly what SRP does for ER-targeted mRNAs) as well. Because mechanisms that regulate translation in a transcript-specific manner and in different subcellular localizations have only been described for a handful of cases, I think that this observation is worth following up on and should be appreciated by a broad scientific audience.

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Referee #1

Evidence, reproducibility and clarity

Unlike other cell organelles, mitochondria contain a small fraction of their genetic information. However, most of the genetic information about mitochondrial proteins is still in the cell's nucleus and the localization of the respective proteins to mitochondria is facilitated by localized translation of their mRNAs. In turn, the mRNA localization to the mitochondria is partly due to the co-translational association, via the mitochondrial target sequence (MTS) of the nascent peptide.

The manuscript "Mitochondrial mRNA localization is governed by translation kinetics and spatial transport" investigates the mechanisms of mRNA transport and attachment to mitochondria. Concerning mitochondria-localized mRNAs, two types of mRNAs have been distinguished before: mRNAs that are always attached to the mitochondrium (called "constitutively binding" by the authors) and mRNAs that become "sticky" only under certain conditions (called "conditionally binding" by the authors). Modeling the corresponding cellular processes biophysically, the authors infer that yeast cells exercise control over the localization of mRNA (and consequently over their metabolism) in two ways: via varying the mitochondrial volume fraction, and via varying the speed of translation elongation. Data from previously published genome-wide measurements of mRNAs that localize constitutively and conditionally via their MTS in budding yeast S. cerevisiae were used to investigate these mechanisms.

The manuscript is very well written and the analysis is of high quality. It starts with an introduction that thoroughly reviews many facets around the conducted research and briefly, but self-consistently, summarizes the current knowledge regarding mitochondrial localization of mRNAs. Next, the consequences of the modeling work (presented in the "methods"-section) are explored in the "Results"-section, which contains meaningful and instructive figures and explanations. The manuscript concludes with a comprehensive evaluation of the consequences of the conducted research. All in all, there are only very few minor changes that could be considered.

Content-wise, we suggest:

The modeling of translation kinetics is pretty coarse-grained, using only an average elongation rate per amino acid. Much work in this field was done using totally antisymmetric exclusion principle (TASEP)-based models (e.g. MacDonald, J.H. Gibbs, A.C. Pipkin: Kinetics of biopolymerization on nucleic acid templates; Duc, Saleem, Song: Theoretical analysis of the distribution of isolated particles in totally asymmetric exclusion processes: Application to mRNA translation rate estimation). Perhaps this work can be mentioned, and furthermore, the consequences of inhomogeneity of elongation rate for different codons and amino acids could be explored or at least discussed. In particular, this could shed light into the question if ribosome interference and tRNA charging times have any impact on mitochondrial mRNA localization.

Ribosome occupancy data from Arava used to infer translation parameters. But there are more recent data sets based on ribosome profiling. Any reason for not using the more recent data?

The effect of the mitochondrial volume fraction on mRNA localization is investigated with a diffusive model. However, the authors make a two dimensional Ansatz for the cell and mitochondrion while it would seem more natural to assume diffusion in three spatial dimensions, as the cell and mitochondria are both three dimensional objects and diffusion strongly depends on the number of dimensions it occurs in. Why was that Ansatz made and why is it justified?

The range of variability in the localized fraction +/- CHX is smaller in the experiment compared to the model (Fig. 4B, C). What could be the rationale?

In l. 417, the authors remark that "constitutively localized mRNAs are on average longer [...] than conditionally localized mRNAs." Yet constitutively localized mRNAs seem to have higher localized fraction than conditionally localized mRNAs. This is somewhat surprising. While it's clear that a higher diffusivity would be compatible with a faster response time of shorter, conditionally-localized mRNAs, it is not clear how the longer, less diffusive mRNAs would have a higher localization fraction. Perhaps the authors can clarify this point.

Minor formal changes would be:

Setting the expressions of the fraction in the binding-competent state in l. 118 and the faction of the mRNA-accessible volume in l. 123 in normal math-environments instead of the inline-environment since they are of key importance to the following discussion.

l. 414 contains the verb "vary" twice

l. 438 lacks an "h" in the word mitochondria

Significance

All in all, this is a strong manuscript that contains solid, simple but meaningful and by no means oversimplified models with impactful consequences on the understanding of mitochondrial mRNA localization. Furthermore, it is likely that the approach applies to other cellular compartments like the ER. The research is explained in a remarkably clear and focussed style which makes it easy to follow and meanwhile succeeds in not omitting any details.

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Reply to the reviewers

REVIEWER #1

Summary:

The manuscript titled "the transcription factor RUNX2 promotes the development of human tissue-resident NK cells" addressed a new role of RUNX2 on human NK cell development and phenotypes. It also provides a new insight into how RUNX2 affects human NK cells switch between the circulatory and tissue-resident NK cells

Major comments:

The authors described that IL-2Rb and other NK cell receptors are not affected in the RUNX2 shRNA system. However, the evidence is not enough to conclude that RUNX2 controls human NK cell development by direct induction of IL-2Rb expression, for the knockdown system did affect the Granzyme B and perforin expression without affecting EOMES and T-bet. More direct evidence should be provided to address the knockdown or knockout system that has a direct induction of IL-2Rb on NK cell development.

You are indeed correct that our conclusion regarding the direct RUNX2-mediated regulation of IL-2Rβ was overstated and that additional experiments needed to be performed in order to validate our strong claims. We tried to demonstrate the direct induction of IL-2Rβ by RUNX2 using the IL-2Rβ reporter construct of Genecopoeia (HPRM30810-LvPM03 with IL-2Rβ promoter sequence, 1585 bp in length, 269bp downstream of TSS). We introduced both this IL-2Rβ reporter vector and the RUNX2-I or empty control LZRS vector in the RUNX2low IL-2Rβlow ALL-SIL cell line to examine whether RUNX2 is able to activate the promoter of IL-2Rβ. Unfortunately, we were unable to generate conclusive results. Since we are unable to definitively demonstrate the direct induction of IL-2Rβ by RUNX2, we have nuanced our statements in the manuscript. Our data still show that RUNX2 affects IL-2Rβ expression in human NK cell development in vitro. We adjusted the text in the manuscript as follows:

• Abstract (page 2 line 9-10)
• Results (page 6 line 110/132-133)
• Discussion (page 10 line 219/page 11 line 273-275).

  In Fig 1e, n is 4-12 for the experiments. Could the authors provide the reason for that? This may increase the bias to use sample number 4 vs. 12. For example, shRNA system d14 of NK cell result may not reflect the truth by 4 vs. 12

The data shown in Figure 1e are the result of multiple experiments using NK cell differentiation cultures, which were performed with transduced umbilical cord blood-derived hematopoietic stem cells (HSC). Whereas the number of samples was indeed different at the different analysis timepoints, the data of the paired control and RUNX2 shRNA/RUNX2-I graphs contain equal sample numbers. So, e.g. both control and RUNX2 shRNA HSC: n=4, while both control and RUNX2 shRNA NK d21: n=12. To illustrate this, I show all individual donor data in the figure as information for the reviewer (see separate uploaded file).

Minor comments:

Fig 1a shows the protein expression level of RUNX 2. Fig 1d shows the qPCR level of RUNX2-1. Could more explanation be provided that ST1 and ST2 have lower mRNA levels but higher protein levels than the d0?

You are indeed correct that the expression levels of RUNX2 in human NK cell developmental stages differ between protein and mRNA levels. However, mRNA levels do not always mirror protein levels, as has also been frequently found in several other studies. Possible causes for this phenomenon include different translation efficiency, protein stability and/or posttranslational modification in different subpopulations of cells. I have included this explanation in the discussion (page 10 line 239-243).

Please check the CCR7 flow data in Fig4a circulatory. The histogram did not reflect the bar plot result. It looks like the expression of CCR4 between Ctrl and RUNX2-1 is different.

Thank you for this remark. I re-examined the data concerning CCR7 and included a more representative biological replicate in the revised figure 4a (see separate figure file).

Please provide more discussion or explanation that the EOMES and T-bet level are not changed in the knockdown system, but the Granzyme B and perforin expression is changed there.

You are indeed correct that despite the unaltered expression T-BET and EOMES, two transcriptional regulators of granzyme B and perforin, RUNX2 knockdown results in the upregulation of these cytotoxic effector molecules. However, as shown by the RUNX2-specific ChIP-seq, granzyme B and perforin are direct targets of RUNX2, which indicates that the expression of these cytotoxic effector molecules can be directly regulated by RUNX2, independent of T-BET and EOMES. I have included this insight in the discussion (page 13 line 338-343).

Fig 5 only showed CD107a+ percentage of NK; how about the CD107a expression level? Based on the current data, CD107a expression did not match with GZMB and PRF. Any explanation for that? PRF and GZMB levels changed in the shRNA system, but K562 cells cannot be killed. Any explanation for the way that happened. How about other target cells or viral infection?

While the percentage of CD107a is significantly reduced when RUNX2 was silenced (Fig. 5b), the expression level of CD107a (MFI) is not significantly altered, neither by knockdown nor by overexpression of RUNX2(-I). Please see the graphs in uploaded file with reviewer comments as information for the reviewer.

Cytoplasmic effector molecule expression in ‘resting’ NK cells and degranulation (cell membrane CD107a expression) upon target recognition are two different processes that are not necessarily similarly regulated. It is possible that NK cells increase expression of cytotoxic effector molecules, while degranulation is reduced. It is known that RUNX2 can act as a transcriptional activator as well as a repressor, depending on the location of the consensus sequence or the type of binding partners in the transcriptional complex. Our hypothesis is that RUNX2 activates expression of cytotoxic effector molecules but reduces degranulation.

One possible explanation for the unaltered cytotoxic potential of RUNX2-silenced NK cells is that, while granzyme B and perforin expression are increased, degranulation is reduced, and these opposite effects might counterbalance each other. Although NK cells with RUNX2 knockdown did not exhibit changes in cytotoxicity towards K562 cells, it does not mean that the same is true for other target cells. However, we did not perform experiments with other target cells or viral infection.

Check the period in line 31. The color is different.

This is adjusted now (see track changes).

Check line 108; it should be "RUNX2 controls human NK cell development."

As indicated in our response to your first major comment, we were not able to demonstrate direct induction of IL-2Rβ by RUNX2, but our data show that RUNX2 affects IL-2Rβ expression in human NK cell development in vitro. We therefore suggest the following title of the paragraph: “RUNX2 controls human NK development possibly by regulating IL-2Rβ expression”

Significance:

Defining the role of Runx2 in NK cell development and functions.

Audience:

Researchers working on transcription factors and NK cell biologists.

REVIEWER #2

Summary:

This is an interesting study that adds new information regarding a role for RUNX2 in NK cell development. Wahlen et al. present very interesting findings highlighting the role for RUNX2 in the acquisition of a tissue-resident phenotype in differentiating NK cells. The authors demonstrate that RUNX2-I isoform is predominantly expressed in specific human NK cells subsets and that RUNX2 upregulates IL-2Rβ expression in NK cell-committed progenitors. Interesting results integrating CHIP-seq and RNAseq data and basic functional studies show that RUNX2 regulates several genes associated with NK cell tissue homing and recirculation. The authors postulate that RUNX2 regulates the acquisition of a tolerogenic tissue-resident phenotype in human NK cells. There are a number of intriguing observations that should be of interest in the field.

Major comments:

While the results obtained are interesting and scientifically sound, the manuscript does not rigorously prove that RUNX2 is involved in NK cell differentiation and development. The results were obtained using human cells ex vivo and in vitro human HSC-based cultures for NK cell differentiation and development. The authors would need a relevant model in vivo to fully characterize phenotypic and functional features of NK cells in the absence or presence of RUNX2. Such studies would be essential, in particular for the acquisition of a tissue-specific resident phenotype in human NK cells in distinct microenvironments. Furthermore, the authors should also modify extensively the title and several statements across the manuscript regarding the role for RUNX2 in NK cell differentiation and development.

Thank you for your very positive comments. We fully agree that an in vivo model is required to study the role of RUNX2 in differentiation of human NK cells and in their acquisition of a tissue-specific resident phenotype in distinct organs. We therefore now performed an in vivo experiment in which we humanised lethally irradiated NSG-huIL-15 mice by intravenous injection of bulk CD34+ CB-derived HSC, which were transduced with either control or RUNX2 shRNA lentivirus. After 6-7 weeks, we analysed the presence of human eGFP+ NK cells (CD45+CD56+CD94+) as well as the frequency of tissue-resident (CD69+CD49e-) and circulating (CD69-CD49e+) human NK cells in the lungs, liver, spleen, bone marrow and lamina propria of the intestine (Figure 6A; Supplementary Figure 5). We found that the absolute number of human NK cells was drastically reduced in all organs of mice injected with RUNX2-silenced HPC compared to those injected with control HPC (Figure 6B). In addition, RUNX2 silencing significantly reduced the frequency of trNK cells in the bone marrow and lamina propria fraction, while it increased the percentage of circNK cells (Figure 6C). These data show that 1) also in vivo RUNX2 is an important transcription factor for human NK cell development and that 2) RUNX2 is involved in human NK cell tissue residency, at least in the bone marrow and in lamina propria of the intestine. With regard to the other examined organs, the frequency of tr- and circNK cells was unaffected by RUNX2 knockdown, except for the spleen where circNK cells were decreased. This suggests that either RUNX2-mediated regulation of NK cell tissue residency is tissue-specific (bone marrow and lamina propria) or that, at least for some organs, this mouse model is not representative for human biology. We have incorporated these new findings in the manuscript as follows:

• Results section (page 8 line 199-212)
• Figure 6 legend (page 30 line 882-891)
• Supplementary Figure 5 (Supplementary materials),
• Discussion (page 13-14 line 354-371).
• Ma____terials and methods (page 21-22 line 570-584). With the new insights that we gained after the additional experiments, we changed the title of the manuscript to ‘The transcription factor RUNX2 drives the generation of human NK cells and promotes tissue residency’. As the reviewer suggested, we also re-evaluated several statements across the manuscript regarding the role of RUNX2 in NK cell differentiation via regulation of IL-2Rβ expression and in promoting tissue residency.

Additional evidence for the direct regulation of IL-2Rβ expression by RUNX2 would be helpful

We fully agree with your comment, which is why we tried to confirm the direct influence of RUNX2 on IL-2Rβ expression using an IL-2Rβ reporter assay. In this assay, we introduced both the IL-2Rβ reporter vector (Genecopoeia vector HPRM30810-LvPM03 with IL-2Rβ promoter sequence, 1585 bp in length, 269bp downstream of TSS), and the LZRS vector with RUNX2-I in a RUNX2low IL-2Rβlow ALL-SIL cell line. Instead of the RUNX2-I vector, control ALL-SIL cells received the empty LZRS vector together with the IL-2Rβ reporter construct. However, due to practical issues, we were unable to generate any conclusive results. Since we are unable to definitively demonstrate the direct induction of IL-2Rβ by RUNX2, we have nuanced our statements in the manuscript. Our data still show that RUNX2 affects IL-2Rβ expression in human NK cell development in vitro. We adjusted the text in the manuscript as follows:

• Abstract (page 2 line 9-10)
• Results (page 6 line 110/132-133)
• Discussion (page 10 line 219/ page 11 line 273-275)

  The studies showing that RUNX2 negatively regulates granzyme B, perforin expression and IFN-γ and TNF-α secretion are intriguing and could be better explored.

Although the role of Runx3 in the transcriptional regulation of granzyme B, perforin, IFN-γ and TNF-α in murine CD8+ T and Th1 cells has been demonstrated, a similar role for Runx2 has not been described yet. For example, a study performed by Olesin et al. (PMID 30264035) showed that although Runx2 plays a role in the generation of murine CD8+ memory T cells, there was no impact on the expression of effector molecules and recall response. Furthermore, the regulation of these NK cell effector molecules by RUNX proteins in human NK cells remains unidentified. I agree that the underlying molecular mechanism of RUNX2-mediated regulation of effector molecule expression is certainly an interesting topic that should be thoroughly investigated. Since there are many mechanisms involved in regulation of the expression and secretion of effector molecules, it is almost a topic on its own and therefore part of a follow-up study.

Minor comments:

"Taken together, we deduce from the data that RUNX2 promotes NK cell development by inducing IL-2Rβ expression and thereby enabling NK lineage commitment" - this is an overstatement

We fully agree with your comment. We have therefore adjusted our statement by concluding that RUNX2 promotes NK cell development in part by regulating IL-2Rβ expression and thereby promoting NK lineage commitment. You can find this adjustment in the discussion on page 11 line 273-274).

"It is well-known that RUNX2 by itself is a relatively weak transcription factor ...." - this statement should be modified.

Our statement that RUNX2 is a weak transcription factor may indeed cause misconceptions. As RUNX2 by itself has a low affinity for DNA, it needs to form a complex with other co-factors such as CBFβ to increase the stability and affinity of the interaction with DNA. You can find the adjusted statement in the discussion (page 11 line 277-278).

Significance:

To date, the role of RUNX2 in NK cell development has not been investigated in mice nor in humans. The findings will contribute to a better understanding of NK cell biology and may help in in improving existing NK cell-based therapies in the future. However, lack of relevant in vivo studies diminishes the importance of this work. Further studies are warranted.

Audience:

Immunologists

Expertise in leukemia pathobiology and immunotherapies.

REVIEWER #3

Summary:

In this study, Wahlen et al. interrogated the role of RUNX2 in regulating human NK cell development through knockdown and overexpression studies. In agreement with previous work, the authors observed high RUNX2 expression in NK cell progenitors and a decline in expression levels in mature subsets. RUNX2 knockdown and overexpression was performed through viral transduction of cord blood-derived HPCs that were subsequently differentiated into NK cells in vitro. The authors found that RUNX2 knockdown led to a reduction in the numbers of mature NK cells, while overexpression had the opposite effect. They also provide data suggesting that RUNX2 may directly promote expression of the beta chain of the IL-2 receptor during NK cell development. The authors also performed RNA-seq on sorted RUNX2 knockdown and overexpressing cells and compared this data to RNA-seq datasets that were generated using tissue-resident NK cells from liver and bone marrow. They identified Gene Set Enrichment signatures that were similar between tissue-resident NK cells and NK cells overexpressing RUNX2. Changes in the expression of several genes associated with circulation and residency were confirmed by flow cytometry. Finally, the authors performed function assays and found that manipulation of RUNX2 did not affect cytotoxicity, but overexpression reduced inflammatory cytokine production.

Major comments:

The title of the paper (The transcription factor RUNX2 promotes the development of human tissue-resident NK cells) presents too strong of a conclusion that is not sufficiently supported by the data. While the NK cells differentiated in vitro with RUNX2 overexpression do appear to share a transcriptional signature with tissue-resident subsets and express receptors associated with tissue residency, the authors did not perform any adoptive transfer experiments showing that RUNX2 overexpressing NK cells are actually tissue resident. Such experiments would be necessary to support the conclusion stated in the title.

Indeed, since the original manuscript contained only data obtained from in vitro differentiation cultures, the concept of NK cell tissue residency required validation in an in vivo system. We therefore performed an in vivo experiment, in which we humanised lethally irradiated NSG-huIL-15 mice by intravenous injection of bulk CD34+ CB-derived HSC, which were transduced with either control or RUNX2 shRNA lentivirus. After 6-7 weeks, we analysed the presence of human eGFP+ NK cells (CD45+CD56+CD94+) as well as the frequency of tissue-resident (CD69+CD49e-) and circulating (CD69-CD49e+) human NK cells in the lungs, liver, spleen, bone marrow and lamina propria of the intestine (Figure 6A; Supplemental Figure 5). We found that the absolute number of human NK cells was drastically reduced in all organs of mice injected with RUNX2-silenced HPC compared to those injected with control HPC (Figure 6B). In addition, RUNX2 silencing significantly reduced the frequency of trNK cells in the bone marrow and lamina propria fraction, while it increased the percentage of circNK cells (Figure 6C). These data show that 1) also in vivo RUNX2 is an important transcription factor for human NK cell development and that 2) RUNX2 is involved in human NK cell tissue residency, at least in the bone marrow and in lamina propria of the intestine. With regard to the other examined organs, the frequency of tr- and circNK cells was unaffected by RUNX2 knockdown, except for the spleen where circNK cells were decreased. This suggests that either RUNX2-mediated regulation of NK cell tissue residency is tissue-specific (bone marrow and lamina propria) or that, at least for some organs, this mouse model is not representative for human biology. We have incorporated these new findings in the manuscript as follows:

• Results section (page 8 line 199-212)
• Figure 6 legend (page 30 line 882-891)
• Supplementary Figure 5 (Supplementary materials),
• Discussion (page 13-14 line 354-371).
• Ma____terials and methods (page 21-22 line 570-584). With the new insights that we gained after the additional experiments, we changed the title of the manuscript to ‘The transcription factor RUNX2 drives the generation of human NK cells and promotes tissue residency’. As the reviewer suggested, we also re-evaluated several statements across the manuscript regarding the role of RUNX2 in NK cell differentiation via regulation of IL-2Rβ expression and in promoting tissue residency.

The authors used RNA-seq data from tissue-resident NK cells in comparisons with their RUNX2 knockdown and overexpressing NK cells. Do they see elevated RUNX2 transcript levels in tissue-resident NK cells? I don't know if matched circulating NK cell data is available, but such a finding would further strengthen the connection between the tissue residency profile and RUNX2.

Thank you for your very valid comment. We re-investigated the public RNA-seq data of tissue-resident and circulatory NK cells of liver (Cuff et al.) and bone marrow (Melsen et al.). These data sets show that in the liver and bone marrow, RUNX2 transcript levels are indeed elevated in tissue-resident NK cells compared to circulatory NK cells. The fold changes of RUNX2 in liver and bone marrow tissue-resident versus circulatory NK cells are 25 and 13, respectively. This supports our hypothesis and we have included this in the results on page 7 line 159-163

The evidence that RUNX2 controls human NK cell development by direct induction of IL-2Rbeta expression is fairly weak. In Figure 2a, it appears as though RUNX2 knockdown didn't significantly affect IL-2Rbeta expression, and RUNX2 overexpression only affected IL-2Rbeta expression at day 7 (not day 14). Furthermore, in Figure 2b, RUNX2 knockdown did not impact IL-2Rbeta expression in YTS cells. The authors speculate that residual RUNX2 may be sufficient to drive IL-2Rbeta expression. This could be tested by knocking out RUNX2 with a CRISPR-Cas9 system. The authors also provide some ChIP-seq data showing that RUNX2 binds to the promoter region of IL2RB in human PBNK cells but do not provide any ChIP data showing enhanced enrichment of RUNX2 within IL2RB in their RUNX2 overexpressing cells.

Indeed, RUNX2 knockdown did not result in significant changes of IL-2Rβ expression in NK cell progenitors or in the YTS cell line, which we attributed to residual RUNX2 expression. As suggested by the reviewer, we attempted to knockout RUNX2 in the YTS cell line using the CRISPR-Cas9 system (Synthego) to investigate the effect on IL-2Rβ expression. However, we were unsuccessful to obtain cells that lacked RUNX2 expression. So at this point we cannot state that RUNX2 is essential for IL-2Rβ expression in human NK cells or their progenitors.

The reviewer is also correct that the percentage of IL-2Rβ+ stage 3 cells upon RUNX overexpression in HSC was significantly increased on day 7, whereas this was no longer the case on day 14. However, this is not a counterargument for a regulating role of RUNX2 in IL-2Rβ expression as the subpopulation of stage 3 cells that expresses IL-2Rβ+ are NK cell-committed progenitors, that will probably have differentiated into stage 4 or stage 5 NK cells on day 14. This is in agreement with the increased absolute cell numbers of stage 4 and stage 5 NK cells in the RUNX2 overexpression cultures on day 14. We could not perform ChIP-seq on RUNX2 overexpressing stage 3 cells as this technique requires large cell numbers, which are not feasible to generate in vitro.

Thus, although we do not state that RUNX2 is essential for IL-2Rβ expression, our data from the RUNX2-I overexpression model and RUNX2-specific ChIP-seq do provide evidence for a certain degree of RUNX2-mediated regulation of IL-2Rβ expression during human NK cell development. We therefore downgraded our statements regarding this matter in the manuscript as follows:

• Abstract (page 2 line 9-10)
• Results (page 6 line 110/132-133)
• Discussion (page 10 line 219/page 11 line 264-275). Minor comments:

No minor comments

Significance:

As an NK cell biologist suggest returning for major revision and re-evaluation.

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Referee #3

Evidence, reproducibility and clarity

In this study, Wahlen et al. interrogated the role of RUNX2 in regulating human NK cell development through knockdown and overexpression studies. In agreement with previous work, the authors observed high RUNX2 expression in NK cell progenitors and a decline in expression levels in mature subsets. RUNX2 knockdown and overexpression was performed through viral transduction of cord blood-derived HPCs that were subsequently differentiated into NK cells in vitro. The authors found that RUNX2 knockdown led to a reduction in the numbers of mature NK cells, while overexpression had the opposite effect. They also provide data suggesting that RUNX2 may directly promote expression of the beta chain of the IL-2 receptor during NK cell development. The authors also performed RNA-seq on sorted RUNX2 knockdown and overexpressing cells and compared this data to RNA-seq datasets that were generated using tissue-resident NK cells from liver and bone marrow. They identified Gene Set Enrichment signatures that were similar between tissue-resident NK cells and NK cells overexpressing RUNX2. Changes in the expression of several genes associated with circulation and residency were confirmed by flow cytometry. Finally, the authors performed function assays and found that manipulation of RUNX2 did not affect cytotoxicity, but overexpression reduced inflammatory cytokine production.

Major comments:

1.The title of the paper (The transcription factor RUNX2 promotes the development of human tissue-resident NK cells) presents too strong of a conclusion that is not sufficiently supported by the data. While the NK cells differentiated in vitro with RUNX2 overexpression do appear to share a transcriptional signature with tissue-resident subsets and express receptors associated with tissue residency, the authors did not perform any adoptive transfer experiments showing that RUNX2 overexpressing NK cells are actually tissue resident. Such experiments would be necessary to support the conclusion stated in the title.

2.The authors used RNA-seq data from tissue-resident NK cells in comparisons with their RUNX2 knockdown and overexpressing NK cells. Do they see elevated RUNX2 transcript levels in tissue-resident NK cells? I don't know if matched circulating NK cell data is available, but such a finding would further strengthen the connection between the tissue residency profile and RUNX2.

3.The evidence that RUNX2 controls human NK cell development by direct induction of IL-2Rbeta expression is fairly weak. In Figure 2a, it appears as though RUNX2 knockdown didn't significantly affect IL-2Rbeta expression, and RUNX2 overexpression only affected IL-2Rbeta expression at day 7 (not day 14). Furthermore, in Figure 2b, RUNX2 knockdown did not impact IL-2Rbeta expression in YTS cells. The authors speculate that residual RUNX2 may be sufficient to drive IL-2Rbeta expression. This could be tested by knocking out RUNX2 with a CRISPR-Cas9 system. The authors also provide some ChIP-seq data showing that RUNX2 binds to the promoter region of IL2RB in human PBNK cells but do not provide any ChIP data showing enhanced enrichment of RUNX2 within IL2RB in their RUNX2 overexpressing cells.

Significance

As an Nk cell biologist suggest returning for major revision and re-evaluation.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This is an interesting study that adds new information regarding a role for RUNX2 in NK cell development. Wahlen et al. present very interesting findings highlighting the role for RUNX2 in the acquisition of a tissue-resident phenotype in differentiating NK cells. The authors demonstrate that RUNX2-I isoform is predominantly expressed in specific human NK cells subsets and that RUNX2 upregulates IL-2Rβ expression in NK cell-committed progenitors. Interesting results integrating CHIP-seq and RNAseq data and basic functional studies show that RUNX2 regulates several genes associated with NK cell tissue homing and recirculation. The authors postulate that RUNX2 regulates the acquisition of a tolerogenic tissue-resident phenotype in human NK cells. There are a number of intriguing observations that should be of interest in the field.

Major comments:

-While the results obtained are interesting and scientifically sound, the manuscript does not rigorously prove that RUNX2 is involved in NK cell differentiation and development. The results were obtained using human cells ex vivo and in vitro human HSC-based cultures for NK cell differentiation and development. The authors would need a relevant model in vivo to fully characterize phenotypic and functional features of NK cells in the absence or presence of RUNX2. Such studies would be essential, in particular for the acquisition of a tissue-specific resident phenotype in human NK cells in distinct microenvironments. Furthermore, the authors should also modify extensively the title and several statements across the manuscript regarding the role for RUNX2 in NK cell differentiation and development.

-Additional evidence for the direct regulation of IL-2Rβ expression by RUNX2 would be helpful

-The studies showing that RUNX2 negatively regulates granzyme B, perforin expression and IFN-γ and TNF-α secretion are intriguing and could be better explored.

Minor comments:

-"Taken together, we deduce from the data that 238 RUNX2 promotes NK cell development by inducing IL-2Rβ expression and thereby enabling 239 NK lineage commitmen" - this is an overstatement

-"It is well-known that RUNX2 by itself is a relatively weak transcription factor ...." - this statement should be modified.

Significance

To date, the role of RUNX2 in NK cell development has not been investigated in mice nor in humans. The findings will contribute to a better understanding of NK cell biology and may help in in improving existing NK cell based therapies in the future. However, lack of relevant in vivo studies diminishes the importance of this work. Further studies are warranted.

Audience: immunologists

Expertise in leukemia pathobiology and immunotherapies.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript titled "the transcription factor RUNX2 promotes the development of human tissue-resident NK cells" addressed a new role of RUNX2 on human NK cell development and phenotypes. It also provides a new insight into how RUNX2 affects human NK cells switch between the circulatory and tissue-resident NK cells.

Major comments:

1.The authors described that IL-2Rb and other NK cell receptors are not affected in the RUNX2 shRNA system. However, the evidence is not enough to conclude that RUNX2 controls human NK cell development by direct induction of IL-2Rb expression, for the knockdown system did affect the Granzyme B and perforin expression without affecting EOMES and T-bet. More direct evidence should be provided to address the knockdown or knockout system that has a direct induction of IL-2Rb on NK cell development.

2.In Fig 1e, n is 4-12 for the experiments. Could the authors provide the reason for that? This may increase the bias to use sample number 4 vs. 12. For example, shRNA system d14 of NK cell result may not reflect the truth by 4 vs. 12.

Minor comments:

1.Fig 1a shows the protein expression level of RUNX 2. Fig 1d shows the qPCR level of RUNX2-1. Could more explanation be provided that ST1 and ST2 have lower mRNA levels but higher protein levels than the d0?

2.Please check the CCR7 flow data in Fig4a circulatory. The histogram did not reflect the bar plot result. It looks like the expression of CCR4 between Ctrl and RUNX2-1 is different.

3.Please provide more discussion or explanation that the EOMES and T-bet level are not changed in the knockdown system, but the Granzyme B and perforin expression is changed there. Fig 5 only showed CD107a+ percentage of NK; how about the CD107a expression level? Based on the current data, CD 107a expression did not match with GZMB and PRF. Any explanation for that? PRF and GZMB levels changed in the shRNA system, but K562 cells cannot be killed. Any explanation for the way that happened. How about other target cells or viral infection?

4.Check the period in line 31. The color is different.

5.Check line 108; it should be "RUNX2 controls human NK cell development."

Significance

Defining the role of Runx2 in NK cell development and functions.

Audience: Researchers working on transcription factors and NK cell biologists.

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Reply to the reviewers

We would like to thank the reviewers for their positive and constructive reviews. We have already addressed their major concerns by including additional screen and control data, especially in the new Figure 7, supplemental figures 3 and 4 and new Table S1. We also detail the planned experiments that we propose to perform to address their remaining comments. Some points are mentioned in both section 2 and 3 of the revision plan.

2. Description of the planned revisions

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

Reviewer #1

• Fig 4 and 5. ARL-8 is localized to lysosomes, phagolysosomes and early endosomes. How about TORC and BORC subunits?*

We plan to acquire images of our endogenously tagged BORC subunit SAM-4::mSc on the polar body phagolysosome. We also crossed SAM-4::mSc to a GFP::RAB-5 early endosomal marker and plan to cross it to a CTNS-1::mCit lysosomal marker and will characterize their colocalization.

To look for the localization of TORC1, we requested a recently published strain with a single-copy transgene encoding a fluorescently tagged DAF-15/RAPTOR (AK Sewell et al., iScience 2022), but there is no fluorescence visible in live embryos. We are currently staining these strains to test for any embryonic expression, but it is not uncommon for transgenes to undergo germline silencing, even single-copy transgenes. To observe TORC1 localization in early embryos, it may be necessary to create a knock-in strain which would take a couple of months to generate and another month to cross to various reporters and analyze.

We predict that TORC1 and BORC will localize to lysosomes and phagolysosomes, consistent with previous literature (Sancak et al. Cell 2010, Pu et al. Dev Cell 2015).

• Figure 6 *

*Authors need to establish knockout cell lines by picking up single drug-resistant colonies and characterize each line by western blot or immunofluorescent microscopy. *

We have been successful in creating stable mutant cell lines for Myrlysin and Lyspersin using CRISPR/Cas9 and are currently characterizing these lines before performing direct assays for phagolysosomal vesiculation.

1. b) While the authors monitored cell growth every 3 hours for 4 days, the authors showed the result of day 4 only. Time lapse data would be useful.

We plan to replace the RBC-overfeeding experiment with more direct evidence for phagolysosomal vesiculation (see 3c below).

1. *c) The effect of KO may be because of defects in phagolysosomes. However, the authors cannot conclude "phagolysosomal vesiculation is affected in mammalian cells" or not until they directly observe the phenomena. *

We plan to feed our newly isolated Myrlysin and Lyspersin mutant cell lines with RBCs and use a stage-based analysis at defined time points to test how the size and shape of the phagolysosomes change over time, similar to Fig. 1a-c in R Levin-Konigsberg et al. Nature Cell Biol 2019. This experiment will assess the effect of these genes directly on phagolysosomal vesiculation rather than general phagolysosome function.

Reviewer #1 (Significance):

This study shows the mechanism [involvement of TORC-BORC-ARL8 pathway] is conserved in phagolysosomes as well in worms. As described above, the involvement of these molecules in the mammalian phagolysosomes is not convincing at this stage.

We plan to provide direct evidence for the involvement of BORC by using stable mutant cell lines and directly monitoring phagolysosome vesiculation, as described above.

**Referees cross-commenting**

*I fully agree with the reviewer #2 that identification of arl8 effectors will make this paper more attractive as I described in my original peer review. Moreover, I agree with the reviewer that genetic data in C. elegans is convincing. *

As RNAi targeting UNC-116 disrupts embryonic development, including the birth of the polar body during meiosis, we generated a ZF1 degron-tagged UNC-116 allele to test the role of Kinesin-1 in phagolysosomal vesiculation. We are currently characterizing this strain and crossing it to polar body markers. We predict that degron-mediated degradation of UNC-116 will start during the 4-cell stage, which is after polar body birth but well before the onset of phagolysosome vesiculation. This new unc-116::mCitrine::ZF1 will provide us with a tool to more specifically test the role of UNC-116 in phagolysosome vesiculation in the context of a developing embryo.

* While reviewer #2 have not concerned about the quality of experiments, I'm still not convinced by their mammalian cell experiments. I don't have any more concerns if the authors (1) remove the mammalian study or (2) improve the quality of mammalian data. *

We hope that our planned experiments with the isolated mutant cell lines will address the reviewer’s concern. Otherwise, we can remove the mammalian experiments.

Reviewer #2

**Referees cross-commenting**

The mammalian work … assays general phagolysosome function rather than directly addressing vesiculation.

We hope that our planned experiments with the isolated mutant cell lines will directly demonstrate a role in phagolysosomal vesiculation.

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

*Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty. *

Reviewer #1

1. • It is very difficult to understand which molecules are TORC, BORC and/or BLOC subunits, which molecules are required and which are not required. * It is very helpful if the authors include a table showing the summary of RNAi and mutant phenotypes. We have added Table S1, summarizing our findings with different protein complexes and previous findings regarding lysosome and synaptic vesicle precursor trafficking.

2. Figure 6 ** a) There are many concerns in mammalian cell experiments. It is not clear whether the knockout procedures really work or not. … *

We performed genotyping for the pooled lines and found high editing efficiency leading to frame-shifts in Arl8B (>96%) and BLOC1S1 (>85%), as well as Cathepsin B (>67%). These data are now included in supplementary figure S4.

As the downstream of ARL8 remains elusive in this study, it is unclear how phagolysosomes are tubulated (Fig 6D model).

ARL8 has been shown to interact with kinesins, dyneins, and the HOPS complex directly or through bridging molecules such as PLEKHM or RUFY proteins.

Using the reference allele e1265 of the KIF1 ortholog UNC-104, which causes a severe paralysis phenotype, we observed no effect on phagolysosomal vesiculation (new Fig. S3A) or polar body degradation (new Fig. S3B).

We next used the partial loss-of-function wy270 allele of the KIF5 ortholog UNC-116 but observed no effect on phagolysosomal vesiculation (new Fig. S3A). There was however a mild delay in polar body degradation (new Fig. S3B), leading us to develop a degron-tagged UNC-116 allele to be able to better analyze the role of UNC-116 in phagolysosomal biology (described in section 2).

We have also included data using RNAi and mutant alleles to test a role for PLEKHM family proteins CUP-14 and RUB-1. We observed no effect on phagolysosomal vesiculation (new Fig. S3A) or polar body degradation (new Fig. S3B). In preliminary data (n=3), knocking down rub-1 in a cup-14 mutant background had no effect on phagolysosomal vesiculation (new Fig. S3A), but sped up polar body degradation (new Fig. S3B). These data are inconsistent with PLEKHM proteins having a role in phagolysosomal vesiculation.

BLAST searches revealed no clear homologs for RUFY proteins in C. elegans.

Based on reviewer #2’s suggestion, we also examined a role for the HOPS complex by knocking down the HOPS subunit VPS-41. Human VPS41 has been shown to bind ARL8b (Khatter et al JCS 2015). Treating worms with vps-41 RNAi resulted in normal phagolysosomal vesiculation (new Fig. 7A) but did result in a significant delay in polar body degradation (new Fig. 7B-C). Interestingly, disappearance of small phagolysosomal vesicles was significantly delayed (new Fig. 7D), while corpse membrane breakdown within the large phagolysosome was unaffected (new Fig. 7E). As corpse membrane breakdown depends on RAB-7-mediated fusion of lysosomes (Fazeli et al., Cell Rep 2018) and HOPS promotes lysosomal fusion (JA Nguyen & RM Yates, Front Immunol 2021), these data suggest that VPS-41 and HOPS are preferentially required for lysosome fusion to small phagolysosomal vesicles and are not necessary for lysosome fusion to the large phagolysosome.

Thus, we screened through the known ARL-8 effectors and the identity of the downstream effector(s) of ARL-8 involved in phagolysosomal vesiculation remain elusive. As the kinesin and PLEKHM data were negative, we had opted not to include it in the original manuscript, but now discuss it in the main text and present it in Fig. 7 and Fig. S3.

Reviewer #2

It would be good if the authors could speculate further as to why mTORC1 is required for Arl8 activity but not recruitment, and if there are further experiments that could augment this conclusion they might be helpful.

We added a new hypothesis to the discussion of how TORC1 might affect a downstream effector of ARL-8. Unfortunately, we have not yet been able to identify any ARL-8 effectors involved in phagolysosome vesiculation to be able to test this hypothesis experimentally.

*The authors could consider making the study more extensive by applying their simple but elegant system to further possible players in the pathway, and in particular to test some possible Arl8 effectors. Although there is no clear orthologue of PLEKHM2 in C. elegans, both the HOPS complex and PLEKHM1 have been reported to bind to Arl8. *

As potential SKIP/PLEKHM-related proteins that link ARL8 to kinesins, we screened two RUN and PH domain-containing proteins, CUP-14 and RUB-1, for their role in phagolysosome resolution. Phagolysosome vesiculation was normal and resolution was not delayed in cup-14(cd32) or rub-1(RNAi) mutants or after treating cup-14 mutants with rub-1 RNAi (Fig. S3A-B). These data are now discussed in the main text and included as a supplementary figure.

To test a role for the HOPS complex, best known for its role in lysosome fusion, we tested whether RNAi knockdown of the HOPS-specific subunit VPS-41 disrupted or delayed phagolysosome vesiculation. Vps41 has been shown to bind ARL8b (Khatter et al. JCS 2015). HOPS knockdown did not affect phagolysosome vesiculation (new Fig. 7A), but significantly delayed polar body degradation (Fig. 7B-C). In particular, vps-41 knockdown delayed the degradation of phagolysosomal vesicles (Fig. 7D), probably by affecting fusion of these small vesicles to additional lysosomes. These data are now discussed in the main text and included as a supplementary figure.

**Referees cross-commenting**

*One approach might to drop the mammalian studies, and instead add an investigation of more Arl8 effectors in C. elegans. Hopefully, few people would doubt the relevance to mammals of studies in C. elegans on the function of well conserved proteins. *

We hope to strengthen the relevance of our findings across species to increase the impact of our work. Therefore, we plan to replace the RBC-overfeeding experiment in Fig. 6 with direct evidence for phagolysosomal vesiculation using established cell culture assays similar to Fig. 1a-c in R Levin-Konigsberg et al. Nature Cell Biol 2019 and newly isolated BORC mutant cell lines.

We added details on our screen for ARL-8 effectors to the manuscript, including new figures (Fig. S3 and Table S1). While the effectors involved in phagolysosomal vesiculation remain a mystery, we were able to distinguish different requirements for HOPS during corpse membrane breakdown and phagolysosomal vesicle resolution, suggesting that HOPS is critical for the lysosomal fusion of small phagolysosomal vesicles, but not the large cell corpse phagosome.

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Referee #2

Evidence, reproducibility and clarity

The authors have previously used C. elegans early development to establish an elegant model system with which to investigate process by which the content of phagolysosomes is degraded and the structure resolved. This phagocytosis plays a central role in the clearance of dead cells and pathogens and so the work is likely to be of widespread interest to those working in both C. elegans and mammalian phagocytic cells like macrophages. The authors have previously shown that the tubulation and fragmentation of the phagolysosome is important for both degradation of contents and resolution of the phagolysosome, and have identified the small GTPase Arl8 and the mTor kinase as being required. This study investigates the relationship between these components and also adds further players to the pathway. In summary, they show that there is a pathway starting with amino acid release and going through mTORC1 and then the BORC complex that is known to activate Arl8. They show that only some subunits of BORC are required (and not the related BLOC complex with which is shares some subunits), and that Arl8 needs to cycle between its GDP- and GTP-bound states to exert its effects. They also examine the membrane recruitment of Arl8 and make two interesting findings. Firstly, mTORC1 is required for Arl8 activity but not its localisation, possibly suggesting that mTORC1 is required for the activity of a critical Arl8 effector. Secondly, they find that when BORC is removed, Arl8 is recruited to endosomes, which implies the existence of second, as yet unknown, GEF for Arl8 that acts on endosomes.

Significance

Overall the data are clear and convincing, with many conclusions based on genetic mutations, and the results carefully quantified. There seems little required to be done to improve the experiments that are presented, although it would be good if the authors could speculate further as to why mTORC1 is required for Arl8 activity but not recruitment, and if there are further experiments that could augment this conclusion they might be helpful.

My only substantial suggestion, is that the authors could consider making the study more extensive by applying their simple but elegant system to further possible players in the pathway, and in particular to test some possible Arl8 effectors. Although there is no clear orthologue of PLEKHM2 in C. elegans, both the HOPS complex and PLEKHM1 have been reported to bind to Arl8. Thus it would be interesting to see if either of these is required in this process and at what step. If suitable mutants are available, then hopefully these experiement would take c 2-3 months and be relatively inexpensive as they would involve worm breeding and fluorescent-microscopy.

My expertise includes membrane traffic and small GTPases but not phagocytosis or C.elegans.

Referees cross-commenting

The mammalian work is rather brief but it does seem to have involved collaborators with relevant experience. Nonetheless, it assays general phagolysosome function rather than directly addressing vesiculation. One approach might to drop the mammalian studies, and instead add an investigation of more Arl8 effectors in C. elegans. Hopefully, few people would doubt the relevance to mammals of studies in C. elegans on the function of well conserved proteins.

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Referee #1

Evidence, reproducibility and clarity

Summary

Phagocytosis is fundamental to innate immunity and tissue homeostasis. C. elegans is a good system to study phagolysosomal dynamics. Here, Fazeli et al. study the molecular mechanism of phagosysosomal tubulation and vesiculation using C. elegans. The authors show the involvement of TORC in the vesiculation of phagolysosomes (Fig 1). Upstream regulatior of TORC would be amino acid release because knockdown of slc-36.1 decreased the number of fission events. BORC is also required for phagolysosome vesiculation (Fig 2). Interestingly, essential subunits are different from synaptic vesicle transport and lysosomal transport. ARL-8, a small GTPase downstream of BORC, is also essential for phagolysosome vesiculation (Fig 3). The nucleotide cycle of ARL-8 is essential for the localization of ARL-8 on phagolysosomes (Fig 4). BORC is required for the vesicular localization of ARL-8 (Fig 5). Finally the authors performed an experiment to show this pathway is conserved in mammalian macrophages (Fig 6).

Genetic experiments in worms are solid while mammalian cell experiments are not. This reviewer thinks the authors need to improve the quality of cell line experiments.

Major comments

1. A lot of components are analyzed in this paper. Then, it is very difficult to understand which molecules are TORC, BORC and/or BLOC subunits, which molecules are required and which are not required. It is very helpful if the authors include a table showing the summary of RNAi and mutant phenotypes. It is very helpful if the table include lysosomal phenotypes and synaptic vesicle phenotypes as well.
2. Fig 4 and 5. ARL-8 is localized to lysosomes, phagolysosomes and early endosomes. How about TORC and BORC subunits? Are there differences in the localization of essential subunits and non-essential subunits?
3. Figure 6
   • a) There are many concerns in mammalian cell experiments. It is not clear whether the knockout procedures really work or not. Methods section says the authors pooled puromycin resistant cells. This is not general protocol to establish knockout cell lines. Generally, some drug resistant cells are not always complete KO. Authors need to establish knockout cell lines by picking up single drug-resistant colonies and characterize each line by western blot or immunofluorescent microscopy.
   • b) While the authors monitored cell growth every 3 hours for 4 days, the authors showed the result of day 4 only. Time lapse data would be useful.
   • c) The effect of KO may be because of defects in phagolysosomes. However the authors cannnot conclude "phagolysosomal vesiculation is affected in mammalian cells" or not until they directly observe the phenomena.

Significance

TORC-BORC-ARL8 pathway has been shown in lysosomal transport in mammalian cells (Pu et al, 2015, 2017). It has been shown that BORC is required for the localization of ARL8 in the case of worm synaptic vesicles and mammalian lysosomes (Pu et al, 2015; Niwa et al., 2016). This study shows the mechanism is conserved in phagolysosomes as well in worms. As described above, the involvement of these molecules in the mammalian phagolysosomes is not convincing at this stage.

In the case of lysosomes and synaptic vesicles, the effector of ARL8 (downstream motors) has been shown (Pu et al., 2015; Niwa et al., 2016). It is interesting observation that the nucleotide cycle of ARL8 is essential for the phagolysosomal fission. However, as the downstream of ARL8 remains elusive in this study, it is unclear how phagolysosomes are tubulated (Fig 6D model).

Referees cross-commenting

I fully agree with the reviewer #2 that identification of arl8 effectors will make this paper more attractive as I described in my original peer review. Moreover, I agree with the reviewer that genetic data in C. elegans is convincing. While reviewer #2 have not concerned about the quality of experiments, I'm still not convinced by their mammalian cell experiments. I don't have any more concerns if the authors (1) remove the mammalian study or (2) improve the quality of mammalian data.

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Reply to the reviewers

We thank the referees for their valuable suggestions. We have revised the text accordingly and already conducted most of the requested experiments.

Reviewer #1

• 1. The authors state that addition of mannan increases length of Birbeck granules however, no data are presented. It would make this more convincing when the length is compared between conditions with and without mannan (as shown in Fig 4, where the condition without mannan is lacking).

Reply: Thank you for pointing out the missing data. We added an EM image of Birbeck granules and quantification of Birbeck granules formation in the absence of mannan (Figure 4A-D).

• Supp, fig 1B perhaps as a panel in main figure as this is an important control to show that Birbeck granules are isolated.

Reply: We moved the supplemental figure 1B to main figure 1D.

• 1. Only the(total) length of Birbeck granules is taken into account, but not the number of Birbeck granules. Is it possible to quantify the number of Birbeck granules.

Reply: We added Figure 4D to show the number of Birbeck granules. Note that the difference in the number of Birbeck granules was less significant than that of total length because there were numerous short fragments in the mutant specimen.

• Fig 5. Only the condition (ARGK) where there is virtually no Birbeck granules formation is included, however, is virus still internalized in the other conditions (MRGD or MRGK) as Birbeck granule formation was less effective but still present? It would be interesting to include those mutants. A more specific quantification would be by p24 ELISA. Is there a reason why immunoblotting has been chosen? In the supernatant condition, explain why the virus p24 seems less in the control condition whereas one would expect max concentration in that condition.

Reply: Thank you for suggesting the use of ELISA. We chose immunoblotting because of its higher sensitivity and lower cost. But ELISA is advantageous when it comes to comparing large number of samples. We performed p24 ELISA and quantified the virus internalization in all the mutants available (Figure 5C). As you pointed out, the transfer efficiency of the immunoblot in Figure 5A was not uniform across the membrane; Pr55 bands became denser toward the right, while p24 bands had a gradient in the opposite direction. The immunoblots and ELISA showed that about ~1% of the viruses were attached or internalized and ~99% did not interact with the cells. Thus, the attached/internalized viruses did not affect the amount of viruses in the supernatant. Results of ELISA also showed the amount of viruses in the supernatant were nearly equal among the samples (Figure S3B).

• Abstract First sentence: not mucosal tissue but mucosal epithelium Last sentence: Virual should be viral

Reply: We corrected the typo. Thank you.

• Discussion The last section comparing DC-SIGN and langerin is not clear and some overstatements are made. "Considering that DC-SIGN serves as an attachment receptor for viruses but not as an entry receptor, the possible structural coupling of lateral ligand binding and internalization implies that langerin functions as a more efficient entry receptor for viruses than DC-SIGN or other C-type lectins." It is not correct that langerin but not DC-SIGN can function as an entry receptor. DC-SIGN has been shown to facilitate infection of different viruses such DENV and ZIKV. In contrast, langerin can restrict viruses such as HIV-1 but also facilitate infection for example Influenza A and DENV. So attachment or entry is more likely a consequence of the internalization and dependence on pH changes for fusion as some viruses such as DENV fuse in acidic vesicles. This needs to be discussed more clearly.

Reply: Thank you for pointing out our wrong statement. We replaced the statement with weakened one as below:

Page 13, line 213: “The difference in the ligand-binding manner between langerin and DC-SIGN may contribute to their different carbohydrate recognition preferences (Valverde et al., 2020; Takahara et al., 2004).“

Reviewer #2 1) Langerin can exist on the cell surface and in Birbeck granules. They should examine langerin cell surface expression in the 3 states, wildtype, mutated and lectin - . Do the mutations change cell surface expression?

Reply: We performed surface labeling experiments and showed that those mutations did not affect surface expression of langerin (Figure S3A).

2) Birbeck granules are present in the absence of mannan and pathogens (see Pena-Cruz JCI 2018, PMID: 29723162). Thus, this suggests that Birbeck granules are present even without langerin clathrin coated pit internalization from the cell surface. How does their model account for this observation?

Reply: We think there are two possibilities:

1. Birbeck granules were shown to stem from the endoplasmic reticulum (Valladeau et al Immunity 2000; Lenormand et al PlosONE 2013). Since the rER is the site of glycosylation, langerin is likely to capture the oligo-mannose-glycosylated proteins within the rER and form Birbeck granules.
2. Blood plasma proteins such as immunoglobulin D, immunoglobulin E, and apolipoprotein B-100 are reported to carry high-mannose glycans (Clerc et al Glycoconj J. 2016). Those glycoproteins in the cell culture media can induce Birbeck granule formation.

   3) Different cell types can have varied Langerin levels (see Pena-Cruz JCI 2018, PMID: 29723162). Is Birbeck granule formation depend on certain level of langerin expression? Do Birbeck granules form when Langerin is present at low as compared to high levels?

Reply: In the course of the experiments, we isolated a cell line stably expressing langerin. However, langerin expressing cells were extremely slow in proliferation and the expression levels were low. To answer this question, we recovered this “failed” stable cell line and found that the low langerin-expressing cells can form Birbeck granules, but with lower efficiency (Figure S3C-E).

4) Authors use immunoblots to show that HIV is present in intra-cellular Langerin structures. It would be ideal to visualize HIV with presumably internal Birbeck granules using imaging techniques such as cryo-electron micrography or another form of high resolution imaging.

Reply: We are currently working on ultra-thin section electron microscopy of HIV-infected langerin-expressing cells. Visualization of HIV-containing Birbeck granules using cryo-electron microscopy is highly challenging because the current precision of cryo-FIB-SEM milling technique is too low to target a specific intracellular structure. We believe conventional electron microscopy will provide sufficiently convincing evidence that HIV is present within Birbeck granules.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, investigators used cryo-electron tomography to reconstruct the structure of langerin and langerin composed organelle, termed Birbeck granule. They find that langerin trimers interact via carbohydrate binding cleft, mediated via 258 - 262 residues. Mutations in the residue prevent Birbeck granule structures. They propose a molecular structure for HIV binding and internalization.

Significance

This is highly interesting work with significance for understanding pathogen, such as HIV, recognition and clearance in mucosal antigen presenting cells.

I am not an expert in structural studies but the cryo-electron tomography is impressive and convincing. I have concerns with some of the HIV - Birbeck granule aspects. Cell transfected with langerin and mutated langerin were exposed to HIV pseudotypes. They show that HIV binding occurs in the absence of mannan with both wildtype and mutated langerin. On the other hand, a langerin that lacks calcium binding does not bind virus (lectin -). They show that the mutated langerin has limited internalization, presumably because of lack of Birbeck granule formation.

1. Langerin can exist on the cell surface and in Birbeck granules. They should examine langerin cell surface expression in the 3 states, wildtype, mutated and lectin - . Do the mutations change cell surface expression?
2. Birbeck granules are present in the absence of mannan and pathogens (see Pena-Cruz JCI 2018, PMID: 29723162). Thus, this suggests that Birbeck granules are present even without langerin clathrin coated pit internalization from the cell surface. How does their model account for this observation?
3. Different cell types can have varied Langerin levels (see Pena-Cruz JCI 2018, PMID: 29723162). Is Birbeck granule formation depend on certain level of langerin expression? Do Birbeck granules form when Langerin is present at low as compared to high levels?
4. Authors use immunoblots to show that HIV is present in intra-cellular Langerin structures. It would be ideal to visualize HIV with presumably internal Birbeck granules using imaging techniques such as cryo-electron micrography or another form of high resolution imaging.

All microbiologists, immunologists, and investigators interested in infectious disease will be interested in this work.

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Referee #1

Evidence, reproducibility and clarity

The authors here have used cryo-electron tomography, 3D reconstruction and modelling on isolated Birbeck granules to provide a molecular mechanism for langerin-induced Birbeck granule formation. Their data revealed a structure of the repeating unit of the honeycomb lattice of langerin in Birbeck granules. Their model suggests that the interaction between the two langerin trimers is mediated by docking the flexible loop at residues 258-262 into the secondary carbohydrate-binding cleft. Mutational analysis within the loop suggests that these interactions are important for Birbeck granule formation and virus internalization.

The results presented in the manuscript are very interesting and propose an novel mechanism how langerin induces Birbeck granule formation and how two langerin trimers are able to interact with virus and induce Birbeck granule formation.

Comments.

Fig. 1. The authors state that addition of mannan increases length of Birbeck granules however, no data are presented. It would make this more convincing when the length is compared between conditions with and without mannan (as shown in Fig 4, where the condition without mannan is lacking).

Supp, fig 1B perhaps as a panel in main figure as this is an important control to show that Birbeck granules are isolated.

Fig. 4. Only the(total) length of Birbeck granules is taken into account, but not the number of Birbeck granules. Is it possible to quantify the number of Birbeck granules.

Fig 5. Only the condition (ARGK) where there is virtually no Birbeck granules formation is included, however, is virus still internalized in the other conditions (MRGD or MRGK) as Birbeck granule formation was less effective but still present? It would be interesting to include those mutants. A more specific quantification would be by p24 ELISA. Is there a reason why immunoblotting has been chosen? In the supernatant condition, explain why the virus p24 seems less in the control condition whereas one would expect max concentration in that condition.

Minor comments

Abstract First sentence: not mucosal tissue but mucosal epithelium Last sentence: Virual should be viral

Discussion The last section comparing DC-SIGN and langerin is not clear and some overstatements are made. "Considering that DC-SIGN serves as an attachment receptor for viruses but not as an entry receptor, the possible structural coupling of lateral ligand binding and internalization implies that langerin functions as a more efficient entry receptor for viruses than DC-SIGN or other C-type lectins." It is not correct that langerin but not DC-SIGN can function as an entry receptor. DC-SIGN has been shown to facilitate infection of different viruses such DENV and ZIKV. In contrast, langerin can restrict viruses such as HIV-1 but also facilitate infection for example Influenza A and DENV. So attachment or entry is more likely a consequence of the internalization and dependence on pH changes for fusion as some viruses such as DENV fuse in acidic vesicles. This needs to be discussed more clearly.

Significance

There is little known about the molecular mechanism of birbeck granule formation and the role of langerin as well as its ligand (HIV or mannan). here the authors convincingly reveal a mechanism which is corroborated by mutational analyses. This is important in the field. the major drawback which is that a cell-line has been used, 293T, and overexpression of langerin. I understand the reason (manipulation in other cells more difficult, no good LC cell-lines, primary cells probably impossible) but it makes the significance a bit less. overall this is a significant contribution to the field.

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Reply to the reviewers

We are grateful for the referees' rigorous review of our manuscript and for their overall positive reception of our work. We have pasted below the entirety of the reviewers’ comments, interleaved with our responses.

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

In this manuscript, Gama et al. use a biophysical assay DAmFRET, structural analysis, and optogenetic tools to uncover the nucleation mechanism of CBM signalosome. They performed experiments first in yeast cells that lack death folds or related signaling networks, then confirmed their discoveries in human cells. The results presented here are clear and convincing. The paper is very well presented and clearly written.

They found it is the CARD domain of BCL10 that acts as a molecular switch that drives all-or-none activation of NF-kB. Monomeric BCL10 possesses an unfavorable conformation and serves as a nucleation barrier, keeping BCL10 in a supersaturated inactive state that allows for binary activation upon stimulation.

They also characterized CARD9 CARD domain and a coiled-coil region. They reasoned that CARD9CARD functions as a polymer seed to nucleate BCL10, and that the coiled-coil region has multimerization ability to facilitate nucleation. Furthermore, they characterized that MALT1 activation doesn't depend on BCL10 polymers but its own proximity. And MALT1 induces graded NF-kB activation, thus further demonstrating the binary activation is conferred by BCL10.

Major comments:

1. Fig S1D and E, the authors used TNF-a to activate NF-kB independent of CBM signalosome and found the activation in each cell increased with dose. In contrast, CBM activation led to bimodal cell activation. The authors claim that this is evidence that positive feedback upstream of NF-kB. We do not believe this claim can be made from this comparative experiment alone. We agree that positive feedback is important for activating an NF-kB response, but the comparison between CBM and TNFa is inaccurate and glosses over published data. Specifically, there is published data that TNF-a does activate a 'switch-like' or digital response, as defined by the translocation of p65 (see (Tay et al. 2010) among other studies that have examined p65 translocation at the single-cell level). The difference in T-sapphire expression between CBM and TNF activation is most likely due to TNFa induced oscillations of p65 translocation (although this is speculation on our part). Therefore we suggest to the authors that the TNF-a data (Fig S1D and E) should be omitted, as the claim of switch or not-switch as pertains to TNF signaling is more complex and nuanced than presented here. We believe omitting this data will strengthen the manuscript and avoid confusion in the field. The bimodal expression of the T-sapphire NF-kB reporter driven by the CBM signalosome activation is sufficient to claim an all-or-none response.

We thank the reviewer for this suggestion. We acknowledge that the activation of NF-κB by TNF-ɑ is more complex than we had presented, and agree that the differences in T-Sapphire reporter output could be attributed to p65 oscillations. We had not previously considered this interesting possibility -- which is not addressed by the present data -- believe it is worth future investigation. As suggested by the reviewer, we have now omitted the TNF-a data, and agree that this change does not impact the overall claims of the paper.

Fig 3B, the authors introduced CARD9CARD-µNS as a stable condensed seed for BLC10. However, considering CARD9CARD can form polymers at high concentration (Fig 3B and S3D), are these high expression levels of CARD9CARD able to induce BCL10-mEos3.1 assembly (as measured by DamFRET in yeast cells)? Can the authors examine BCL10 FRET at these high expression level of CARD9CARD? We assume that BCL10 will be assembled in these cells. This would provide a valuable control experiment and support the author's conclusions.

Indeed, this question is amenable to DAmFRET. Accordingly, we have now performed DAmFRET of yeast cells expressing Bc10-mEos3.1 in the presence of either CARD9CARD-mCardinal or mCardinal itself (see new Fig S6A and B, and associated results section). We confirmed that cells with high CARD9CARD-mCardinal expression had higher FRET on average than cells with low expression. Importantly, cells expressing high or low levels of mCardinal itself had the same FRET level (Fig S6).

Fig 3C, the text said "Whereas WT CARD9CARD assembled into polymers at high concentration, the pathogenic mutants R18W, R35Q, R57H, and G72S failed to do so (Fig 3C and S7B,C), explaining why they cannot nucleate BCL10". This claim that these mutants can not nucleate BCL10 does not have a figure call out or a reference. The authors then show the results in Fig 3E which supports this claim. Even though they were done in the context of full-length CARD, all proteins contain the I107E mutation that releases autoinhibition. For clarity, the authors should consider rearranging the text to avoid explaining a phenomenon and making conclusions before showing the results.

We have now rearranged this section to match the figures and claims.

Fig 4D, E and Video 1, the authors showed the nucleation of BCL10 into puncta within live cells is followed by p65 translocation to the nucleus. The authors claim that 'this result suggests that BCL10 is indeed supersaturated prior to stimulation' (paragraph 2 section titled BCL10 is endogenously supersaturated'). We fail to understand how this live-cell experiment leads to the conclusion BCL10 is supersaturated before stimulation. We think this text should be deleted from the text, or put into context with the DAmFRET data that lead the authors to make this claim. It would be interesting for the authors to define in discussion what are the golden criteria to claim a protein exists in a supersaturated state with live cells (by microscopy or other methods)? Adaptor protein assembly into puncta and the subsequent nuclear translocation of transcription factors is a common phenomenon across signalling pathways. Not all these pathways rely on signaling adaptors existing in a supersaturated state. The field of cell signaling (and cell biology in general) would benefit from a detailed definition of how these physical-chemical definitions of proteins are supported by experimental data. We believe that this paper will become a seminal paper in the field, and future work will benefit from a clear definition of how a claim of supersaturation is derived from the data.

We appreciate that the concept of supersaturation will be foreign to many biologists, and welcome this opportunity to elaborate. We have now rephrased the corresponding results section for figure 4D, E, and have added new evidence to support our claim that BCL10 is supersaturated, as had been requested by reviewer 2 (see below in response to point 1). Supersaturation, as we (correctly) use the term, occurs when the concentration of a protein in solution exceeds its equilibrium solubility for the given conditions. The term is also sometimes used to describe __global __protein “concentrations” in excess of the solubility limit, even if a dense phase has already formed and potentially depleted the effective concentration (in solution) to the solubility limit. This is a key distinction, as only the former implies a high-energy out-of-equilibrium scenario that predetermines a future change -- release of the excess energy via phase separation.

How does one experimentally determine if a protein is supersaturated? In theory, one may conclude that a protein is supersaturated if its assembly causes a net loss of energy from the system (i.e. exothermic). Unfortunately, it is likely not yet possible to perform such measurements with sufficient sensitivity inside a living cell. However, it is possible to infer that a protein is supersaturated if assembly can be shown to occur without a net input of energy to the system, i.e. without any change in thermodynamic control parameters such as temperature, pH, post-translational modifications, concentration of the protein, or concentration of any interacting factor. To do this, one introduces a substoichiometric amount of pre-assembled protein to the system. This manipulation will trigger assembly if the protein is supersaturated. If the protein is instead subsaturated, assembly will not occur and the exogenously added assemblies will simply dissolve. This phenomenon, known as “seeding” in the prion field, is considered a golden criterion sufficient to conclude that a protein has prion behavior. However, because bona fide prions additionally require a means for dissemination between cells, seeding analyzed at the cellular rather than population level is more appropriately considered a sufficient criterion for supersaturation (which is a prerequisite for classical prion behavior (Khan et al. 2018)). Our CARD9CARD-Cry2 experiment was designed to test this criterion. Specifically, it allowed us to introduce a seed independently of receptor activation, thereby precluding any orthogonal cellular response that might lower Bcl10 solubility through e.g. a post-translational change. That the seeds were substoichiometric is evidenced by the fact that Bcl10 polymerized homotypically following stimulation (i.e. it didn’t just bind to the CARD9CARD puncta, but went on to deposit onto itself).

How does assembly under this scenario differ in principle from the many examples of puncta formed by other signaling proteins that occur upon stimulation of their respective pathways? Puncta formation that is induced by a thermodynamic change in the cell cannot be said to have resulted from pre-existing supersaturation. Rather, the stimulus may have caused some change that either increases the effective concentration of the protein (e.g. upregulates its expression, induces a post-translational change that activates it, or releases an inhibitory factor) or reduces solvent activity (e.g. change in pH).

An additional requirement (necessary but not sufficient) is that the assembly must be regular with respect to some order parameter. That is to say, it must be a bona fide “phase”. At a minimum, this implies a uniform density. Additionally, for supersaturation to persist over biological timescales under physiological conditions and confinement volumes, the assembly (once formed) must also have structural repetition in at least two dimensions, i.e. crystallinity (Rodríguez Gama et al. 2021; Zhang and Schmit 2016). We know this to be true for Bcl10.

Rodríguez Gama A, Miller T, Halfmann R. 2021. Mechanics of a molecular mousetrap-nucleation-limited innate immune signaling. Biophys J 120:1150–1160. doi:10.1016/j.bpj.2021.01.007

Khan, T., Kandola, T.S., Wu, J., Venkatesan, S., Ketter, E., Lange, J.J., Rodríguez Gama, A., Box, A., Unruh, J.R., Cook, M., et al. (2018). Quantifying nucleation in vivo reveals the physical basis of prion-like phase behavior. Mol. Cell 71, 155-168.e7.

Zhang L, Schmit JD. 2016. Pseudo-one-dimensional nucleation in dilute polymer solutions. Phys Rev E 93:060401. doi:10.1103/PhysRevE.93.060401

Regarding the supersaturated state of BCL10, the authors convincingly use optogenetics to show how transient assemblies of CARD-Cry2 can template BCL10 assembly. This is a convincing experiment that shows templated nucleation of BCL10. To strengthen the claim that BCL10 is supersaturated endogenously we suggest the author quantify the expression of BCL10-mScarlet and CARD-Cry2 and ideally show that this phenomenon can be observed at expression levels equivalent to endogenous.

As stated above, that BCL10-mScarlet formed polymers that we observed to elongate homotypically off of the CARD9CARD seeds indicates that the protein was supersaturated under the conditions of the experiment. The concentration of CARD9 is not a relevant parameter in this case. We had already compared the expression of BCL10-mScarlet to endogenous BCL10 in 293T, THP-1, and human fibroblast cells by quantitative immunodetection (Fig. S10D), revealing that the expression level of our BCL10-mScarlet constructs matched that of endogenous BCL10, which was approximately the same in all cell lines. We also compared the distribution of expression levels of BCL10-mScarlet versus that of endogenous BCL10 using antibody staining followed by flow cytometry, which confirmed that the range of expression levels of BCL10-mScarlet falls within that of endogenous BCL10 in 293T cells (Fig. S10F). Hence, we believe our data suffice to conclude that Bcl10 is supersaturated at endogenous levels of expression.

Minor comments:

1. Special character "delta" is not displayed in the text (instead only a space).

This error occurred upon exporting the manuscript from our text editor to a PDF. We now have made sure all special characters are present in the PDF version.

Several cell lines including mouse, human, and yeast lines were used across this manuscript. It would be clearer and more helpful if the exact cell type of the line could be indicated. Such as, "BCL10-mEos3.1 yeast cells" instead of "BCL10-mEos3.1 cells", "BCL10-mScarlet HEK293T cells" instead of "BCL10-mScarlet cells".

We have now modified all instances to indicate the origin of the cell lines tested.

Fig 5B, the authors indicated that BCL10 colocalized with CARD9CARD, then please show the merged image as well.

We have now included the merged image to indicate colocalization in the inset images.

Fig 6E, authors claimed that cells were stimulated with blue light for the indicated durations. The longest duration is 12 hours. Please specify if it was continuous exposure or several rounds of exposure in the indicated durations.

We have now specified in the figure legends, text, and methods section, that this specific experiment used a continuous exposure of blue light.

Reviewer #1 (Significance (Required)):

This work used a combination of FRET and optogenetic tools to engineer CBM signaling and visualize the effects. They incorporated knowledge from structure biology, together with their results from mutations and truncations, dissected the significance of each protein in CBM signalosome, and demonstrated in detail how higher-order assemblies make all-or-none cellular decisions. We believe this paper will be a seminal paper in the field of cell signalling and cytoplasmic organization. It defines a new paradigm of macromolecules assembly of signalling complexes as being dependent on protein existing in a supersaturated state. Importantly this paper opens up new questions regarding macromolecular signaling complexes (found in many innate immune signaling pathways): How is protein supersaturation maintained and used throughout evolution to construct biochemical signalling switches?

This paper will be of particular interest to scientists working on immunity and cell signalling, especially in the field of higher-order assemblies. However, we feel the impact of this paper goes beyond these fields, and we believe this manuscript will be of broad interest to the cell biology and biophysics communities. For reference, our expertise is in innate immunity and cell biology.

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

In their manuscript entitled "A nucleation barrier springloads..." Rodriguez-Gama et al. dissect the assembly mechanism of the signalosome, composed of the proteins CARD9, BCL10 and MALT1, using a novel in-cell biophysical approach (DAmFRET). They first overexpressed fluorescently tagged versions of the proteins to promote their assembly in yeast and mammalian cells, finding that CARD9 forms higher order assemblies across a wide range of concentrations with no discontinuity in the DAmFRET profile. In contrast, the DAmFRET profile of BCL10 showed a clear separation between monomers and higher order assemblies, which started to form spontaneously only at higher BCL10 concentrations. Furthermore, at the two states of the proteins co-exist at all concentrations. These observations imply that there is a nucleation barrier to forming BCL10 assemblies. MALT1 showed no change in FRET regardless of its expression level. These observations, alongside fluorescence microscopy of the assemblies, and previous structural studies, suggest that BCL10 forms self-templating polymers that act as a switch for an all-or-nothing immune response, assayed in this case by monitoring the nuclear translocation of the NF-kB subunit p65. The authors also assessed the effects of known disease-causing mutations on the nucleation barrier, showing that changes in the strength of the nucleation barrier can have major effects on signalosome function. Finally, they used optogenetic methods to trigger assembly of individual signalosome components, providing insight into the minimal components/conditions required for signalosomes to work.

Major comments

Overall, the experiments by Rodriguez-Gama et al. offer convincing evidence that there is a nucleation barrier to BCL10 polymerisation, and that a CARD9 template is sufficient to overcome the barrier. Although the existence of a nucleation barrier had already been postulated, based on structural and other studies (referenced by the authors), it had lacked a rigorous demonstration. This work provides that demonstration, which is important for the signalosome field and more broadly applicable to researchers studying cellular decision making. The study further demonstrates that DaMFRET is an excellent to study protein assembly processes in their native environment, allowing the authors to tackle a question that would have been technically very difficult to address otherwise. The optogenetic experiments are a nice sufficiency test for their ideas.

We feel there are a few key points to address before publication.

1) One of the main conclusions is that spring-loading the nucleation barrier with high super-saturating BCL10 concentrations allows a decisive response. Although much of the data strongly imply this conclusion, the dependence of the immune response on BCL10 concentration was not tested directly. A key prediction of the nucleation barrier is that at concentrations below saturation, BCL10 should not be able to induce an all-or-nothing response when stimulated. At saturated/super-saturated concentrations BCL10 should be able to induce a response. At deeply super-saturated concentrations the response should start to be activated spontaneously in the absence of an external stimulus. These predictions could be tested using the doxycycline-inducible BCL10 system (Figure S2D), without establishing major new experimental avenues. We feel that such an experiment would strengthen the main conclusion. It might also help to shed light on whether being highly supersaturated enables a more decisive response than being just saturated.

This is a great idea. As the reviewer suggested, our Doxycycline-inducible BCL10 system enables us to induce and track the state of BCL10 over time. We have now performed the requested experiments (Fig. S9D, E) and incorporated the results into the relevant section of the text. In short, our new analyses show that BCL10 indeed has a concentration threshold for activation by stimulation, and that it can also nucleate spontaneously when overexpressed. Note that our original analyses in Fig. 4B and C also demonstrate spontaneous BCL10 activation at high concentrations. With this new evidence and the orthogonal approaches used in Fig. 5, we believe our data definitively support our conclusion that BCL10 is supersaturated.

2) Intuitively, readers might expect that if BCL10 is supersaturated then, once nucleated, it would rapidly assemble at the nucleation sites. In Figure 5B, CARD9CARD-miRFP670nano-Cry2 assemblies are optically induced throughout the cell. However, BCL10 appears to nucleate at just a few sites with a few minutes delay. More widespread nucleation and growth of BCL10 polymers seems to take longer (20-40 minutes, Figures 5B and 5C), after CARD9CARD-miRFP670nano-Cry2 has disassembled. Furthermore, in Figures 4D and 4E, very few BCL10 assemblies are visible/quantifiable after 70 minutes PMA exposure, but p65 has clearly entered the nucleus. It looks like BCL10 assembly slightly lags behind p65 nuclear entry. Can the authors provide a more detailed explanation of these kinetics?

We do note that the number of CARD9CARD clusters formed upon opto-stimulation exceeds the apparent number of BCL10 nucleation sites. We believe this is consistent with nucleation-limited kinetics, where the clustering of CARD9-CARD increases the local probability of nucleation. As nuclei form and grow, they lower the probability of subsequent nucleation elsewhere in the cell. Additionally, it is possible that our artificial seeds do not perfectly mimic the native CARD9 seeds that form upon natural stimulation (e.g. due to potential steric interference from the fluorophore and Cry2). We also acknowledge that there is a slight delay in the visible appearance of BCL10 polymers relative to p65 nuclear translocation. We expect that MALT1 activates already when the polymers are still too small to see (sub-resolution), whereas the polymers only become microscopically visible once they’ve grown quite a bit more.

3) Related to point 2 above, in Figure 5D, the leftmost cell in the field of view clearly contains CARD9CARD assemblies but there are no BCL10 assemblies and p65 is not imported into the nucleus (in contrast to the central cell in the field of view). How often does CARD9CARD optogenetic assembly lead to BCL10 assembly? In other words, can the authors quantify the cell-to-cell variability in this experiment?

Throughout our experiments, whether analyzing BCL10 puncta formation, NF-kB transcriptional activity, or p65 translocation, we observed a persistent nonresponsive fraction of cells even at saturating levels of stimulation. Specifically, approximately 30% of THP-1 cells failed to acquire T-Sapphire fluorescence or form BCL10-mEos3.2 puncta when stimulated with high levels of β-glucan (Fig 1B and E, respectively), and approximately 25% of 293T cells failed to acquire T-Sapphire fluorescence or exhibit p65 nuclear translocation when stimulated with high levels of PMA (Fig 1C and Fig 4E, respectively). Because these numbers did not depend on whether BCL10 was endogenously or exogenously expressed, we know that the underlying cell-to-cell heterogeneity involves factors upstream of BCL10. Indeed, the fraction of recalcitrant cells drops to 10% in our optogenetic experiments that bypass upstream factors (Fig S11E). Possible sources of heterogeneity include different physiological states of the cells or fluctuations in the expression levels of any upstream factor in the signaling pathway. We believe that this phenomenon is not unique to the CBM signalosome, as we (unpublished) and others (Fernandes-Alnemri T et al, 2009, Dick M et al, 2016) have similarly observed a fraction of non-responding cells upon activation of the inflammasome, which involves nucleation-limited polymerization of the adaptor protein ASC. While this phenomenon is interesting and may be important to our understanding of the full complexity of signalosomes in vivo, we believe that identifying the source of heterogeneity would be outside the scope of the present manuscript. We now describe this phenomenon in the final paragraph of the “Endogenous BCL10 is constitutively supersaturated” section.

Fernandes-Alnemri, T., Yu, JW., Datta, P. et al. AIM2 activates the inflammasome and cell death in response to cytoplasmic DNA. Nature 458, 509–513 (2009). https://doi.org/10.1038/nature07710

Dick, M., Sborgi, L., Rühl, S. et al. ASC filament formation serves as a signal amplification mechanism for inflammasomes. Nat Commun 7, 11929 (2016). https://doi.org/10.1038/ncomms11929

Minor comments

While the work is scientifically well done, the text reads as though it is meant for experts rather than a broad audience. This is a pity because it risks alienating readers. We suggest that some adjustments to the text (mainly additional explanations and not ruling out alternative interpretations of the data) would widen the audience and increase the impact of this important study. Below are some suggestions that might help.

1. In the first results section, the authors write: 'This suggests that Bcl10 but not CARD9 assembly occurs in a highly cooperative fashion that could, in principle (Koch, 2020), underlie the feed forward mechanism.' It isn't obvious how Figure 1 leads to this statement. Could the authors give a more detailed explanation?

We have now revised the text to elaborate on this interpretation.

One limitation of DAmFRET is that it can only detect a nucleation barrier where there is a difference in FRET between the monomer and the assembled form of the protein. However, it can't necessarily detect when there is not a nucleation barrier i.e. if there's no difference in FRET. The text seems to suggest that CARD9 and MALT1 don't have nucleation barriers to their assembly. While this might not be intentional, it would be helpful to explicitly state that CARD9 and MALT1 could also possess such barriers that are not detectable by this method. This wouldn't detract from the finding that BCL10 has a barrier that plays an important function.

The reviewer is correct that DAmFRET would not be able to detect a nucleation barrier if the assembled phase does not condense the fluorophore to a sufficiently high density for FRET to occur. In our experience, this is only a concern for very large proteins whose bulk “dilutes” the fluorophores within the assembly. Death domains, on the other hand, are only ~ 3 nm in diameter, and FRET occurs within a range of ~10 nm; hence we think it very unlikely that the death domains could be forming cryptic polymers that escape our detection. In any case, when assembly does produce a change in FRET, we can with confidence determine how strongly that form of assembly is governed by concentration. Hence, for CARD9, which does produce a FRET signal upon assembly, we can say that assembly has a smaller intrinsic nucleation barrier than that of BCL10. We further eliminated the possibility of multi-step nucleation (which would reduce the apparent nucleation barrier relative to the one-step ideal case) for CARD9 by showing that artificial condensates of the protein expressed in trans do not influence the concentration-dependence of FRET (Fig. 4 B). Finally, under all conditions where CARD9 lacked FRET, it also lacked signaling activity, suggesting there is not a cryptic functional assembly that evades our assay. Likewise MALT1, which lacked FRET at all concentrations, was entirely unable to activate NF-kB upon overexpression (Fig. S8 A and B), suggesting that it too is not forming a cryptic functional assembly that evades our assay. We therefore feel confident in our conclusion that CARD9 and MALT1 lack nucleation barriers of a magnitude comparable to that of BCL10. Note that our claim is not that they entirely lack a nucleation barrier (CARD9 after all does form a multi-dimensionally ordered polymer), but rather that we fail to observe a nucleation barrier and hence any barrier that may exist is insufficient to manifest at the cellular level.

In the final results section, the idea that MALT1 activation doesn't depend on BCL10 polymer structure doesn't necessarily follow from the data. An alternative interpretation is that optogenetic clustering of MALT1 causes it to recruit BCL10 and form BCL10-MALT1 filaments (structure solved by Schlauderer et al., 2018). Also, the optogenetic clustering of MALT1 may mimic some structure found in the BCL10 cluster. Therefore, we are neither convinced that the data unambiguously show that MALT1 activation strictly depends on multi-valency rather than an ordered structure of BCL10 polymers nor that this conclusion is truly necessary for the paper.

We agree that the reviewer’s alternative interpretation of this experiment is possible. However, we consider it unlikely because we performed the experiment with MALT1 lacking its Death Domain (residues 126-824), which mediates its interaction with BCL10 (Schlauderer et al., 2018). Our experiments then suggest that MALT1 clustering is sufficient for activation independent of any structuring mediated by BCL10. Nevertheless, we have now performed an additional control in which we treated these cells with PMA to induce BCL10 polymerization. As expected, the NF-kB transcriptional reporter utterly failed to activate in this condition, indicating that MALT1 does not interact with BCL10 polymers when it lacks its death domain. This aspect has been further elaborated in our response to reviewer 3 point 5.

What optical density do the yeast cells reach during the 16h induction in galactose? If they are in stationary phase, this could affect the assembly status of the proteins being expressed, as the cytoplasm becomes glassy when cells are starved, and this coincides with widespread protein aggregation/assembly (Joyner et al., 2016; Munder et al., 2016).

In our DAmFRET strategy, we first dilute an overnight culture and regrow the cells to log phase prior to resuspending them in galactose media. Our strain is engineered to undergo cell cycle arrest upon protein induction, hence exponential growth is prevented and the cells do not deplete galactose during the 16 hr induction. We have also performed many time courses of DAmFRET following induction and generally find no qualitative difference between early and late times (unpublished). Early time points simply have lower expression and correspondingly fewer cells in the high FRET state. Importantly, all comparisons between proteins are made with the same 16 hr induction.

Although these experiments show that thermodynamically lowering the BCL10 nucleation barrier (e.g. by post-translational modifications or protein expression levels) isn't required for a response, they don't rule it out. It would be good to state this in the discussion, as cells may have multiple mechanisms of switching on the signalosome.

We thank the reviewer for this suggestion and have now explicitly stated in the discussion that our experiments do not argue against possible thermodynamic tuning of the nucleation barrier.

The discussion compares signalosomes with condensates formed by liquid-liquid phase separation. This is an interesting comparison but it suggests that disordered assemblies would not be capable of performing signalosome-like functions. This needs to be explained more clearly. For example, non-amyloid prions seem to form gel-like assemblies with a high nucleation barrier that are capable of driving heritable traits, likely through self-templating (Chakravarty et al., 2020). Such examples could represent disordered assemblies with signalosome switch-like behaviour. Furthermore, there are examples of condensates that are induced by environmental changes e.g. Pab1 and Ded1 condensates (Riback et al., 2017; Iserman et al., 2020). This potentially allows the proteins to reach high concentrations and remain un-condensed until a change in heat or pH overcomes a nucleation barrier required for condensate formation. Although the condensates aren't self-templating, they seem to require energy for their disassembly. Combined, this also allows switch-like behaviour, where the switch is flipped back to the uncondensed off state once conditions return to normal. In general, crossing a phase boundary can represent a switch-like response. Finally, recent electron-tomography experiments show that ASC puncta comprise clusters of filaments (Liu et al., 2021, biorxiv). CARD9/BCL10 assemblies may have similar ultrastructures and liquid-liquid phase separation may well play a role in their assembly.

Indeed, we explicitly maintain that liquid phases cannot themselves perform signalosome-like functions. Chakravarty et al. 2020 did not observe amyloids associated with their phenomena, but the relevant experiments were not designed to exhaustively exclude an underlying ordered phase. To the extent that gelation is involved, their observations are fully consistent with ours. IUPAC defines a “gel” as a colloidal network involving a solid phase and a dispersed phase. The existence of a solid phase necessarily implies an underlying disorder-to-order transition, even if limited to small length scales. In the case of gelation associated with liquid-liquid phase separation, nucleation of the ordered phase simply occurs in two steps (first condensation, then ordering). Note also that a liquid phase could in principle give rise to a heritable phenotype if it activates a positive feedback in a molecular biological process involving the protein of interest (e.g. upregulation of its expression or a change in interacting factors). Chakravarty et al. did not exclude such phenomena (it would be very difficult to do so); hence it cannot be concluded that phase separation is responsible for the sustained phenotypic changes.

We do not fully follow the reviewer’s logic concerning the relevance of Pab1 and Ded1 condensates. These proteins only condense when their respective phase boundaries fall below the endogenous protein concentration, as upon thermal stress. The proteins are not supersaturated in the absence of such conditions (for example, they cannot be seeded), and it is incorrect to characterize the change in heat or pH as overcoming a pre-existing nucleation barrier. The concept of a nucleation barrier only applies under conditions where a phase is thermodynamically favored. It is also misleading to state that the Ded1 and Pab1 condensates require energy for disassembly. Rather, they require energy to disassemble rapidly. Unless the assemblies have accessed a more ordered phase as described above (two step nucleation), involving a lower phase boundary, they will inevitably dissolve after the conditions return to normal.

We have much prior experience with ASC. Although it has not been explicitly shown, that it forms ordered polymers and can behave as a prionoid in vivo suggests that it very likely operates the same way as BCL10 (i.e. is physiologically supersaturated). That full-length ASC forms clusters of filaments is not relevant (in our view) to the mechanism shown here, which only requires that filaments are indeed formed. Formally, the size of the relevant nucleus determines the minimum length scale at which ordering must manifest in our mechanism. Based on the structure of death domain filaments, this could be as small as tetramers or hexamers (a minimal but structurally complete “polymer”).

As stated above, and now elaborated in the discussion, our data do not exclude a role of thermodynamic regulation, as could lead to liquid-liquid phase separation, in tuning the nucleation barrier of Bcl10. What they do exclude is that such changes are required for Bcl10 to activate in the first place.

Can the authors comment on the loss of BCL10 in Echinodermata, Anthropoda, Nematoda? Is there another protein that plays a similar role? Could a CARD or PCASP protein possess self-templating properties? Could other methods of control be at play e.g. protein expression?

This is a very interesting question! We think the reviewer’s suggested explanations for the loss of BCL10 in those lineages are valid and worthy of future exploration. Nematodes such as C. elegans have lost multiple components of innate immunity. They have very few pathogen recognition receptors and also lack NF-kB! They do, however, have other adaptor proteins that the literature and our unpublished data suggest may have self-templating ability, such as TIR-1. Drosophila also encodes multiple TIR-containing proteins that are essential for innate immunity. In short, it is possible that other proteins have acquired the hypothetically essential role of supersaturation and nucleation-limited signaling in these organisms.

Figures 1B/1C: Can the authors comment on why the active cells plateau at about 70-75%? This is a striking feature of the plots, but the explanation may not be obvious to readers.

See our response to major point 3, above.

Figures 1D/1E: What was the concentration of B-glucan used in this experiment? This could be included in the figure legend. If greater than 1ug/ml this means that the % of active cells in Figure 1B matches the % of cells with BCL10 assemblies in Figures 1D/1E, which is potentially an important point.

We thank the reviewer for bringing this point to our attention. We have now indicated in the figure legend the concentration of B-glucan used in this experiment (10 μg/ml). That the percentage of active cells in Fig. 1B matches that of cells containing BCL10 polymers in Fig. 1D and E indeed strengthens the stated relationship between BCL10 assembly and NF-kB activation in THP-1 cells subjected to a relatively physiological stimulus. Additionally, we have performed experiments to measure the levels of p65 translocation in THP-1 cells treated with B-glucan that express BCL10-mEos3.2. This data is shown in Figs. S1D and E in response to reviewer 3.

Use of both 'BCL10' and 'Bcl10' when referring to the protein.

We have now replaced all instances where Bcl10 was used to follow guidelines for gene and protein name conventions.

Bruford EA, Braschi B, Denny P, Jones TEM, Seal RL, Tweedie S. Guidelines for human gene nomenclature. Nat Genet. 2020;52(8):754-758. doi:10.1038/s41588-020-0669-3

In the supplementary figures there are some formatting problems/missing words in the figure legends. In Figure S11 there is a black box covering the lower part of the figure.

We have now fixed these instances.

References used in this review

Chakravarty, A.K. et al. (2020) "A Non-amyloid Prion Particle that Activates a Heritable Gene Expression Program," Molecular Cell, 77(2), pp. 251-265.e9. doi:10.1016/j.molcel.2019.10.028.

Iserman, C. et al. (2020) "Condensation of Ded1p Promotes a Translational Switch from Housekeeping to Stress Protein Production," Cell, 181, pp. 818-831.e19. doi:10.1016/j.cell.2020.04.009.

Joyner, R.P. et al. (2016) "A glucose-starvation response regulates the diffusion of macromolecules," eLife, 5. doi:10.7554/eLife.09376.

Munder, M.C. et al. (2016) "A pH-driven transition of the cytoplasm from a fluid- to a solid-like state promotes entry into dormancy," eLife, 5(MARCH2016). doi:10.7554/ELIFE.09347.

Riback, J.A. et al. (2017) "Stress-Triggered Phase Separation Is an Adaptive, Evolutionarily Tuned Response," Cell, 168(6), pp. 1028-1040.e19. doi:10.1016/j.cell.2017.02.027.

Schlauderer, F. et al. (2018) "Molecular architecture and regulation of BCL10-MALT1 filaments," Nature Communications 2018 9:1, 9(1), pp. 1-12. doi:10.1038/s41467-018-06573-8.

Reviewer #2 (Significance (Required)):

The existence of a nucleation barrier had already been postulated, based on structural and other studies (referenced by the authors), it had lacked a rigorous demonstration. This work provides that demonstration, which is important for the signalosome field and more broadly applicable to researchers studying cellular decision making. The study further demonstrates that DaMFRET is an excellent to study protein assembly processes in their native environment, allowing the authors to tackle a question that would have been technically very difficult to address otherwise.

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

The study by Rodriguez Gama et al. addresses the molecular function of CBM complex-forming proteins CARD9, BCL10 and MALT1 in the activation of myeloid cells, using optogenetic tools, transcriptional reporters and biochemical approaches. It is known from previous studies that Bcl10 oligomerizes into filamentous oligomeric structures incorporating Malt1, and that these structures are nucleated by receptor-induced activation of CARD proteins such as CARD11 (in lymphocytes) or CARD9 (in myeloid cells), but the mechanism underlying the assembly of the resulting CBM complexes remain incompletely understood.

The authors develop beautiful optogenetic tools to address this question, and convincingly demonstrate that CARD9-mediated nucleation of BCL10 triggers a binary cellular NF-kB response in a spring-load-like fashion, and identify mutants of BCL10 and CARD9 that impact this capacity. Unfortunately, however, the authors do not do a good job to simplify this complex problem so it can be easily understood. In particular, the choices of mutants, models and experiments are not consistent between figures, and some data seem to be arbitrarily added or omitted. Complex hybrid constructs are also used, without assessing whether these are indeed functional in the corresponding ko cells. The paper would therefore benefit from a major overhaul. We also noticed that the literature is often not cited adequately and have included a (non-exhaustive) list of examples of wrong, incomplete, or erroneous citations below.

1. The initial observations of binary signaling are derived from a reporter system. Although there are controls to show that the reporter used does not function intrinsically cooperatively, it would be nice to see additional data to show that cooperativity occurs also at the level of endogenous response systems, for instance by qPCR-based assessment of a natural NF-kB target gene (induced for example by TNFa versus B-glucan in THP-1 cells, and by TNFa versus PMA in 293T cells).

As detailed in the introduction, NF-kB has been shown by multiple labs to activate in a binary fashion. Our manuscript shows that NF-kB activation occurs in a binary fashion both at the level of transcription and at the level of nuclear translocation (upstream of any transcriptional output). While we do agree that additional data could further illustrate the biological significance of our findings, we do not feel it is necessary for our conclusions. Note also that because NF-kB activation occurs in a binary fashion per cell, a simple qPCR experiment would not suffice to extend our findings to the broader Nf-kB regulon. Instead, one would have to use e.g. RNA-FISH or single cell RNA-seq, nontrivial experiments that would take months to complete.

The cell lines in Figures 1D-E (and also some of the BCL10 mutants used later on) would have been better run in the assays in the early parts of Figure 1. The final conclusion prior to the section The adaptor protein BCL10 is a nucleation-mediated switch is otherwise not justified. This is a central tenet of the paper, that is referred to again, with some other ancillary data to support it. These mutants reappear later in the paper, but it would have been better, and easier to make rescue lines of BCL10 KO in Figure 1, otherwise the logic is lost, and the models seem chosen arbitrarily.

The choice of experiments in different panels of Fig. 1 resulted from a chronological progression of reagent construction as the project evolved. We do appreciate that switching between the assays may lead readers to doubt one or the other. Therefore, we have now immunostained for endogenous p65 in the same experiment as for Fig. 1D and confirmed that p65 translocated to the nucleus only in THP-1 BCL10-KO cells that have been reconstituted with WT BCL10-mEos3.2, but not E53R. We think this additional evidence along with our orthogonal measurements in other reporter systems confirms our findings that BCL10 nucleation determines NF-kB activity.

Expression with microNS is not well controlled and gives little real evidence for what is occurring. It is unclear what the concentration of the protein expressed was, but certainly the relative expression of the CARD9(CARD) and the microNS version should be assessed.

We believe these concerns result from a misunderstanding. We assume the reviewer is referring to the experiment in Fig. 3B. Expression of muNS on its own has no effect on the DAmFRET of other proteins, and we have previously used it in exactly the same way as here (Holliday M et al. 2019 and Kandola T et al. 2021). Please note that muNS fusion proteins in our experiment have an orthogonal fluorescent protein whose spectra do not significantly overlap with those of mEos3.1. The experiment evaluates a protein’s ability, when condensed via its fusion to muNS, to nucleate an mEos3.1-fused protein that is expressed in trans. Fusion of proteins to muNS does not affect their expression levels, as we now show for CARD9CARD-muNS-mCardinal versus CARD9CARD-mCardinal (Fig. S6D).

Also, the AmFRET profile of CARD9CARD looks very weird, it cannot be compared to BCL10.

We are unsure in what way the AmFRET profile of CARD9CARD is “weird”. It is fully consistent with expectations and has been thoroughly explained in the text. We suspect the reviewer was bothered by the sharp acquisition of FRET at approximately 100 uM. As explained in the text, this represents the phase boundary, also known as the solubility line, for CARD9CARD polymers, which we previously showed in vitro (Holliday M et al. 2019). Above this concentration, the protein self-assembles without a nucleation barrier, hence the sharp but continuous change in FRET. BCL10 plots, in contrast, show a discontinuous acquisition of FRET, which indicates a nucleation barrier. In order to highlight that the CARD9CARD transition is understood and expected, we have also now added a line to the plot to demarcate the phase boundary.

We are not convinced of the usefulness of the introduction of a slew of disease-causing CARD9 mutations that may or may not be relevant to the authors' point. The fact that they do or do not function in a specific sub portion of an assay that may or may not be relevant to biological activity seems to be of interest but without biochemical understanding, little is clear.

While several reports have shown the clinical importance of these CARD9 mutations on susceptibility to fungal infections, little was known about the molecular mechanism underlying their effects. The inclusion of the disease-causing mutants to this paper is justified for the following reasons. First, they demonstrate the relevance of our work to disease. Second, they build off our findings to provide an otherwise unknown molecular mechanism of these mutants. We showed using independent methods that CARD9CARD mutations disrupt the ability to nucleate BCL10, via two different mechanisms. Finally, validating the disease-causing mutations allowed us to use them as controls for subsequent experiments demonstrating that BCL10 is supersaturated.

The Optogenetic experiments are interesting, but difficult to interpret without evidence that these MALT1 constructs are indeed still functional when expressed in MALT1-deficient THP-1 cells. We do not therefore think that this experiment shows a necessity for clustering to signal, just a sufficiency, and in a highly artificial construct.

We welcome the opportunity to elaborate on the optogenetic experiments. Since BCL10 and MALT1 are expressed ubiquitously across cell types, the validity of our findings should not depend on the cell type used. Indeed, much of what we already know about innate immunity signalosomes comes from work in HEK293T cells. Our optogenetic experiments using MALT1 were performed in 293T MALT1-KO cells in Figures 6E and F, and employed two distinct functional assays (p65 nuclear translocation and a transcriptional reporter). While our approach employs light to control clustering, similar approaches using (no less-artificial) chemically induced dimerization domains have been used to study caspase activation (Oberst A et al, 2010, Boucher D et al, 2018). Our use of light affords higher specificity, reversibility, and spatial and temporal control over MALT1 assembly than does chemically induced dimerization.

To demonstrate the necessity of clustering, we have now performed an experiment with MALT1(126-824)-miRFP670-Cry2 expressed in 293T MALT1 KO cells that contain a transcriptional reporter of NF-kB ,as in figures 6E and F. We added PMA to the cells and found that it failed to activate NF-kB (Fig. 6), confirming that the interaction of MALT1 (via its death domain) with polymerized BCL10 is required for activation. Note that MALT1 and BCL10 exist as a soluble heterodimer prior to BCL10 polymerization; hence it is polymerization, rather than the interaction itself, that activates MALT1. That artificial clustering rescues this defect strongly suggests that the effect of polymerization can be attributed to increased proximity rather than some allosteric effect communicated from BCL10 polymers through the MALT1 DD to its caspase-like domain.

Oberst, A., Pop, C., Tremblay, A.G., Blais, V., Denault, J.-B., Salvesen, G.S., and Green, D.R. (2010). Inducible dimerization and inducible cleavage reveal a requirement for both processes in caspase-8 activation. J. Biol. Chem. 285, 16632–16642.

Boucher, D., Monteleone, M., Coll, R.C., Chen, K.W., Ross, C.M., Teo, J.L., Gomez, G.A., Holley, C.L., Bierschenk, D., Stacey, K.J., et al. (2018). Caspase-1 self-cleavage is an intrinsic mechanism to terminate inflammasome activity. J. Exp. Med. 215, 827–840.

In the introduction and other parts of the paper, there are numerous instances where the previous literature in the field is not adequately cited. Examples include:

• In the introduction, it is weird to cite one original paper (a MALT1 ko study by Ruland et al., 2001; there are several other studies of ko papers for CBM components that would merit being citated along with this study) together with two reviews on that topic (Ruland and Hartjes 2019 and Gehring et al. 2018)

• In the introduction, the original study by Wang et al., 2002 should be cited together with Rebeaud et al., 2002; the two studies on the same topic were published back-to-back

• In the introduction, the statement "CARD10 and CARD14 are expressed in nonhematopoietic cells including intestinal and skin epithelia, respectively" should be supported by citations.

• Still in the introduction, the 2 references for the statement "... CARD14 gain of function mutations cause psoriasis (Howes et al., 2016; Jordan et al., 2012)" are not appropriate. There are several reports of patients with CARD14 mutations (the study by Jordan et al is only one of them) and several CARD14 mouse models that provoke a psoriasis-like phenotype, which would merit being cited.

• In the following sentence: "Point mutations and translocations involving BCL10 and MALT1 cause immunodeficiencies (Ruland and Hartjes, 2019), testicular cancer (Kuper-Hommel et al., 2013), and lymphomas (Zhang et al., 1999).", the citation style also seems completely random, combining the citation of a single original paper for lymphomas (Zhang et al. 1999) (there are several other important original studies on that topic or recent reviews that could be cited instead), together with a review on immunodeficiencies (Ruland and Hartjes, 2019) and then another single example for a role of BCL10 and MALT1 in carcinoma (the study by Kuper-Hommel et al. is one, but several other original publications exist on the latter topic, showing for example a role in breast carcinoma or glioblastoma).

• In the first section of the results, the reference cited for endogenous CARD10 expression in 293T cells (Ruland et al., 2001) is wrong, no endogenous CARD10 expression was assessed in that study

We have now revised the citations mentioned above and other instances to ensure adequate citations in each case.

Reviewer #3 (Significance (Required)):

The paper deals with a complex question, namely how the CBM signalosome assembles and functions to stimulate NF-kB signaling. This question is important to the understanding of pro-inflammatory immune responses and basic life sciences in general. As the focal point of the paper is complex, and tools to study such phenomena are at the limit of technical capabilities, this further increases the potential impact of the work.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

The characterization of open-ended signalosomes in a number of innate-immunity and cell-death pathways, in particular formed by domains from the death-fold family, has led to the suggestions that these complexes allow a switch-like signalling response suitable for these pathways. It appears that this has been widely accepted. However, these suggestions are based largely on indirect observations and speculation.

Rodriguez-Gama and coworkers have decided to test these suggestions more directly. Their results confirm the suggestions. Based on my own experience, papers that validate widely adopted suggestions are often not considered seriously by top journals, who are looking for hot topics/paradigm-changing/surprising type results. I would urge the editors to consider seriously work such as in this paper, which directly tests important suggestions and does so at a technically high standard. The authors use a range of ingenious approaches, both with recombinant proteins and in cells, and including proteins from organisms from different parts of the evolutionary tree, to support their interpretations, so it is an extensive and high-quality study. I am impressed that so many different fusion proteins with fluorescent tags continued to function as expected, but I guess the authors controlled for this as much as they could.

Having said all this, I do get the feeling the authors are "over-selling" the nucleation barrier aspect of these signalling mechanisms. It is clearly an important and critical aspect of signalling in many systems, but then it is not the only important aspect; a number of other regulatory inputs play a role in different systems. So the statement "Our findings introduce a novel structure-function paradigm" in my view is overstretching things somewhat. Further in the Discussion section, the authors state "Existing explanations for the preponderance of ordered polymers in immune cell signalosomes have centered on the functions of multivalency at steady state, such as scaffolding and sensitivity enhancement resulting from the cooperativity of homo-oligomerization". They cite a small (and non-exhaustive) number of papers discussing this topic; all these include "seeding" or "nucleation" as an important part of the proposed mechanism. So I suggest the authors provide a more balanced discussion of this aspect. Different pathways appear to display a different level of switch-like behaviour, and one thing that the current version of the manuscript is missing is more discussion of other death fold-based systems and how the results on the CBM signalosome apply to these, and also other systems such as TIR domain-based ones, which currently get no mention whatsoever. In the CBM system, there seems to be one main nucleation barrier; can there be more than one in others?

We appreciate the reviewer’s perspective and have now acknowledged in the introduction and discussion additional prior literature that has paved the way for our study. Nevertheless, we maintain -- as now stated in the abstract -- that “our results defy the usual protein structure/function paradigm, and demonstrate that protein structure can evolve via selection for energetic maxima in addition to minima”. We have elaborated in the introduction and discussion how immune signaling provides the functional context in which such a paradigm can evolve, and how our findings uniquely support the paradigm.

One other aspect I need to express some criticism about is attention to detail - especially with a paper focusing on the physics behind biological processes, I would expect a higher standard of getting the terminology and units correct - see specific examples below. This can obviously be fixed easily.

Specific points are listed below. No page or line numbers are provided so I have done my best to make it clear what the comments refer to.

1. Abstract line 6 and throughout: in "NF-kB", the "k" is supposed to be "kappa" (Greek letter) - it stands for "nuclear factor kappa-light-chain-enhancer of activated B cells", not fully defined in the manuscript as far as I can see. Occasionally, small k is also used instead of the small cap K or whatever the authors used most of the time, but I don't think any of them use the Greek letter.

We had indeed used a version of the small “kappa” κ. We have now fixed the cases where we mistakenly used k instead of κ.

Page 2 (Introduction) paragraph 2 line 9: period missing at the end of sentence. Same Page 4 (Results: Assembly) paragraph 4 line 3.

This is now fixed.

Page 2 (Introduction) paragraph 2 line 15 and throughout: in long sentences, more commas can help help readability, for example before "leading" here. Similar page 15 paragraph 2 line 3 after "Additionally", paragraph 4 line 2 before "which".

We have now included more commas and tried to improve readability throughout.

Page 4 (Results: Assembly) paragraph 2 line 2: is "positive feedback" different from "cooperativity"? Is it a broader term that includes cooperativity, nucleation and other mechanisms? It may be useful to introduce some of these terms to avoid confusion by the readers.

“Positive feedback” is the broadest term as it is agnostic to mechanism. “Nucleation” refers to the initiation of a first order phase transition, which is one mechanism of positive feedback. Nucleation involves “cooperativity”, in that a higher order species is more stable than smaller species. However, cooperativity can occur for oligomers of finite size, whereas nucleation is reserved for phase transitions to species of infinite size. We appreciate that the use of so many related terms may have created more confusion than necessary. Hence, we have now revised the text to omit the more general terms -- “positive feedback” and “cooperativity” where possible.

Page 4 (Results: Assembly) paragraph 2 line 3: please define "TNF".

We have now fixed this and other acronyms.

Page 4 (Results: Assembly) paragraph 3 line 2: the use of size-exclusion chromatography to follow the size of complexes would assume that they are irreversible or very stable. It appears this may be the case here, but some discussion may be warranted.

We have now explained that SEC is appropriate for this experiment because large nucleation barriers generally imply stable assemblies.

Page 4 (Results: Assembly) paragraph 3 line 4 and throughout: the symbol for "kilodalton" is "kDa".

We have now fixed this mistake.

Page 4 (Results: Assembly) paragraph 3: I am not sure how the results discussed in this paragraph demonstrate that assembly occurs in cooperative fashion - just that there is a change in oligomeric states upon stimulation.

Cooperativity is implied by the absence of oligomer sizes between monomer and the large assembly. Nevertheless, we realized this can only be concluded in the case of homotypic assembly, which we cannot yet assume at this point in the paper. Therefore, we have revised this paragraph to say that the distribution is “consistent with” an underlying phase transition (which we then go on to prove).

Page 4 (Results: Assembly) paragraph 4 line 2: "WT" is not defined. Wild-type what? I presume "protein"?

We refer here to the wild-type protein. We have now fixed this mistake.

Page 4 (Results: Assembly) paragraph 4: it may be worth pointing out here the wild-type and mutant proteins expressed at similar levels; clearly the outcomes will depend on protein concentration in the cell. I believe the supplementary figure shows this to a large extent.

Indeed, our supplementary figure shows that the WT and mutant protein express to comparable levels. We have now pointed this out in the text.

Page 4 (Results: The adaptor) paragraph 1 line 4: "CARD domain" would stand for "caspase activation and recruitment domain domain". Please check throughout (including Supplementary Material).

We have fixed this mistake.

Page 4 (Results: The adaptor) paragraph 1 line 9: "expressed over a range of concentrations in cells" - this would imply the authors controlled expression - please rephrase to explain what exactly was done.

We have now rephrased this sentence to indicate that the range of expression results from the use of a genetic construct with cell-to-cell variation in copy number.

Page 5 (Results: The adaptor) paragraph 2 line 3 and throughout (including Supplementary Material): please use the Greek letter rather that "u" for micro.

We have now fixed this mistake.

Page 5 (Results: The adaptor) paragraph 3: this analysis is rather simplistic, it is not just the RMSD value, it is the nature of conformational change that is important? Please elaborate, I would think the papers presenting structural work have already discussed this to some extent?

The reviewer is correct; it is the nature of the conformational change that is most important. We are unsure how to accurately estimate the energy barrier separating the two conformations for each protein. However, we have now undertaken a collaboration to attempt to do so via FAST molecular simulations (Zimmerman and Bowman 2015). In lieu of the results of these ongoing studies, we have modified the text to acknowledge that RMSD does not necessarily relate to nucleation barriers.

Maxwell I. Zimmerman and Gregory R. Bowman. Journal of Chemical Theory and Computation, 2015, 11 (12), 5747-5757 DOI: 10.1021/acs.jctc.5b00737

Page 5 (Results: The adaptor) paragraph 4 line 5 and further in this section: some symbol(s) do not show in the pdf - before "(delta)", next page line 3-5 after "higher" and "both".

We have fixed this issue that resulted from exporting to a PDF file from our text editor.

Page 6 (Results: The adaptor) paragraph 4: interface IIa and IIIb are not introduced, and there is not even any reference provided here.

We have now added a reference for these mutations and elaborated on the interfaces IIa and IIIb.

Page 6 (Results: Pathogenic) paragraph 1 line 12: "FL" is not introduced.

We have now fixed this mistake.

Page 8 (Results: Pathogenic) paragraph 7: the text "absent the pathogenic mutations" is missing something.

We have now reworded this section.

Page 10 (Results: BCL10) paragraph 3: why does CARD9 CARD clustering peak and then disassemble (I guess "clustering" doesn't disassemble, please rewrite as well).

We have now fixed this mistake.

Page 11 (Results: MALT1) paragraph 1: I presume dimerization doesn't achieve the same level of proximity as higher-order multimerization?

Our interpretation here is that for MALT1, activation requires close proximity of more than two molecules. Although our dimerization module did not activate the caspase-like domain of MALT1, we know that it achieves close enough proximity to activate the caspase domain of CASP8. Hence we believe the MALT1 mechanism has a stoichiometry requirement in addition to a proximity requirement. This is, of course, consistent with the fact that activation normally occurs in the context of polymers rather than dimers.

Page 11 (Results: Ancient) paragraph 1 line 4: is this AlphaFold2?

That is correct, we used AlphaFold2. We have added that detail.

Page 12 (Discussion) paragraph 4: not sure if "molecular examples of evolutionary spandrels" will be clear to most readers.

We have now explained what evolutionary spandrels are, and elaborated on the relationship to our findings.

Page 14 (Materials: Plasmid) line 2 and throughout: "Golden Gate" is usually capitalized. Similar for "Gibson" further in the paragraph. The English in this paragraph is not up to standard in general; for example "Then placing..." is not a complete sentence, and a number of sentences ending with "via gibson" need to be rewritten.

We have now rewritten this paragraph.

Page 16 (Materials: Cell) line 4 and throughout: "2" in "CO2" should be subscripted.

This is now fixed.

Page 16 (Materials: Transient) line 6 and throughout (including Supplementary Material): please use a space between number and unit ("35 mm").

This is now fixed.

Page 16 (Materials: Generation) line 4 and throughout: to distinguish from "gram", please italicize "g" and/or use "x g".

We have now fixed this.

Page 17 (Materials: Yeast) line 3: please specify which table is "table X".

We have now fixed this mistake.

Page 17 (Materials: Mammalian) line 1: please provide full reference. Same next paragraph line 2.

We have now fixed this.

Page 17 (Materials: DAmFRET) line 3: "SSC" and "FSC" are not defined.

We have now fixed this.

Page 18 (Materials: Fluorescence) line 10: "Coefficient" does not have to be capitalized. It does not have to be defined again in the next paragraph.

We have now fixed this.

Page 19 (Materials: Optogenetic) line 1: "performed" rather than "made"?

We have now fixed this.

Page 19 (Materials: Protein) line 12: the Compass software doesn't have a reference?

We have now added the reference to the software.

References: please make format consistent: articles titles in sentence or title case.

We have now formatted all references to be consistent.

Legend to Fig. 1: I suggest "Schematic diagram"; and "h" rather than "hrs"; please check throughout (including Supplementary Material).

We agree with this suggestion.

Legend to Fig. S1: is "TNF-a" supposed to be "TNF-alpha"?

We have fixed this.

Legend to Fig. S7: please capitalize "Figure 2H".

We have fixed this.

Legend to Fig. S10F: please move "Dox" behind the concentration.

We have fixed this.

Fig. S14B: the colours in the superposition make it difficult to see the differences.

We have used a different color now.

Legend to Fig. S14: I suggest "structure...predicted by AlphaFold" (2?) and include the reference.

We agree with this suggestion.

Reviewer #4 (Significance (Required)):

As argued above, the significance of this paper is that it tests directly important hypotheses proposed or assumed previously, and does so at a technically high standard. No published report has done so to a similar extent.

The paper should be of interest to a broad audience from cell biologists and immunologists to biochemists, biophysicists and structural biologists.

My expertise is in structural biology or systems similar to the one studied here.

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

The characterization of open-ended signalosomes in a number of innate-immunity and cell-death pathways, in particular formed by domains from the death-fold family, has led to the suggestions that these complexes allow a switch-like signalling response suitable for these pathways. It appears that this has been widely accepted. However, these suggestions are based largely on indirect observations and speculation.

Rodriguez-Gama and coworkers have decided to test these suggestions more directly. Their results confirm the suggestions. Based on my own experience, papers that validate widely adopted suggestions are often not considered seriously by top journals, who are looking for hot topics/paradigm-changing/surprising type results. I would urge the editors to consider seriously work such as in this paper, which directly tests important suggestions and does so at a technically high standard. The authors use a range of ingenious approaches, both with recombinant proteins and in cells, and including proteins from organisms from different parts of the evolutionary tree, to support their interpretations, so it is an extensive and high-quality study. I am impressed that so many different fusion proteins with fluorescent tags continued to function as expected, but I guess the authors controlled for this as much as they could.

Having said all this, I do get the feeling the authors are "over-selling" the nucleation barrier aspect of these signalling mechanisms. It is clearly an important and critical aspect of signalling in many systems, but then it is not the only important aspect; a number of other regulatory inputs play a role in different systems. So the statement "Our findings introduce a novel structure-function paradigm" in my view is overstretching things somewhat. Further in the Discussion section, the authors state "Existing explanations for the preponderance of ordered polymers in immune cell signalosomes have centered on the functions of multivalency at steady state, such as scaffolding and sensitivity enhancement resulting from the cooperativity of homo-oligomerization". They cite a small (and non-exhaustive) number of papers discussing this topic; all these include "seeding" or "nucleation" as an important part of the proposed mechanism. So I suggest the authors provide a more balanced discussion of this aspect. Different pathways appear to display a different level of switch-like behaviour, and one thing that the current version of the manuscript is missing is more discussion of other death fold-based systems and how the results on the CBM signalosome apply to these, and also other systems such as TIR domain-based ones, which currently get no mention whatsoever. In the CBM system, there seems to be one main nucleation barrier; can there be more than one in others?

One other aspect I need to express some criticism about is attention to detail - especially with a paper focusing on the physics behind biological processes, I would expect a higher standard of getting the terminology and units correct - see specific examples below. This can obviously be fixed easily.

Specific points are listed below. No page or line numbers are provided so I have done my best to make it clear what the comments refer to.

1. Abstract line 6 and throughout: in "NF-kB", the "k" is supposed to be "kappa" (Greek letter) - it stands for "nuclear factor kappa-light-chain-enhancer of activated B cells", not fully defined in the manuscript as far as I can see. Occasionally, small k is also used instead of the small cap K or whatever the authors used most of the time, but I don't think any of them use the Greek letter.
2. Page 2 (Introduction) paragraph 2 line 9: period missing at the end of sentence. Same Page 4 (Results: Assembly) paragraph 4 line 3.
3. Page 2 (Introduction) paragraph 2 line 15 and throughout: in long sentences, more commas can help help readability, for example before "leading" here. Similar page 15 paragraph 2 line 3 after "Additionally", paragraph 4 line 2 before "which".
4. Page 4 (Results: Assembly) paragraph 2 line 2: is "positive feedback" different from "cooperativity"? Is it a broader term that includes cooperativity, nucleation and other mechanisms? It may be useful to introduce some of these terms to avoid confusion by the readers.
5. Page 4 (Results: Assembly) paragraph 2 line 3: please define "TNF".
6. Page 4 (Results: Assembly) paragraph 3 line 2: the use of size-exclusion chromatography to follow the size of complexes would assume that they are irreversible or very stable. It appears this may be the case here, but some discussion may be warranted.
7. Page 4 (Results: Assembly) paragraph 3 line 4 and throughout: the symbol for "kilodalton" is "kDa".
8. Page 4 (Results: Assembly) paragraph 3: I am not sure how the results discussed in this paragraph demonstrate that assembly occurs in cooperative fashion - just that there is a change in oligomeric states upon stimulation.
9. Page 4 (Results: Assembly) paragraph 4 line 2: "WT" is not defined. Wild-type what? I presume "protein"?
10. Page 4 (Results: Assembly) paragraph 4: it may be worth pointing out here the wild-type and mutant proteins expressed at similar levels; clearly the outcomes will depend on protein concentration in the cell. I believe the supplementary figure shows this to a large extent.
11. Page 4 (Results: The adaptor) paragraph 1 line 4: "CARD domain" would stand for "caspase activation and recruitment domain domain". Please check throughout (including Supplementary Material).
12. Page 4 (Results: The adaptor) paragraph 1 line 9: "expressed over a range of concentrations in cells" - this would imply the authors controlled expression - please rephrase to explain what exactly was done.
13. Page 5 (Results: The adaptor) paragraph 2 line 3 and throughout (including Supplementary Material): please use the Greek letter rather that "u" for micro.
14. Page 5 (Results: The adaptor) paragraph 3: this analysis is rather simplistic, it is not just the RMSD value, it is the nature of conformational change that is important? Please elaborate, I would think the papers presenting structural work have already discussed this to some extent?
15. Page 5 (Results: The adaptor) paragraph 4 line 5 and further in this section: some symbol(s) do not show in the pdf - before "(delta)", next page line 3-5 after "higher" and "both".
16. Page 6 (Results: The adaptor) paragraph 4: interface IIa and IIIb are not introduced, and there is not even any reference provided here.
17. Page 6 (Results: Pathogenic) paragraph 1 line 12: "FL" is not introduced.
18. Page 8 (Results: Pathogenic) paragraph 7: the text "absent the pathogenic mutations" is missing something.
19. Page 10 (Results: BCL10) paragraph 3: why does CARD9 CARD clustering peak and then disassemble (I guess "clustering" doesn't disassemble, please rewrite as well).
20. Page 11 (Results: MALT1) paragraph 1: I presume dimerization doesn't achieve the same level of proximity as higher-order multimerization?
21. Page 11 (Results: Ancient) paragraph 1 line 4: is this AlphaFold2?
22. Page 12 (Discussion) paragraph 4: not sure if "molecular examples of evolutionary spandrels" will be clear to most readers.
23. Page 14 (Materials: Plasmid) line 2 and throughout: "Golden Gate" is usually capitalized. Similar for "Gibson" further in the paragraph. The English in this paragraph is not up to standard in general; for example "Then placing..." is not a complete sentence, and a number of sentences ending with "via gibson" need to be rewritten.
24. Page 16 (Materials: Cell) line 4 and throughout: "2" in "CO2" should be subscripted.
25. Page 16 (Materials: Transient) line 6 and throughout (including Supplementary Material): please use a space between number and unit ("35 mm").
26. Page 16 (Materials: Generation) line 4 and throughout: to distinguish from "gram", please italicize "g" and/or use "x g".
27. Page 17 (Materials: Yeast) line 3: please specify which table is "table X".
28. Page 17 (Materials: Mammalian) line 1: please provide full reference. Same next paragraph line 2.
29. Page 17 (Materials: DAmFRET) line 3: "SSC" and "FSC" are not defined.
30. Page 18 (Materials: Fluorescence) line 10: "Coefficient" does not have to be capitalized. It does not have to be defined again in the next paragraph.
31. Page 19 (Materials: Optogenetic) line 1: "performed" rather than "made"?
32. Page 19 (Materials: Protein) line 12: the Compass software doesn't have a reference?
33. References: please make format consistent: articles titles in sentence or title case.
34. Legend to Fig. 1: I suggest "Schematic diagram"; and "h" rather than "hrs"; please check throughout (including Supplementary Material).
35. Legend to Fig. S1: is "TNF-a" supposed to be "TNF-alpha"?
36. Legend to Fig. S7: please capitalize "Figure 2H".
37. Legend to Fig. S10F: please move "Dox" behind the concentration.
38. Fig. S14B: the colours in the superposition make it difficult to see the differences.
39. Legend to Fig. S14: I suggest "structure...predicted by AlphaFold" (2?) and include the reference.

Significance

As argued above, the significance of this paper is that it tests directly important hypotheses proposed or assumed previously, and does so at a technically high standard. No published report has done so to a similar extent.

The paper should be of interest to a broad audience from cell biologists and immunologists to biochemists, biophysicists and structural biologists.

My expertise is in structural biology or systems similar to the one studied here.

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

The study by Rodriguez Gama et al. addresses the molecular function of CBM complex-forming proteins CARD9, BCL10 and MALT1 in the activation of myeloid cells, using optogenetic tools, transcriptional reporters and biochemical approaches. It is known from previous studies that Bcl10 oligomerizes into filamentous oligomeric structures incorporating Malt1, and that these structures are nucleated by receptor-induced activation of CARD proteins such as CARD11 (in lymphocytes) or CARD9 (in myeloid cells), but the mechanism underlying the assembly of the resulting CBM complexes remain incompletely understood.

The authors develop beautiful optogenetic tools to address this question, and convincingly demonstrate that CARD9-mediated nucleation of BCL10 triggers a binary cellular NF-kB response in a spring-load-like fashion, and identify mutants of BCL10 and CARD9 that impact this capacity. Unfortunately, however, the authors do not do a good job to simplify this complex problem so it can be easily understood. In particular, the choices of mutants, models and experiments are not consistent between figures, and some data seem to be arbitrarily added or omitted. Complex hybrid constructs are also used, without assessing whether these are indeed functional in the corresponding ko cells. The paper would therefore benefit from a major overhaul. We also noticed that the literature is often not cited adequately and have included a (non-exhaustive) list of examples of wrong, incomplete, or erroneous citations below.

1) The initial observations of binary signaling are derived from a reporter system. Although there are controls to show that the reporter used does not function intrinsically cooperatively, it would be nice to see additional data to show that cooperativity occurs also at the level of endogenous response systems, for instance by qPCR-based assessment of a natural NF-kB target gene (induced for example by TNFa versus B-glucan in THP-1 cells, and by TNFa versus PMA in 293T cells).

2) The cell lines in Figures 1D-E (and also some of the BCL10 mutants used later on) would have been better run in the assays in the early parts of Figure 1. The final conclusion prior to the section The adaptor protein BCL10 is a nucleation-mediated switch is otherwise not justified. This is a central tenet of the paper, that is referred to again, with some other ancillary data to support it. These mutants reappear later in the paper, but it would have been better, and easier to make rescue lines of BCL10 KO in Figure 1, otherwise the logic is lost, and the models seem chosen arbitrarily.

3) Expression with microNS is not well controlled and gives little real evidence for what is occurring. It is unclear what the concentration of the protein expressed was, but certainly the relative expression of the CARD9(CARD) and the microNS version should be assessed. Also, the AmFRET profile of CARD9CARD looks very weird, it cannot be compared to BCL10.

4) We are not convinced of the usefulness of the introduction of a slew of disease-causing CARD9 mutations that may or may not be relevant to the authors' point. The fact that they do or do not function in a specific sub portion of an assay that may or may not be relevant to biological activity seems to be of interest but without biochemical understanding, little is clear.

5) The Optogenetic experiments are interesting, but difficult to interpret without evidence that these MALT1 constructs are indeed still functional when expressed in MALT1-deficient THP-1 cells. We do not therefore think that this experiment shows a necessity for clustering to signal, just a sufficiency, and in a highly artificial construct.

6) In the introduction and other parts of the paper, there are numerous instances where the previous literature in the field is not adequately cited. Examples include:

• In the introduction, it is weird to cite one original paper (a MALT1 ko study by Ruland et al., 2001; there are several other studies of ko papers for CBM components that would merit being citated along with this study) together with two reviews on that topic (Ruland and Hartjes 2019 and Gehring et al. 2018)
• In the introduction, the original study by Wang et al., 2002 should be cited together with Rebeaud et al., 2002; the two studies on the same topic were published back-to-back
• In the introduction, the statement "CARD10 and CARD14 are expressed in nonhematopoietic cells including intestinal and skin epithelia, respectively" should be supported by citations.
• Still in the introduction, the 2 references for the statement "... CARD14 gain of function mutations cause psoriasis (Howes et al., 2016; Jordan et al., 2012)" are not appropriate. There are several reports of patients with CARD14 mutations (the study by Jordan et al is only one of them) and several CARD14 mouse models that provoke a psoriasis-like phenotype, which would merit being cited.
• In the following sentence: "Point mutations and translocations involving BCL10 and MALT1 cause immunodeficiencies (Ruland and Hartjes, 2019), testicular cancer (Kuper-Hommel et al., 2013), and lymphomas (Zhang et al., 1999).", the citation style also seems completely random, combining the citation of a single original paper for lymphomas (Zhang et al. 1999) (there are several other important original studies on that topic or recent reviews that could be cited instead), together with a review on immunodeficiencies (Ruland and Hartjes, 2019) and then another single example for a role of BCL10 and MALT1 in carcinoma (the study by Kuper-Hommel et al. is one, but several other original publications exist on the latter topic, showing for example a role in breast carcinoma or glioblastoma).
• In the first section of the results, the reference cited for endogenous CARD10 expression in 293T cells (Ruland et al., 2001) is wrong, no endogenous CARD10 expression was assessed in that study

Significance

The paper deals with a complex question, namely how the CBM signalosome assembles and functions to stimulate NF-kB signaling. This question is important to the understanding of pro-inflammatory immune responses and basic life sciences in general. As the focal point of the paper is complex, and tools to study such phenomena are at the limit of technical capabilities, this further increases the potential impact of the work.

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 their manuscript entitled "A nucleation barrier springloads..." Rodriguez-Gama et al. dissect the assembly mechanism of the signalosome, composed of the proteins CARD9, BCL10 and MALT1, using a novel in-cell biophysical approach (DAmFRET). They first overexpressed fluorescently tagged versions of the proteins to promote their assembly in yeast and mammalian cells, finding that CARD9 forms higher order assemblies across a wide range of concentrations with no discontinuity in the DAmFRET profile. In contrast, the DAmFRET profile of BCL10 showed a clear separation between monomers and higher order assemblies, which started to form spontaneously only at higher BCL10 concentrations. Furthermore, at the two states of the proteins co-exist at all concentrations. These observations imply that there is a nucleation barrier to forming BCL10 assemblies. MALT1 showed no change in FRET regardless of its expression level. These observations, alongside fluorescence microscopy of the assemblies, and previous structural studies, suggest that BCL10 forms self-templating polymers that act as a switch for an all-or-nothing immune response, assayed in this case by monitoring the nuclear translocation of the NF-kB subunit p65. The authors also assessed the effects of known disease-causing mutations on the nucleation barrier, showing that changes in the strength of the nucleation barrier can have major effects on signalosome function. Finally, they used optogenetic methods to trigger assembly of individual signalosome components, providing insight into the minimal components/conditions required for signalosomes to work.

Major comments:

Overall, the experiments by Rodriguez-Gama et al. offer convincing evidence that there is a nucleation barrier to BCL10 polymerisation, and that a CARD9 template is sufficient to overcome the barrier. Although the existence of a nucleation barrier had already been postulated, based on structural and other studies (referenced by the authors), it had lacked a rigorous demonstration. This work provides that demonstration, which is important for the signalosome field and more broadly applicable to researchers studying cellular decision making. The study further demonstrates that DaMFRET is an excellent to study protein assembly processes in their native environment, allowing the authors to tackle a question that would have been technically very difficult to address otherwise. The optogenetic experiments are a nice sufficiency test for their ideas.

We feel there are a few key points to address before publication.

1) One of the main conclusions is that spring-loading the nucleation barrier with high super-saturating BCL10 concentrations allows a decisive response. Although much of the data strongly imply this conclusion, the dependence of the immune response on BCL10 concentration was not tested directly. A key prediction of the nucleation barrier is that at concentrations below saturation, BCL10 should not be able to induce an all-or-nothing response when stimulated. At saturated/super-saturated concentrations BCL10 should be able to induce a response. At deeply super-saturated concentrations the response should start to be activated spontaneously in the absence of an external stimulus. These predictions could be tested using the doxycycline-inducible BCL10 system (Figure S2D), without establishing major new experimental avenues. We feel that such an experiment would strengthen the main conclusion. It might also help to shed light on whether being highly supersaturated enables a more decisive response than being just saturated.

2) Intuitively, readers might expect that if BCL10 is supersaturated then, once nucleated, it would rapidly assemble at the nucleation sites. In Figure 5B, CARD9CARD-miRFP670nano-Cry2 assemblies are optically induced throughout the cell. However, BCL10 appears to nucleate at just a few sites with a few minutes delay. More widespread nucleation and growth of BCL10 polymers seems to take longer (20-40 minutes, Figures 5B and 5C), after CARD9CARD-miRFP670nano-Cry2 has disassembled. Furthermore, in Figures 4D and 4E, very few BCL10 assemblies are visible/quantifiable after 70 minutes PMA exposure, but p65 has clearly entered the nucleus. It looks like BCL10 assembly slightly lags behind p65 nuclear entry. Can the authors provide a more detailed explanation of these kinetics?

3) Related to point 2 above, in Figure 5D, the leftmost cell in the field of view clearly contains CARD9CARD assemblies but there are no BCL10 assemblies and p65 is not imported into the nucleus (in contrast to the central cell in the field of view). How often does CARD9CARD optogenetic assembly lead to BCL10 assembly? In other words, can the authors quantify the cell-to-cell variability in this experiment?

Minor comments:

While the work is scientifically well done, the text reads as though it is meant for experts rather than a broad audience. This is a pity because it risks alienating readers. We suggest that some adjustments to the text (mainly additional explanations and not ruling out alternative interpretations of the data) would widen the audience and increase the impact of this important study. Below are some suggestions that might help.

1) In the first results section, the authors write: 'This suggests that Bcl10 but not CARD9 assembly occurs in a highly cooperative fashion that could, in principle (Koch, 2020), underlie the feed forward mechanism.' It isn't obvious how Figure 1 leads to this statement. Could the authors give a more detailed explanation?

2) One limitation of DAmFRET is that it can only detect a nucleation barrier where there is a difference in FRET between the monomer and the assembled form of the protein. However, it can't necessarily detect when there is not a nucleation barrier i.e. if there's no difference in FRET. The text seems to suggest that CARD9 and MALT1 don't have nucleation barriers to their assembly. While this might not be intentional, it would be helpful to explicitly state that CARD9 and MALT1 could also possess such barriers that are not detectable by this method. This wouldn't detract from the finding that BCL10 has a barrier that plays an important function.

3) In the final results section, the idea that MALT1 activation doesn't depend on BCL10 polymer structure doesn't necessarily follow from the data. An alternative interpretation is that optogenetic clustering of MALT1 causes it to recruit BCL10 and form BCL10-MALT1 filaments (structure solved by Schlauderer et al., 2018). Also, the optogenetic clustering of MALT1 may mimic some structure found in the BCL10 cluster. Therefore, we are neither convinced that the data unambiguously show that MALT1 activation strictly depends on multi-valency rather than an ordered structure of BCL10 polymers nor that this conclusion is truly necessary for the paper.

4) What optical density do the yeast cells reach during the 16h induction in galactose? If they are in stationary phase, this could affect the assembly status of the proteins being expressed, as the cytoplasm becomes glassy when cells are starved, and this coincides with widespread protein aggregation/assembly (Joyner et al., 2016; Munder et al., 2016).

5) Although these experiments show that thermodynamically lowering the BCL10 nucleation barrier (e.g. by post-translational modifications or protein expression levels) isn't required for a response, they don't rule it out. It would be good to state this in the discussion, as cells may have multiple mechanisms of switching on the signalosome.

6) The discussion compares signalosomes with condensates formed by liquid-liquid phase separation. This is an interesting comparison but it suggests that disordered assemblies would not be capable of performing signalosome-like functions. This needs to be explained more clearly. For example, non-amyloid prions seem to form gel-like assemblies with a high nucleation barrier that are capable of driving heritable traits, likely through self-templating (Chakravarty et al., 2020). Such examples could represent disordered assemblies with signalosome switch-like behaviour. Furthermore, there are examples of condensates that are induced by environmental changes e.g. Pab1 and Ded1 condensates (Riback et al., 2017; Iserman et al., 2020). This potentially allows the proteins to reach high concentrations and remain un-condensed until a change in heat or pH overcomes a nucleation barrier required for condensate formation. Although the condensates aren't self-templating, they seem to require energy for their disassembly. Combined, this also allows switch-like behaviour, where the switch is flipped back to the uncondensed off state once conditions return to normal. In general, crossing a phase boundary can represent a switch-like response. Finally, recent electron-tomography experiments show that ASC puncta comprise clusters of filaments (Liu et al., 2021, biorxiv). CARD9/BCL10 assemblies may have similar ultrastructures and liquid-liquid phase separation may well play a role in their assembly.

7) Can the authors comment on the loss of BCL10 in Echinodermata, Anthropoda, Nematoda? Is there another protein that plays a similar role? Could a CARD or PCASP protein possess self-templating properties? Could other methods of control be at play e.g. protein expression?

8) Figures 1B/1C: Can the authors comment on why the active cells plateau at about 70-75%? This is a striking feature of the plots, but the explanation may not be obvious to readers.

9) Figures 1D/1E: What was the concentration of B-glucan used in this experiment? This could be included in the figure legend. If greater than 1ug/ml this means that the % of active cells in Figure 1B matches the % of cells with BCL10 assemblies in Figures 1D/1E, which is potentially an important point.

10) Use of both 'BCL10' and 'Bcl10' when referring to the protein.

11) In the supplementary figures there are some formatting problems/missing words in the figure legends. In Figure S11 there is a black box covering the lower part of the figure.

References used in this review

Chakravarty, A.K. et al. (2020) "A Non-amyloid Prion Particle that Activates a Heritable Gene Expression Program," Molecular Cell, 77(2), pp. 251-265.e9. doi:10.1016/j.molcel.2019.10.028.

Iserman, C. et al. (2020) "Condensation of Ded1p Promotes a Translational Switch from Housekeeping to Stress Protein Production," Cell, 181, pp. 818-831.e19. doi:10.1016/j.cell.2020.04.009.

Joyner, R.P. et al. (2016) "A glucose-starvation response regulates the diffusion of macromolecules," eLife, 5. doi:10.7554/eLife.09376.

Munder, M.C. et al. (2016) "A pH-driven transition of the cytoplasm from a fluid- to a solid-like state promotes entry into dormancy," eLife, 5(MARCH2016). doi:10.7554/ELIFE.09347.

Riback, J.A. et al. (2017) "Stress-Triggered Phase Separation Is an Adaptive, Evolutionarily Tuned Response," Cell, 168(6), pp. 1028-1040.e19. doi:10.1016/j.cell.2017.02.027.

Schlauderer, F. et al. (2018) "Molecular architecture and regulation of BCL10-MALT1 filaments," Nature Communications 2018 9:1, 9(1), pp. 1-12. doi:10.1038/s41467-018-06573-8.

Significance

The existence of a nucleation barrier had already been postulated, based on structural and other studies (referenced by the authors), it had lacked a rigorous demonstration. This work provides that demonstration, which is important for the signalosome field and more broadly applicable to researchers studying cellular decision making. The study further demonstrates that DaMFRET is an excellent to study protein assembly processes in their native environment, allowing the authors to tackle a question that would have been technically very difficult to address otherwise.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Gama et al. use a biophysical assay DAmFRET, structural analysis, and optogenetic tools to uncover the nucleation mechanism of CBM signalosome. They performed experiments first in yeast cells that lack death folds or related signaling networks, then confirmed their discoveries in human cells. The results presented here are clear and convincing. The paper is very well presented and clearly written.

They found it is the CARD domain of BCL10 that acts as a molecular switch that drives all-or-none activation of NF-kB. Monomeric BCL10 possesses an unfavorable conformation and serves as a nucleation barrier, keeping BCL10 in a supersaturated inactive state that allows for binary activation upon stimulation.

They also characterized CARD9 CARD domain and a coiled-coil region. They reasoned that CARD9CARD functions as a polymer seed to nucleate BCL10, and that the coiled-coil region has multimerization ability to facilitate nucleation. Furthermore, they characterized that MALT1 activation doesn't depend on BCL10 polymers but its own proximity. And MALT1 induces graded NF-kB activation, thus further demonstrating the binary activation is conferred by BCL10.

Major comments:

1) Fig S1D and E, the authors used TNF-a to activate NF-kB independent of CBM signalosome and found the activation in each cell increased with dose. In contrast, CBM activation led to bimodal cell activation. The authors claim that this is evidence that positive feedback upstream of NF-kB. We do not believe this claim can be made from this comparative experiment alone. We agree that positive feedback is important for activating an NF-kB response, but the comparison between CBM and TNFa is inaccurate and glosses over published data. Specifically, there is published data that TNF-a does activate a 'switch-like' or digital response, as defined by the translocation of p65 (see (Tay et al. 2010) among other studies that have examined p65 translocation at the single-cell level). The difference in T-sapphire expression between CBM and TNF activation is most likely due to TNFa induced oscillations of p65 translocation (although this is speculation on our part). Therefore we suggest to the authors that the TNF-a data (Fig S1D and E) should be omitted, as the claim of switch or not-switch as pertains to TNF signaling is more complex and nuanced than presented here. We believe omitting this data will strengthen the manuscript and avoid confusion in the field. The bimodal expression of the T-sapphire NF-kB reporter driven by the CBM signalosome activation is sufficient to claim an all-or-none response.

2) Fig 3B, the authors introduced CARD9CARD-µNS as a stable condensed seed for BLC10. However, considering CARD9CARD can form polymers at high concentration (Fig 3B and S3D), are these high expression levels of CARD9CARD able to induce BCL10-mEos3.1 assembly (as measured by DamFRET in yeast cells)? Can the authors examine BCL10 FRET at these high expression level of CARD9CARD? We assume that BCL10 will be assembled in these cells. This would provide a valuable control experiment and support the author's conclusions.

3) Fig 3C, the text said "Whereas WT CARD9CARD assembled into polymers at high concentration, the pathogenic mutants R18W, R35Q, R57H, and G72S failed to do so (Fig 3C and S7B,C), explaining why they cannot nucleate BCL10". This claim that these mutants can not nucleate BCL10 does not have a figure call out or a reference. The authors then show the results in Fig 3E which supports this claim. Even though they were done in the context of full length CARD, all proteins contain the I107E mutation that releases autoinhibition. For clarity, the authors should consider rearranging the text to avoid explaining a phenomenon and making conclusions before showing the results.

4) Fig 4D, E and Video 1, the authors showed the nucleation of BCL10 into puncta within live cells is followed by p65 translocation to the nucleus. The authors claim that 'this result suggests that BCL10 is indeed supersaturated prior to stimulation' (paragraph 2 section titled BCL10 is endogenously supersaturated'). We fail to understand how this live-cell experiment leads to the conclusion BCL10 is supersaturated before stimulation. We think this text should be deleted from the text, or put into context with the DAmFRET data that lead the authors to make this claim. It would be interesting for the authors to define in discussion what are the golden criteria to claim a protein exists in a supersaturated state with live cells (by microscopy or other methods)? Adaptor protein assembly into puncta and the subsequent nuclear translocation of transcription factors is a common phenomenon across signalling pathways. Not all these pathways rely on signalling adaptors existing in a supersaturated state. The field of cell signaling (and cell biology in general) would benefit from a detailed definition of how these physical-chemical definitions of proteins are supported by experimental data. We believe that this paper will become a seminal paper in the field, and future work will benefit from a clear definition of how a claim of supersaturation is derived from the data.

5) Regarding the supersaturated state of BCL10, the authors convincingly use optogenetics to show how transient assemblies of CARD-Cry2 can template BCL10 assembly. This is a convincing experiment that shows templated nucleation of BCL10. To strengthen the claim that BCL10 is supersaturated endogenously we suggest the author quantify the expression of BCL10-mScarlet and CARD-Cry2 and ideally show that this phenomenon can be observed at expression levels equivalent to endogenous.

Minor comments:

1) Special character "delta" is not displayed in the text (instead only a space).

2) Several cell lines including mouse, human, and yeast lines were used across this manuscript. It would be clearer and more helpful if the exact cell type of the line could be indicated. Such as, "BCL10-mEos3.1 yeast cells" instead of "BCL10-mEos3.1 cells", "BCL10-mScarlet HEK293T cells" instead of "BCL10-mScarlet cells".

3) Fig 5B, the authors indicated that BCL10 colocalized with CARD9CARD, then please show the merged image as well.

4) Fig 6E, authors claimed that cells were stimulated with blue light for the indicated durations. The longest duration is 12 hours. Please specify if it was continuous exposure or several rounds of exposure in the indicated durations.

Significance

This work used a combination of FRET and optogenetic tools to engineer CBM signaling and visualize the effects. They incorporated knowledge from structure biology, together with their results from mutations and truncations, dissected the significance of each protein in CBM signalosome, and demonstrated in detail how higher-order assemblies make all-or-none cellular decisions. We believe this paper will be a seminal paper in the field of cell signalling and cytoplasmic organization. It defines a new paradigm of macromolecules assembly of signalling complexes as being dependent on protein existing in a supersaturated state. Importantly this paper opens up new questions regarding macromolecular signaling complexes (found in many innate immune signaling pathways): How is protein supersaturation maintained and used throughout evolution to construct biochemical signalling switches?

This paper will be of particular interest to scientists working on immunity and cell signalling, especially in the field of higher-order assemblies. However, we feel the impact of this paper goes beyond these fields, and we believe this manuscript will be of broad interest to the cell biology and biophysics communities. For reference, our expertise is in innate immunity and cell biology.

Referees cross-commenting

In general, I agree with reviewer 4. However, I'm afraid I have to disagree with reviewer 3 that the paper requires 'a major overhaul'. I also believe that reviewer 3 suggestion #1 to use qPCR to assess NF-kB target genes is not a 'constructive and realistic suggestion'. Or, to put it another way, not within the guidelines of the RC for reviewers. This type of suggestion is too open-ended to be of use to the authors. Which should the authors analyze of the tens to hundreds of genes activated by NF-kB? A rigorous and robust editor should ignore this comment.

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Reply to the reviewers

Two reviewers commented on the smeared appearance of Tae1 bands in our Western blot analyses (Figure 4F and 5B) and asked us to improve their technical quality.

-We agree and will repeat these experiments with more careful attention to lysate preparation, using a higher percentage SDS gel for better separation of low molecular weight proteins as suggested.

Reviewer 2 requested that we assess how Tae1 variants impact interbacterial competition outcomes.

-We agree that this would be interesting to take a look at. While this will not be feasible for every variant we examine in the paper, we can conduct comparative interbacterial assays between P. aeruginosa and E. coli using P. aeruginosa strains with a tae1 point mutation for c110s. Given that our biochemical experiments show that this hyperactive variant evades inhibition by the cognate immunity protein, we expect that this may decrease P. aeruginosa fitness, even in the context of competition.

More generally, we think that examining Tae1 variants in the context of interbacterial competitions would be a critical orthogonal approach in order to validate that the DMS results have any bearing on competition outcomes. However, we feel that major focus of this paper is on the more molecular and biophysical insights that our approach can offer. Our study tests our assumptions about the kinds of features and surfaces that are important for proteins that engage with non-canonical complex substrates. It is, of course, interesting to think about the implications of this for physiological phenotypes and the drivers of toxin evolution. It is also exciting to imagine how this kind of information could be used to one day engineer certain interbacterial outcomes. We hope that others in the field will push our efforts into these directions, but we do not feel that these directions are essential for our conclusions. However, our conclusions on the molecular and biophysical aspects have helped generate interesting hypotheses in microbial ecology that could be largely followed up on by others.

In order to conduct well-controlled P. aeruginosa:E. coli competition assays for more Tae1 variants, we would need to generate a significant number of new P. aeruginosa strains encoding point mutations for each of our variants across several genetic backgrounds. The competitions themselves also require a considerable amount of work to optimize and quantify. We are able to do this for one of the variants as previously mentioned (C110S). It’s important to note that the first author of this paper, who was the primary driver of this work, is no longer in my lab or in academia. As for myself, I am also in the middle of a transition out of academia and am actively ramping down my lab at UCSF. I no longer have the space or appropriate set-up to support this longer-term effort.

Reviewer 2 asked that we examine Tae1 (WT and C110S) expression levels in vivo to more precisely examine whether increased self-intoxication by Tae1C110S in P. aeruginosa was due to differences in toxin activity or toxin levels.

We agree with this suggestion and will look at toxin protein levels by Western blot analysis in the context of P. aeruginosa cells grown 1) alone on solid media and 2) together with E. coli on solid media during interbacterial competition using conditions that match our other competition assays.

All 3 reviewers asked us to provide more experimental evidence addressing the hypothesis that differential peptidoglycan (PG) affinity across Tae1 variants could explain variation in toxic activity.

-We agree that this is an interesting point to follow up on further. To be clear, we also do not know whether this hypothesis is true at this stage, and the answer is not necessarily critical for our central advance, but we would like to give it a try! We have devised an approach to ask the question experimentally across a subset of our deep mutational scanning (DMS) variants.

Reviewer 1 suggested that we quantify in vitro binding affinities for PG using isothermal titration calorimetry (ITC). However, given that ITC requires high concentrations of well-defined homogeneous substrates, which we are not able to generate for more complex higher order structures of cell wall PG, we propose a pull-down based approach.

Briefly, we plan to conduct pull-downs using insoluble, purified cell wall sacculi from our two E. coli grown under the two conditions as bait for recombinant Tae1 proteins. Given that intact sacculi or inherently insoluble, we can simply collect bound Tae1 through centrifugation of sacculi pellets and examine the amount of Tae1 associated by Western blot analysis. These analyses will need to be conducted across a titration of Tae1 concentrations and also with catalytic activity inhibited to avoid solubilization of sacculi. We will block Tae1 hydrolysis by carrying out pull-downs in the presence of a general commercially-available cysteine hydrolase inhibitor, E64. If there is indeed differential affinity for PG underlying lytic differences across Tae1 variants, we would expect to see greater relative association of Tae1 variants with the type of cell wall sacculi that they more effectively lyse in our DMS screen. We would expect the reverse trend to also be true (lower affinity for less active variants).

Reviewer 1 would like to know if we have done lysis experiments with any E. coli mutants that only impact PG density but not PG polymer structure? If they haven’t tested any E. coli mutants, have we done lysis experiments using drugs that have a similar impact on PG? Even if we don’t include these data in the paper, the reviewer would like us to comment on the trends we have observed.

We have not done experiments in any mutants or chemical backgrounds known to only impact PG density but not polymer structure. We think this would be a very interesting angle! But unfortunately this is outside the scope of this study. It would require that we first experimentally confirm that the restrictive effect on only density is clearly demonstrated using a variety of techniques, including microscopy, chemical analyses, and biophysical probing of sacculi.

Reviewer 1 asked for additional DMS screens in more conditions

We love this idea! In fact, we hope that others are motivated to adopt our workflow to run many more DMS screens for T6S toxins, as we believe these screens provide a lot of useful and sometimes surprising insights that could be of great interest to others. However, we believe that the primary goal of this paper is to establish this methodology as a compelling approach for studying toxins and, more generally, proteins with complex cellular substrates. It does not necessarily fall within the scope of this paper to fully assess the mechanistic implications of cell wall diversity across a wide range of conditions.

In our experience, rigorously conducting DMS screens requires a significant amount of effort and resources to establish consistent experimental conditions. Also, a non-trivial number of costly sequencing-based experiments are required across control and variables for the results to be statistically sound and meaningful. Furthermore, experimental validation of results are ultimately important for our ability to confidently generate hypotheses stemming from these datasets. As stated above, the first author of this paper, who was the primary driver of this work, is no longer in my lab or in academia. As for myself, I am in the middle of a transition out of academia and am actively ramping down my lab at UCSF. I no longer have the space or appropriate set-up to support this longer-term effort.

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Referee #3

Evidence, reproducibility and clarity

This paper by Radkov et al. represents an extensive structure-function-evolution treatment of the Type VI secretion effector protein Tae1. Using mutational scanning, the authors identify multiple residues that either enhance or reduce Tae1 function in an E. coli model, and validate these residues through direct functional assays. The main conclusion is that Tae1 contains a surprising number of non-intuitive residues important for its activity, particularly several surface-exposed residues far from the active site. The authors then suggest that these residues mediate binding to specific PG architectures and supply some evidence that the functional mutation landscape changes when the DMS assays is repeated in E. coli with altered cell wall architecture. Lastly, natural variants of Tsae1 are identified and discussed in the context of the trade-off between optimal toxicity and maintenance of self-immunity.

I have no major comments. The study is beautifully-done, with all controls in place. It might be worth following up on their putative PG binding residue mutants with an additional binding assay (MST, or just a crude cell wall pulldown assay), but that is not critical to support the main conclusions.

Minor comments

• The Western Blot of the vector control in Fig. 4F has the same impurities as the one in Fig. 5 B. Was the control blot re-used? If so, please indicate in the figure legend. Also, please show full Western Blots in supplemental material.
• Small typo in Fig. 5 legend ("does is not")
• The citation in line 108 seems a little off - that does not seem to support a physiologically relevant context for Tae.
• Line 122/123 - something seems to be missing in this sentence.
• Line 148 - this is not clear to me. Did they sequence plasmid barcodes (are those in the plasmid backbone?), or the mutated orfs?

Significance

This paper makes an impactful contribution to the open question of substrate- and species-specificity of PG hydrolases, particularly those weaponized by Type VI secretion systems. The major advance here is that PG binding by the hydrolase, and PG architecture of the substrate, are important determinants of Tae function and that this has important evolutionary consequences. The study will be of interest to the Type VI secretion community, but also to the PG turnover field.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript aims to investigate the molecular basis underlying the differential toxicity of the bacterial T6SS amidase effector (Tae) by using Pseudomonas aeruginosa Tae1 as a model. The rationale is that while Tae is a conserved T6SS toxin degrading bacterial peptidoglycan (PG) by specific cleavage activity, different Tae toxins of the same family exhibit distinct lysis/antibacterial activity. Thus, the authors used combination of a deep mutagenesis scanning (DMS) coupled with fitness assay, NMR, and PG-binding/amidase activity to address this question by expressing Tae1 variants in E. coli. Besides finding the residues at/near the catalytic site critical for amidase activity, the authors further discovered many surface-exposed resides distant from the catalytic cleft also contributed to Tae activity likely by affecting binding or hydrolysis of PG. The authors further explored whether the residues contributing to loss or gain of Tae1 activity could be different against different PG structure by performing the same suite of DMS analyses from E. coli grown in the presence of D-Met, which resulted in reduced PG density and crosslinks. They discovered the fitness landscape of Tae1 variants shift dramatically, suggesting that Tae1 toxicity is highly context-dependent and optimizable for specific PG forms. A hyperactive Tae1 C110S variant is also naturally encoded in a subset of Proteobacteria outside of P. aeruginosa. This further led to a prediction that Tae1 C110S variant may evade binding and inhibition by cognate immunity, which was confirmed by the higher binding affinity of WT Tae1 than C110S Tae1 determined by ITC analysis. Together, the authors concluded that substrate-specificity and toxin-immunity interactions are the two distinct selective pressures for shaping diversity across the Tae1 toxin superfamily.

Major comments:

This is a well thought, carefully designed and executed research article reporting important and interesting findings. The conclusions made are mostly supported by the provided data. However, the toxicity assay for Tae1 variants except C110S was only validated by ectopic expression in E. coli or in vitro activity assay. Considering Tae1 is a bacterial toxin involved in interbacterial antagonism, the mutants with newly discovered key residues contributing to loss or gain of function shall be also evaluated for their role in the context of interbacterial competition, not simply by the cell lysis assay of expressed Tae1 variants in E. coli. Below are the specific comments that shall be addressed in order to claim the findings of this work .

1. It is an exciting finding that several surface residues distal from catalytic core mediate PG hydrolysis or binding. While the validation of their cell lysis activity by expressing each Tae1 variants fused with LepB signal peptide is informative, the role of these surface residues in toxicity shall be also tested by interbacterial competition assay either using E. coli or susceptible Pseudomonas aeruginosa strain as a prey. Tai may be expressed in E. coli prey to determine its neutralization activity during interbacterial competition context.
2. Based on the results that fitness landscape of Tae1 variants grown in the presence or absence of D-Met, the authors stated in line 334 "Condition-specific phenotypes suggests that Tae1 toxicity in vivo is highly context-dependent and optimizable for specific PG forms." However, there could be other physiological changes due to D-methionine. To claim this, the authors may test the surface residues with altered impacts on fitness between two growth conditions for their PG-binding activity using PG isolated from culture in the presence or absence of D-Met .
3. Quality of western blotting for Tae1 variants in Fig. 4F, 5B should be improved as the signals from WT is not clearly detected for comparison. The authors may use higher percentage of SDS-PAGE for better resolution of small Tae1 proteins. Relevant protein marker should be indicated. In addition, why there is no western blot analysis of C30A variant?
4. It is exciting that a hyperactive Tae1 C110S variant is also naturally encoded in a subset of Proteobacteria outside of P. aeruginosa. The authors showed higher binding affinity of WT Tae1 than C110S Tae1, which correlated with lower fitness of C110S variant in a competition setup (Fig. 6C, 6E). The authors suggest that "Tae1 of C110S variant lyses kin cells at a faster rate than Tae1 WT can bind and inhibit killing, leading to a fitness cost for this strain" (Line 460-463). To claim this, expression levels of endogenous Tae1 of both WT and C110S should be shown as well as their secretion levels to rule out the effect of protein abundance and secretion levels may affect the fitness. It would be also recommended to set up a real interbacterial competition assay by selecting the survival cfu of prey cells.

Minor comments:

1. Is Tae1 previously named as Tse1? Please clarify and indicate the previous name and accession number. As stated in Line 61" Although many T6S bacteria deploy similar toxins, interbacterial outcomes can vary considerably depending on the bacterial species engaged in T6S-mediated competition", the authors should also cite other relevant references showing differential Tae toxicity from different organisms (such as Serratia marcescens. Ssp1 and Ssp2 from English et al., 2012, Enterobacter cloacae Tae4 from Zhang et al., 2012, and Agrobacterium tumefaciens Tae from Yu et al., 2021). The manuscript shall gain more insights by discussing the biological significance of their conservation yet distinct toxicity and potential condition-specific activity of Tae toxins studied in different bacterial lineage besides those in P. aeruginosa.
2. Line 111-113 "the Tae1 protein from P. aeruginosa, which is injected into E. coli and leads to cell lysis": citations are needed here.
3. The heatmap in Fig. 4E also include those with mixed phenotypes. Are the averaged fitness score meaningful since some residues are likely derived from the mixed phenotypes, which make the data less reliable. I suggest the authors to only include those true GOF or indicate which one is true GOF and which one is from mixed phenotypes.

Significance

This manuscript used innovative approaches to investigate the mechanism and biological significance underlying the differential toxicity of the bacterial T6SS amidase effector (Tae). Tae superfamily can be classified into four families (Tae1-4), which are universally encoded in T6SS of diverse Proteobacteria. It is intriguing that Tae toxins classified in the same family produced by different bacterial lineage/strains exhibit distinct lysis/antibacterial activity but the underlying mechanism is unknown. This manuscript provided evidence suggesting the existing natural diversity of Tae1 in substrate-specificity and toxin-immunity interactions, which are the key selective pressures for shaping diversity across the Tae1 toxin superfamily. The findings provide an explanation how bacterial toxin effectors evolve in the context of interbacterial antagonism, which have not been answered from previous literatures (Russell et al., 2012; English et al., 2012; Chou et al., 2012; Zhang et al., 2013; Yu et al., 2021). The methods combining deep mutagenesis scan, biochemical, and structural analysis provide a comprehensive and unbiased view to understand the diversity of Tae1 family and their corresponding phenotypes and biochemical features. As a molecular microbiologist working on bacterial secretion systems and their effectors not familiar with structural studies, I am better qualified in evaluating the biological and biochemical data but not the structural studies in NMR and structural modeling. However, I highly appreciate the authors who nicely presented the story by explaining the concept of each method which allows the reviewers/readers to understand the data even though not within their expertise.

Russell et al., Cell Host Microbe 11:538-549. https://doi.org/10.1016/j.chom.2012.04.007 English et al., Mol Microbiol 86:921-936. https://doi.org/10.1111/mmi.12028. Chou, S. et al. Cell Reports 1, 656-664. DOI: 10.1016/j.celrep.2012.05.016 Zhang et al., J Biol Chem 288:5928-5939. https://doi.org/10.1074/jbc.M112.434357 Yu et al., J Bacteriol 203:e00490-20. https://doi.org/10.1128/JB.00490-20.

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Referee #1

Evidence, reproducibility and clarity

In this paper the authors characterize a member of the bacterial T6SS amidase effector (Tae) superfamily of toxins that are delivered by the Type 6 Secretion system of Pseudomonas aeruginosa into target prey bacterial cells. The authors focused on why this toxic effector because it shows different potency when delivered to different target species despite the fact that all target species have peptidoglycan, the substrate that Tae attacks. The authors use powerful approaches such as deep mutational scanning (DMS), to define critical residues near the Tae active site and other sites that affect its enzymatic activity and interaction with its cognate immunity protein. The discovery of the C110S mutation which increases Tae activity is a fine example of the power of this approach. When combined with structural biological analysis, the results of the study and discussion in the manuscript is of broad interest to the community of scientists interested in toxic bacterial effectors that digest the cell wall and also others that are interested in the remodeling of peptidoglycan during cell growth and shape determination. I would recommend acceptance of this paper for publication after the authors address a few minor comments:

1. The authors observe PG changes caused by D-met (Fig 4 and relevant text). I'm curious as to whether changes in lysis are caused by differences in PG crosslinking or PG density. They point out that the sugar binding surface of WT could localize the PG digestion (paragraph at line 521) which would no longer be required at lower density PG. However, my concern is that they propose that variation in Tae activity in different target organisms could be explained by differences in PG affinity without testing this DMS screen in any other strain, let alone species.
2. They also don't screen any Tae1 homologs, though they address one residue in their phylogeny. I'm not sure if there are species with such a low-density PG layer, so their repeated connection to Tae's variable lytic capacity between species in the text and discussion seems tenuous until they do a DMS screen with their plasmid library in another species (or at least another strain).
3. If WT Tae1 has some checking mechanism to ensure it's in the PG layer, I can imagine it might be slower to fire in less dense PG. That would also make sense given the chemical perturbations in Fig 3 where residues on the opposite face from the catalytic site are involved in binding PG. I would be interested to see if WT Tae1 can bind multiple PG chains or binds at higher affinity. A calorimetry approach like the one they use later may answer those questions, but that might be outside the range of this paper.
4. It's also worth looking around for E. coli PG synthesis mutants that don't change the PG polymer structure, only the density. That might also happen if the bugs are grown under osmotic stress, which should at the very least stretch out the sacculus. That may help differentiate differences in PG composition from differences in chain density. Perhaps subinhibitory amounts of drugs that affect PG synthesis my have the same of effect of increasing or even decreasing Tae potency by modulating PG density. Of course, this may have to be done under protective osmotic conditions. Have the authors tried these sorts of experiments and if so, please comment on the trends even if the data will not be presented in this report.

Significance

When combined with structural biological analysis, the results of the study and discussion in the manuscript is of broad interest to the community of scientists interested in toxic bacterial effectors that digest the cell wall and also others that are interested in the remodeling of peptidoglycan during cell growth and shape determination.

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Reply to the reviewers

1. General Statements [optional]

We would like to thank the reviewers for their prompt and thoughtful input on our manuscript, and their willingness to participate in more portable review through ReviewCommons.

2. Description of the planned revisions

Reviewer #1, major comments:

• A major concern is that the data are reported and analyzed on a per tomogram basis when many tomograms contain multiple mitochondria. Given that the mitochondria appear mostly well separated in Sup. Fig 1 with only a few connections visible, and the high degree of pleomorphism noted by the authors, I would strongly suggest that the authors use each mitochondrion as the basis for reporting their metrics rather than the FOV/tomogram as this would avoid mixing metrics from different mitochondria that may be in different states (e.g., fusion/fission). This would apply to data shown in Figures 3, 4, 5, and 6.

We appreciate the reviewer suggestion to separate on a per mitochondrion vs per tomogram basis for our analysis. While we do not anticipate that this will significantly change the overall findings, we agree that splitting per mitochondrion will account for any possible variability between mitochondria within the given field of view. Furthermore, we anticipate that this will actually improve our analysis and statistical power by effectively increasing the total sample size per experimental group. For our next revision, we will divide surfaces on a per mitochondrion basis within a given tomogram, and re-run the full analysis pipeline. Additionally, per reviewer request, we will include an output histogram for each measurement per mitochondrion surface in a supplemental figure.

• In Figure 3C the authors show the combined distribution of OMM-IMM distances within each condition. This may obscure some variability within populations. Individual histograms for all mitochondria should be included as supplementary material. Currently, it is difficult to judge if the peak of the combined distribution is appropriate and impossible to judge the variability between tomograms (preferably mitochondria, see above comment). Additionally, the shape of the distributions appears significantly different between conditions, suggesting that selecting a single peak value as representative and the basis for the statistical tests (Fig 3D) might not be appropriate. Please comment.

We will include individual histograms for each measurement per mitochondrion surface in a supplemental figure.

We agree that peak-based statistical tests limit our ability to quantify more complex differences, and this is why we chose to output histograms in addition to violin plots, so that shape differences can be observed qualitatively. A major challenge of shape-based statistical quantification is the assessment of independent samples. By using peak-based quantification, we could assume that each tomogram (and in the planned revision, each mitochondrion) is an independent sample, but for shape distribution this is inappropriate since there is more than one value represented per tomogram. Running a KS test with N equal to the number of tomograms yields no significance even in the visible cases where the shape appears very different.

However, the number of triangles also poorly represents the number of independent samples, since 1) the number of triangles used to represent a surface is somewhat arbitrary and remeshing can change it dramatically and 2) Our chosen triangle size is considerably smaller than the visually observed feature size in order to allow effective vector voting in the pycurv AVV algorithm. The result of this is that when we use a KS test on the distribution of values per triangle, even visually identical distributions yield p-values below 10^-200.

We do estimate the approximate smallest feature size during our calculations, since that is used to generate the radius used by pycurv in vector voting, to be 12 nm (the radius hit parameter in pycurv). During a public presentation of this work an audience member suggested that we might use the area implied by this feature size (~450 nm^2) as the size of an independent sample. This would yield around 1000 independent samples per tomogram. Because the choice of feature size is heuristic and manual, this is not as statistically sound as the peak-based metric, which is why we believe that the more conservative peak-based statistical testing is the gold standard for proving differences, but we believe this will be the most reliable way to quantify differences in shape of distributions. We plan to implement this quantification in our revision, and will evaluate whether it gives “expected” statistical results by a bootstrapping approach using subsampling of triangles from the same vs different mitochondria.

We would welcome reviewer suggestions for additional shape-based metrics and will explore other potential metrics to capture shape as part of our revision. While our peak-based metrics demonstrate our ability to statistically capture small changes in ultrastructure with this method, shape-based quantification will significantly enhance the capability to capture finer changes in structure that may be critical to understand physiologically.

Once this additional testing is complete, we will add a section to the results section describing choice of statistical framework. We also plan to generate a supplementary table showing the results of the peak-based quantification alongside all shape-based quantifications.

• In Figure 4C-F, again combined distributions are shown. Authors should include individual histograms for all mitochondria as supplementary material. The diversity of distributions in the metrics are more pronounced than the distances in reported in Fig 3, again making assessment of variability difficult and raising doubt about using the single peak value.

We will include individual histograms for each measurement per mitochondrion surface in a supplemental figure.

As we describe above, we will make test several options for distribution-based statistical quantifications and incorporate the results in the manuscript. We expect them to be useful for every measurement we make.

• It would be helpful to include the curvature or curvedness of the OMM for each mitochondrion in the supplementary material. The data to correlate OMM curvature with elongated/fragmented mitochondria should be available and might be of interest to some readers.

We will calculate curvedness of the OMM for each mitochondrion and include these data in the supplemental material. The inverse of the curvedness of the OMM gives a reasonable approximation of the radius of the mitochondrial “tube”, a feature which can be challenging to quantify fully automatically, and we agree that this may be of particular interest to some of our readers – particularly if morphology changes or stress-driven changes alter that radius in a statistically significant way!

Reviewer #1, minor comments:

• For all data, exact n per condition should be given (in text and captions as appropriate), not a range for the whole set.

We will report the exact n per condition in text and in captions after we separate our data on a per mitochondrion basis and update the analysis.

• Fig 5E middle, legend obscures some of the data.

We will reformat the graph such that the legend does not obscure the data after we separate our data on a per mitochondrion basis and update the analysis.

Reviewer #2, major comments:

Barad, Medina et al. presents a new toolkit for the analysis of membrane ultrastructure in cryo-tomograms. More specifically, the toolkit is designed to compare curvature, angles and spacing between different membrane types in mitochondria. These analyses allow for the quantitative comparison of membrane features e.g. for different growth conditions. To demonstrate the utility of the toolkit tomogram datasets of mitochondria in the presence and absence of ER stress were analyzed. The authors conclude that ER stress affects mitochondria morphology through remodeling of the membrane structure. The presented biological results and statistics are convincing and show active mitochondrial membrane remodeling in the cell when exposed to ER stress. It is also clear that there is a need for more quantitative evaluation based on the wealth of tomographic image features and mitochondrial membranes are certainly a well-chosen application. For this purpose, the authors developed a new workflow even though most of the discussed analyses are very specific to mitochondrial structures. Therefore, broader applications of these tools to other organelles are not easily envisaged without significant adaption. In that context, the title and abstract overpromise a much more powerful utility that can be applied to any other membrane analysis. Rather it seems that the proposed workflow is more of a specific tool or a pipeline for mitochondrial inner and outer membrane analysis instead of a toolkit for general morphological analysis. Hence, the manuscript cannot be accepted in its current form. In particular, the structure needs a significant rework of editing to become more comprehensible.

We appreciate the criticism that our workflow as implemented at the time of preprint is seemingly too focused on mitochondrial membranes and is not general. We’ve overhauled our workflow into a configurable (through a project YML file) scripted workflow that can take a folder with arbitrary segmentations and convert them into high quality meshes, followed by per-triangle quantification of the four primary metrics we describe in the manuscript: inter-membrane distance, intra-membrane through-space distance, curvature, and orientation. Generating fully automated visualization tools is more challenging, because which quantities are measured and how they are sub-classified (e.g., as we did for cristae, junctions, and IBM) is very project-specific; however, we did convert our visualization script into a library of utilities to combine tomograms into experiment objects, with methods to serialize for rapid access and functions for generating statistics and plots. Our converted visualizations script has been reorganized to act as an example of how similar questions could be asked for arbitrary membranes.

We propose to further demonstrate the generality of this updated approach by segmenting several examples of another organelle, the autophagosome, found in our dataset and applying the workflow to them in a supplementary figure.

The focussing to a method paper will also require more in-depth descriptions of the methodology in the main text. Although the code is deposited at github, there is no script-based workflow and description presented in the manuscript. Although Figure 1 puts the work into context of tomography, it remains very superficial on the image analysis. What are the input and output formats required for each step to follow the sequence of the workflow and at which steps critical interactive input is needed? What are the hardware requirements (CPU, GPU) or performance characteristics (CPU hours for certain operations)?

In addition to the changes mentioned above, we also added a “Supplemental Table 1” detailing computational requirements and time for each step.

We expanded on the description of this approach in the first paragraph of the results section:

“With this strategy, we were able to segment 32 tomograms containing mitochondria, divided between the elongated and fragmented bulk morphology populations and the two treatment groups (Figure 2, Supplementary Figure 1). The segmentation output was fed into the fully automated surface morphometrics pipeline (Figure 2B, Supplementary Figure 2, Supplementary Table 1). The voxel segmentation was converted to high quality membrane surfaces using the screened poisson algorithm32. Next, these surfaces were converted into triangle graphs and curvedness was estimated using pycurv15, and the distances within and between surfaces as well as the relative orientations of different surfaces were estimated using the resulting graph. Finally, the quantifications for each tomogram were combined into experiments to allow aggregate statistics and visualizations. This 3D surface morphometrics pipeline is configurable for any segmented membrane and is available at https://github.com/grotjahnlab/surface_morphometrics.”

We added a description of the up to date workflow in the methods section:

“Software workflow

The surface morphometrics pipeline is a python 3 scripted workflow with requirements that can be installed as a conda environment contained in an environment.yml file. The workflow is fully scripted and configurable with a config.yml file, and is run in 3 steps, with statistical analysis and visualization as an optional fourth step. First, a segmentation MRC file is converted automatically to a series of surface meshes formatted in the VTP file format. Second, for each mesh, the surface is converted to a graph (tg format) and curvature is estimated using pycurv. Third, orientations and distances between and within surfaces are calculated using the resulting graphs, and a CSV with quantifications as well as a final VTP surface file is output with all quantifications built in. Fourth, the outputs from multiple tomograms are combined for visualization and statistical analysis. Times and computational requirements are shown in supplementary table 1.”

Figures 3-7 contain colorful 3D renderings of the measured quantities. In addition, they are filled with histograms of every possible quantitative parameter, which often are not very significant or different between. The authors should focus the main results and the figures to show the most relevant and significant findings and put the remaining panels and results into the supplement.

Figures 3-7 were organized around the different methodologies (inter and intra-membrane spacing, curvature, orientation) but we agree that focusing to the main results of each methodology is sufficient to show the value of these results. We propose to address this criticism by moving figure 4D,F (inter-crista and junction spacing), figure 6 E,G (the junction measurements) and Figure 7 to supplemental figures. These supplemental figures will also be joined by the previously requested OMM curvature analysis and our proposed analysis of autophagosomes.

One of the key steps is the generation of a smooth surface from a segmented membrane, there is a question whether true membrane disruptions will be smoothed and may be overlooked in this approach. When these disruptions present true membrane ruptures, they may be of particular biological importance. The authors should support the choice and selection of the smoothing parameters in order to illustrate this potential pitfall.

The smoothing and hole-filling parameters are now configurable using the point_weight and extrapolation_voxels parameters in the config.yml file. Notably, the surfaces used for quantification used minimal smoothing, and any triangles more than a single voxel away from the point cloud were deleted, in order to ensure that the quantifications were minimally impacted by “hallucinated” surfaces. Additionally, the following text was added to the methods section discussion surface reconstruction:

“A surface mesh was calculated from the oriented point cloud using the screened Poisson algorithm32, with a reconstruction depth of 9, an interpolation weight of 0.7, and a minimum number of samples of 1.5. These settings were chosen to maximize correspondence to the data, rather than smoothness. The resulting surface extended beyond the segmented region, so triangles more than 1 voxel away from the point cloud were deleted. Interpolation weight (point_weight) and the mask distance (extrapolation_voxel) are both configurable in the surface morphometrics pipeline if more aggressive smoothing and hole filling are desirable.”

Throughout the manuscript, the authors mention statistical significance several times and one of the main aims of the study is perform statistical hypothesis testing. It is important to specify the significance test (not only in the methods) and the p-value in order to support this claim. In the manuscript, the authors use exclusively the Mann-Whitney test. What is the rationale for choosing this test? Have the authors considered comparing the total distributions and not just the peaks with e.g. a Kolmogorov-Smirnov test? For a statistical methods paper, there are also no discussion on error analysis.

This was a common concern raised by both reviewers, and we agree that a test based on total distribution would be more powerful than only looking at peaks. We address the use of the Kolmogorov-Smirnov test and the limitations we have run into thus far in our response to reviewer 1 in detail. In brief, KS tests tend to vastly overestimate statistical significance because the number of samples (the number of triangles) is vastly larger than the true number of independent features sampled in the data, so that even very similar looking distributions such as those in figure 5C yield p values in the range of 10^-200. We propose several approaches to better estimate the number of independent variables. We will also use a random subsampling approach within individual mitochondria to ensure sampling from the same distribution does not yield statistically significant results.

In addition to testing additional approaches to incorporate KS testing (based on estimation of number of independent features in each tomogram), we propose to improve our peak-based statistics by estimating a standard error for the peak of each tomogram using a bootstrap approach, getting the peaks from different random subsamples of triangles.

Reviewer #2, minor comments:

1. https://github.com/grotjahnlab/surface_morphometricsshould include an example data set or tutorial for dissemination.

We are in the process of uploading all frame-averaged tilt series, tomograms, segmentations, and reconstructed surfaces to EMPIAR. Additionally, we propose to implement a complete tutorial including a single tomogram for readier workflow testing, separate from the complete data upload.

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

Reviewer #1, major comments:

• As the work reported here is heavily computational, additional details about the computer hardware used and the time it took for the calculations to complete would be helpful for readers considering applying the code to their own data.

We appreciate the suggestion and included Supplementary Table 1 in the supplemental material outlining the computation time per step in our analysis pipeline:

“Supplemental Table 1. Approximate time and for each step of the surface morphometrics workflow.

Representative times and computational resources used for each step of the surface morphometrics workflow for each tomogram (unless otherwise noted) by the authors. Most time-intensive calculations were run in parallel on a compute cluster for each tomogram.

Step

Human Time (HH:MM)

Computational Wall Clock time (HH:MM)

CPU Cores Used

RAM Used

Automated initial segmentation (TomoSegMemTV)

00:10*

00:10*

8

64GB

Manual segmentation cleanup and classification

03:00

N/A

8

64GB

Point cloud conversion and mesh generation

00:01

00:03

4

16GB

Graph generation and curvature estimation (pycurv)

00:01

01:40

16

128GB

Distance and orientation measurement

00:01

00:10

16

128GB

Assembly of outputs from multiple tomograms into dataframes and serialization

00:01

00:10

1

16GB

Visualizations and statistical tests

00:01

00:10

1

16GB

* Tomosegmemtv is sometimes run iteratively with different settings to improve output. 10 minutes is approximately the time taken for a run without iteration, in the case of good output.”

Reviewer #1, minor comments:

• Pink and purple very close, consider alternative pair of colors or different shades to distinguish OMM and IMM

We kept OMM as purple but changed IMM to orange for Figure 3-7, and will make the associated changes to Figure 2 and Supplementary Movie 1 on final submission.

• Orientation of scaleboxes/scalebars should be consistent per figure panel. If knowledge of the axes is important to the reader, these should be included as well.

We followed the reviewer’s suggestion and updated the scale cubes to be standardized per panel.

• In the last sentence of the introduction, the term "organellar architectures" is used, instead of the previously defined "membrane ultrastructure." Consider changing for clarity.

We changed “organellar architectures” to “membrane ultrastructure” in the last sentence of the abstract.

• Inconsistent use of the phrase "cryo-electron tomography" after defining and using "cryo-ET"

We changed all instances of “cryo-electron tomography” to “cryo-ET” after defining in the first instance in the introduction.

• Authors argue that the distinction between curvedness and curvature is important and that curvature is less appropriate in this context, but then use curvature in the abstract, throughout introduction and in the results section. Usage can be improved for readability.

We changed all instances of “curvature” to “curvedness” throughout the text and figure legends.

• In section "Development of a framework to automate quantification of ultrastructural features of cellular membranes" the second last sentence should read "... higher quality membrane surfaces as compared..."

We changed “surface” to “surfaces” in text.

• In section "IMM curvedness is differentially sensitive to Tg treatment in elongated and fragmented mitochondrial networks" the fourth sentence should perhaps read "... despite apparent visual differences, no significant..."

We changed “difference” to “differences” in text.

• The term "cell's growth plane" is not clear from the text nor from Fig 6A. Do the authors mean surface of the substrate the cell is growing on?

We clarified and further defined the “cell’s growth plane” in the text by adding the following phrase:

“… the cell’s growth plane (i.e. the plane of electron microscopy grid substrate to which the cell is adhered) (Figure 6A).”

• In Materials and Methods:

• The authors report that manual back-blotting was used in a Vitrobot. This is non-standard usage and more details should be provided.

We added the following description to clarify our manual back-blotting procedure on the Vitrobot:

“After 8 hours of incubation, samples were plunge-frozen in a liquid ethane/propane mixture using a Vitrobot Mark 4 (Thermo Fisher Scientific). The Vitrobot was set to 37° C and 100% relative humidity and blotting was performed manually from the back side of grids using Whatman #1 filter paper strips through the Vitrobot humidity/temperature chamber side port. The Vitrobot settings used to disable automated blotting apparatus were as follows: Blot total: 0, 2; Blot force: 0, 3; Blot time: 0 seconds.”

• In section "Fluorescence Guided Milling" in the third sentence, the word "based" is repeated, second can be removed.

We deleted the second instance of “based” in this sentence.

• Symbol for degree (or the word degree) should be added to angular increment and tilt range for clarity.

Added degree symbols to the following sentence in the “Tilt Series Data Collection” portion of the materials and methods:

“Tilt series were acquired using SerialEM software (Mastronarde, 2005) with 2° steps between -60° and +60°.”

• Capitalization of TomoSegMemTV is inconsistent.

We changed all mentions to TomoSegMemTV.

• Fig 3 title - consider replacing "Inter-mitochondrial membrane..." with "Intra-mitochondrial membrane..." for clarity.

We clarified this point by changing “Inter-mitochondrial membrane distance” to “Distance between inner and outer mitochondrial membranes” in the figure legend:

“Figure 3. Distance between inner and outer mitochondrial membranes is dependent on mitochondrial network morphology and presence or absence of ER stress.”

• Fig 3C caption - should explicitly state it is a combined histogram and that the dashed lines correspond to the peak of the pooled data.

We changed “Quantification of” to “Combined histogram of” and added the sentence ” to each of the relevant figure captions (Fig. 3c, 4c-f, 5b-e, 6d-g, 7c):

“Dashed vertical lines correspond to peak histogram values of pooled data”

• Fig 6B and 6C caption - upper and lower parts not explicitly described.

We modified Fig 6B&C caption to more clearly describe the figure panel:

“(B) Two representative membrane surface reconstructions of lamellar Tg-treated elongated mitochondria, colored by angle of IMM relative to OMM.

(C) Two representative membrane surface reconstructions of a less rigidly oriented Tg-treated elongated mitochondria, colored by angle of IMM relative to the growth plane of the cell.”

Reviewer #2, major comments:

1. Title and abstract need to be toned down not to overpromise a very general toolkit. The presented method may be a tool or a collection of scripts - a toolkit can be used to address other types of (membrane) analysis problems. In the end, the analysis builds to a large extent on the previous developments and implementation of PyCurve. Perhaps, the most interesting contribution here is the application of the mesh generation by the Poisson reconstruction method to the segmented membranes, which is, however, well implemented in the used pymeshlab framework. The computation of distances and angles is straightforward.

We appreciate this critique and do not want to overpromise with our work, although we believe the overhaul to a fully configurable workflow addresses the primary concern. We are quite clear in the text that we build on top of pycurv, and recommend citation of the original tool as well as our pipeline in the github repository as a result. With that said,

We have changed the title as follows:

“Quantifying mitochondrial ultrastructure in cryo-electron tomography using a surface morphometrics pipeline”

We have also renamed our method to the surface morphometrics pipeline to reduce over-implication of generality, and made other small changes to increase degree of detail about what our method is resolving.

When reading the manuscript, the reader is left in the open whether this is a method paper or a biological results paper. The title/abstract suggests that this is a method paper and the manuscript is more of a mitochondrial membrane report in ER stress. Therefore, the title/abstract does not reflect the manuscript very well.

We aim to use this manuscript to describe the development of a workflow that enabled novel and interesting biological results. We adjusted the title to better match the combined development of a new pipeline and application to an interesting biological system as proof of concept:

“Quantifying mitochondrial ultrastructure in cryo-electron tomography using a surface morphometrics pipeline”

The manuscript also requires substantial structural editing. Several references to Figures are not appearing in the text in the order that the Figure panels are built. Excessive cross-referencing of figures also make the manuscript hard to read.

We simplified our referencing of figures and made sure the text matched the order of the figure panels.

The exact morphological discrimination between fragmented and elongated mitochondria is not easily understood from the results section. What is really meant by blinded manual classification? It only became clear when reading the methods. The results section should stand on its own. How is the overall population between fragmented and elongated cells is affected after Tg application?

To clarify our methodology for blinded classification of mitochondrial network morphologies we included the following text:

“We categorized cells for mitochondrial network morphology by blinded manual classification in which five researchers were given fluorescence microscopy images of exemplar network morphologies (elongated and fragmented) as references to assign morphologies to the experimental fluorescence micrographs.”

We targeted similar ratios of elongated and fragmented cells in both vehicle and Tg treated conditions for tomography, but qualitatively saw the expected increase in the elongated population to what has been previously described during Tg treatment. Because of our single cell targeting approach we did not quantify the population shift.”

Similarly, what is meant by manual classification of IMM, OMM and ER? Is there any clustering involved?

Our automated segmentation approach labels all membranes, and the separation of the IMM, OMM, and ER membranes is done by an expert user selecting and relabeling each membrane based on cellular context (e.g. IMM is inside of OMM and contains cristae). We have added the following text to clarify our methodology for manual classification of IMM, OMM, and ER:

“This was followed by manual labeling of membranes into mitochondrial IMM and OMM and ER membrane based on cellular context, as well as manual cleanup of individual membrane segmentations using AMIRA software (Thermo Fisher Scientific).”

Reviewer #2, minor comments:

What is meant by growth plane? This term is not defined in the manuscript.

We clarified and further defined the “cell’s growth plane” in the text by adding the following phrase:

“… the cell’s growth plane (the plane of electron microscopy grid substrate on which the cell is grown) (Figure 6A).”

What is meant by vehicle treatment? There is no explanation in the main text of the manuscript.

We clarified and further defined vehicle treatment in the main text by adding the following:

“We applied our correlative approach to identify and target specific Tg-treated and vehicle (media with DMSO) treated MEFmtGFP cells with either elongated or fragmented mitochondrial network morphologies for cryo-FIB milling and cryo-ET data acquisition and reconstruction.”

Have the authors noticed/calculated any differences in the width of the cristae?

We measure this difference in figure 4C (Intra-crista distance). We found significant changes in width/intra-crista distance in response to Tg treatment in both elongated and fragmented morphologies.

Methods: Automated surface reconstruction: "In cases where the resulting surface was very complex, the surface was simplified..." How was the complexity determined?

With the updated state of the software, we simplify all surfaces to generate a maximum of 150,000 triangles. This has minimal effect on very small surfaces, but greatly speeds computation on very large surfaces. We corrected the language to match this:

“The resulting mesh was simplified with quadric edge collapse decimation to produce a surface that represented the membrane with 150,000 triangles or fewer.”

Methods: Calculation of distances between individual surfaces: "For surfaces with small numbers of triangles, this was accomplished using a distance matrix...". What is the threshold for a small number of triangles?

As part of our software overhaul we have changed to always using a more memory-efficient KD tree based quantification, since the additional speed for the distance matrix approach is minimal when there are few enough triangles for it to be appropriate, and the hardwired cutoff was not as flexible for different hardware configurations. The updated text is below, but to satisfy any potential reviewer curiosity, the decision was made when the required distance matrix would use more than 128GB of memory. In the case of two identically sized surfaces, this crossover happens when there are approximately 45,000 triangles in each surface.

“For calculations of distances between respective surface meshes, the minimum distance from each triangle on one surface to the nearest triangle on the other surface was calculated using a KD-tree.”

Reviewer #2 (Significance (Required)):

The aim of the paper is well motivated. Cryo-ET is a growth field and there is a need for quantitative parameterization of cryo-ET data. Recently a toolkit for the analysis of filaments from cryo-ET has been published (Dimchev et al. 2021 DOI: 10.1016/j.jsb.2021.107808). Given the specific nature of the implementation, i.e. the membrane structures of mitochondria, I cannot easily see that this implementation will be useful beyond the analysis of mitochondrial membrane structure.

We hope that we have addressed this concern with generality has been addressed by our previously described updates to the software implementation.

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

Review 2, minor comments:

Angle between OMM and cristae: Maybe use the average angle of each cristae for comparison or fit a plane for each cristae because you are interested in the angle between the cristae and the OMM and the membrane of the cristae has a lot of uneven surfaces

We believe that the advantage of our approach is the ability to incorporate more complex geometric information from uneven surfaces such as those seen in cristae. With that said, the ability to quantify metrics for individual cristae in an automated manner would be very appealing, since in many ways cristae are functionally independent compartments. Accomplishing this would require either subdividing the larger surface into individual cristae, which will require development of additional sub-graph processing strategies. Additionally, pairing surfaces to represent opposite sides of a crista will require additional development. While we agree that this will be an excellent extension of the surface morphometrics approach, we feel that the additional development required is out of the scope of this initial manuscript focused on the general workflow. New methods leveraging sub-graph analysis will be explored in future manuscripts.

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Referee #2

Evidence, reproducibility and clarity

Barad, Medina et al. presents a new toolkit for the analysis of membrane ultrastructure in cryo-tomograms. More specifically, the toolkit is designed to compare curvature, angles and spacing between different membrane types in mitochondria. These analyses allow for the quantitative comparison of membrane features e.g. for different growth conditions. To demonstrate the utility of the toolkit tomogram datasets of mitochondria in the presence and absence of ER stress were analyzed. The authors conclude that ER stress affects mitochondria morphology through remodeling of the membrane structure. The presented biological results and statistics are convincing and show active mitochondrial membrane remodeling in the cell when exposed to ER stress. It is also clear that there is a need for more quantitative evaluation based on the wealth of tomographic image features and mitochondrial membranes are certainly a well-chosen application. For this purpose, the authors developed a new workflow even though most of the discussed analyses are very specific to mitochondrial structures. Therefore, broader applications of these tools to other organelles are not easily envisaged without significant adaption. In that context, the title and abstract overpromise a much more powerful utility that can be applied to any other membrane analysis. Rather it seems that the proposed workflow is more of a specific tool or a pipeline for mitochondrial inner and outer membrane analysis instead of a toolkit for general morphological analysis. Hence, the manuscript cannot be accepted in its current form. In particular, the structure needs a significant rework of editing to become more comprehensible.

Major comments:

1. Title and abstract need to be toned down not to overpromise a very general toolkit. The presented method may be a tool or a collection of scripts - a toolkit can be used to address other types of (membrane) analysis problems. In the end, the analysis builds to a large extent on the previous developments and implementation of PyCurve. Perhaps, the most interesting contribution here is the application of the mesh generation by the Poisson reconstruction method to the segmented membranes, which is, however, well implemented in the used pymeshlab framework. The computation of distances and angles is straightforward.
2. When reading the manuscript, the reader is left in the open whether this is a method paper or a biological results paper. The title/abstract suggests that this is a method paper and the manuscript is more of a mitochondrial membrane report in ER stress. Therefore, the title/abstract does not reflect the manuscript very well.
3. The manuscript also requires substantial structural editing. Several references to Figures are not appearing in the text in the order that the Figure panels are built. Excessive cross-referencing of figures also make the manuscript hard to read.
4. The focussing to a method paper will also require more in-depth descriptions of the methodology in the main text. Although the code is deposited at github, there is no script-based workflow and description presented in the manuscript. Although Figure 1 puts the work into context of tomography, it remains very superficial on the image analysis. What are the input and output formats required for each step to follow the sequence of the workflow and at which steps critical interactive input is needed? What are the hardware requirements (CPU, GPU) or performance characteristics (CPU hours for certain operations)?
5. Figures 3-7 contain colorful 3D renderings of the measured quantities. In addition, they are filled with histograms of every possible quantitative parameter, which often are not very significant or different between. The authors should focus the main results and the figures to show the most relevant and significant findings and put the remaining panels and results into the supplement.
6. The exact morphological discrimination between fragmented and elongated mitochondria is not easily understood from the results section. What is really meant by blinded manual classification? It only became clear when reading the methods. The results section should stand on its own. How is the overall population between fragmented and elongated cells is affected after Tg application?
7. Similarly, what is meant by manual classification of IMM, OMM and ER? Is there any clustering involved?
8. One of the key steps is the generation of a smooth surface from a segmented membrane, there is a question whether true membrane disruptions will be smoothed and may be overlooked in this approach. When these disruptions present true membrane ruptures, they may be of particular biological importance. The authors should support the choice and selection of the smoothing parameters in order to illustrate this potential pitfall.
9. Throughout the manuscript, the authors mention statistical significance several times and one of the main aims of the study is perform statistical hypothesis testing. It is important to specify the significance test (not only in the methods) and the p-value in order to support this claim. In the manuscript, the authors use exclusively the Mann-Whitney test. What is the rationale for choosing this test? Have the authors considered comparing the total distributions and not just the peaks with e.g. a Kolmogorov-Smirnov test? For a statistical methods paper, there are also no discussion on error analysis.

Minor comments:

1. https://github.com/grotjahnlab/surface_morphometrics should include an example data set or tutorial for dissemination.
2. What is meant by growth plane? This term is not defined in the manuscript.
3. What is meant by vehicle treatment? There is no explanation in the main text of the manuscript.
4. Angle between OMM and cristae: Maybe use the average angle of each cristae for comparison or fit a plane for each cristae because you are interested in the angle between the cristae and the OMM and the membrane of the cristae has a lot of uneven surfaces
5. Have the authors noticed/calculated any differences in the width of the cristae?
6. Methods: Automated surface reconstruction: "In cases where the resulting surface was very complex, the surface was simplified..." How was the complexity determined?
7. Methods: Calculation of distances between individual surfaces: "For surfaces with small numbers of triangles, this was accomplished using a distance matrix...". What is the threshold for a small number of triangles?

Significance

The aim of the paper is well motivated. Cryo-ET is a growth field and there is a need for quantitative parameterization of cryo-ET data. Recently a toolkit for the analysis of filaments from cryo-ET has been published (Dimchev et al. 2021 DOI: 10.1016/j.jsb.2021.107808). Given the specific nature of the implementation, i.e. the membrane structures of mitochondria, I cannot easily see that this implementation will be useful beyond the analysis of mitochondrial membrane structure.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Barad and Medina, along with their co-authors, report on the development of a new software toolkit to quantitatively assess membrane structures that are observed in cryo-ET. This new toolkit builds upon existing methodologies by successfully incorporating additional methods and applying this to cryo-ET data to allow for more automated and reliable segmentations. This work addresses a long-standing difficulty in generating membrane segmentations, which are either done manually with huge labor investments or with automated methods that are known to be error prone. The authors demonstrate that their toolkit can generate high quality segmentations across multiple tomograms with limited manual intervention. They use correlative light and electron microscopy in combination with these segmentations to gain insight into the ultrastructural morphology of mitochondria within embryonic fibroblasts, both under control conditions and under endoplasmic reticulum stress induced by treatment with the drug Thapsigarin. Unlike changes to the ER which are more dramatic under stressed conditions, the changes to the mitochondria are more subtle and impossible to quantify without high quality segmentations. The authors show that inner and outer membrane distances change under stress, and that the distances between cristae, their junctions, and the angle of the cristae with respect to the margin of the mitochondria change. While they characterize the curvedness under the same set of conditions, they report no significant differences.

Major comments:

• A major concern is that the data are reported and analyzed on a per tomogram basis when many tomograms contain multiple mitochondria. Given that the mitochondria appear mostly well separated in Sup. Fig 1 with only a few connections visible, and the high degree of pleomorphism noted by the authors, I would strongly suggest that the authors use each mitochondrion as the basis for reporting their metrics rather than the FOV/tomogram as this would avoid mixing metrics from different mitochondria that may be in different states (e.g., fusion/fission). This would apply to data shown in Figures 3, 4, 5, and 6.
• In Figure 3C the authors show the combined distribution of OMM-IMM distances within each condition. This may obscure some variability within populations. Individual histograms for all mitochondria should be included as supplementary material. Currently, it is difficult to judge if the peak of the combined distribution is appropriate and impossible to judge the variability between tomograms (preferably mitochondria, see above comment). Additionally, the shape of the distributions appears significantly different between conditions, suggesting that selecting a single peak value as representative and the basis for the statistical tests (Fig 3D) might not be appropriate. Please comment.
• In Figure 4C-F, again combined distributions are shown. Authors should include individual histograms for all mitochondria as supplementary material. The diversity of distributions in the metrics are more pronounced than the distances in reported in Fig 3, again making assessment of variability difficult and raising doubt about using the single peak value.
• It would be helpful to include the curvature or curvedness of the OMM for each mitochondrion in the supplementary material. The data to correlate OMM curvature with elongated/fragmented mitochondria should be available and might be of interest to some readers.
• As the work reported here is heavily computational, additional details about the computer hardware used and the time it took for the calculations to complete would be helpful for readers considering applying the code to their own data.
• Discussion should be expanded to include a comparison of semi-automated segmentations generated here versus manual results from Navarro (Ref 35) & Burt (Ref 54 / doi: 10.1371/journal.pbio.3001319) and how one might estimate the error.

Minor comments:

• In the fourth sentence of the third paragraph of the introduction, Hoppe 1992 is cited as evidence of the limitations of work published in 2020, which is confusing. Perhaps the sentence can be re-phrased?
• Pink and purple very close, consider alternative pair of colors or different shades to distinguish OMM and IMM
• For all data, exact n per condition should be given (in text and captions as appropriate), not a range for the whole set.
• Orientation of scaleboxes/scalebars should be consistent per figure panel. If knowledge of the axes is important to the reader, these should be included as well.
• In the last sentence of the introduction, the term "organellar architectures" is used, instead of the previously defined "membrane ultrastructure." Consider changing for clarity.
• Inconsistent use of the phrase "cryo-electron tomography" after defining and using "cryo-ET"
• Authors argue that the distinction between curvedness and curvature is important and that curvature is less appropriate in this context, but then use curvature in the abstract, throughout introduction and in the results section. Usage can be improved for readability.
• In section "Development of a framework to automate quantification of ultrastructural features of cellular membranes" the second last sentence should read "... higher quality membrane surfaces as compared..."
• In section "IMM curvedness is differentially sensitive to Tg treatment in elongated and fragmented mitochondrial networks" the fourth sentence should perhaps read "... despite apparent visual differences, no significant..."
• The term "cell's growth plane" is not clear from the text nor from Fig 6A. Do the authors mean surface of the substrate the cell is growing on?
• In Materials and Methods:
  • The authors report that manual back-blotting was used in a Vitrobot. This is non-standard usage and more details should be provided.
  • The description of the Leica microscope is insufficient. The objective lens and camera used should be included.
  • In section "Fluorescence Guided Milling" in the third sentence, the word "based" is repeated, second can be removed. A second Pt coat on top of the GIS would also be unusual, please check writing for accuracy.
  • Symbol for degree (or the word degree) should be added to angular increment and tilt range for clarity.
  • Capitalization of TomoSegMemTV is inconsistent.
• Fig 1B: showing computational steps twice does not provide additional information. Consider just one example. Also, labels for elongated and fragmented would be more useful than the duplicated labels for each computational step.
• Fig 2A caption - should report actual thickness range measured (as given in Materials and Methods section) instead of estimated range.
• Fig 3 title - consider replacing "Inter-mitochondrial membrane..." with "Intra-mitochondrial membrane..." for clarity.
• Fig 3C caption - should explicitly state it is a combined histogram and that the dashed lines correspond to the peak of the pooled data.
• Fig 5E middle, legend obscures some of the data.
• Fig 6B and 6C caption - upper and lower parts not explicitly described.

Significance

This work primarily describes a technical advancement in methods to analyze cryo-ET data. The novelty arises from the combination of methods and their application rather than completely new ideas or approaches. Demonstrations of the utility of this toolkit based on the authors' analyses are convincing and will likely help a number of researchers in the field who are engaged in explorations of cellular ultrastructure and organelle responses to stimuli. Importantly, this work will help the field move past qualitative descriptions, historically accepted only because quantitative measurements at this level have not been feasible. Overall, in this reviewer's opinion, while the biological findings are modest, the utility of the toolkit for the field is indisputable and the work is of sufficient quality for publication.

My expertise is in cryo-EM, both single particle analysis and tomography, as well as CLEM workflows, applied mostly to cytoskeletal research and some ER stress. I do not have or strong background in mitochondrial biology nor sufficient computer science expertise to evaluate the numerical methods employed, but based on inspection of the github contents, the screened Poisson reconstruction algorithm is not reimplemented here.

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