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Referee #1

Evidence, reproducibility and clarity

This manuscript by de Groot et al. is focused on investigating the role of the DNA damage tolerance (DDT) pathway for maintaining genomic stability in mammalian cells. All experiments are well designed and executed, and the conclusions are strongly supported by the experimental data. The authors generate a pair of congenic T cell lymphoma cell lines with either WT or PcnaK164R/-Rev1-/- genotype (the latter are referred to as double-mutant [DM] cells throughout the proposal). The DDT-deficient DM cells are surprisingly normal under standard growth conditions but show a strongly increased sensitivity to DNA damaging agents. Thus the authors conclude that in the absence of exogenous stress a backup pathway exists to allow for normal growth, and a CRISPR screen reveals the CDC13/CTC1, STN1, and TEN1 (CST) complex as central for cell survival and cell cycle progression. Subsequent DNA fiber assays reveal that this survival relies on increased repriming of replication, and that exogenous stress overwhelms this backup pathway. Finally, the consequences of DDT deficiency were tested by whole genome sequencing of the WT and DM cells were exposed after a single round of UV stress. and subsequent whole genome sequencing was used to identify DNA alterations. The absence of DDT led to a striking increase in the number of deletions ranging in size from 0.4 to 4.0 kbp (called to a type 3 deletions). Importantly, such mutations are also present in many human tumor genomes and their level appears to be linked to alterations in DNA repair pathways (but no clear causal relationship was shown). The main take home message is that repriming after the lesion is the last resort when a replication forks stalls at a DNA lesion as this leads to the loss of 400-4000 bp of genome information at every such event. The DDT pathway serves to channel the responses towards less deleterious (or even error-free) replication outcomes.

Major points:

1. The authors rely on a genetically modifed cell line in which the Pcna and Rev1 genes are altered (the latter by CRISPR/Cas9 technology). To rule out that any additional inadvertent genetic changes occurred that may influence the phenotypes see here, it would be important to show for at least a subset of the experiments that ectopic re-expression of Rev1 and WT PCNA can rescue the survival defects seen here.
2. It is unclear whether all experiments were conducted with a single clone of each genotype or if different clones were tested. This should be clarified.
3. The increase in the type 3 deletions in human cancers is very obvious, and as the authors clearly demonstrate DDT-deficiency results in the very same type 3 deletions. Although there is no data for this shown here, I'm assuming that a single deficiency in Rev1 would show a distinctly different mutation pattern. Given alterations of DNA repair/DNA damage tolerance gene mutations in the human tumors, it appears very unlikely to me that all tumors lack the DDT in its entirety. So why would the type 3 deletions then emerge? The authors should provide a clearer model of how this might work that could be tested in the future.
4. The authors only assess the genome alterations after a single dose of UV irradiation. Do the type 3 deletions also accumulate (albeit at a much lower rate) when these cells are grown for an extended period of time under normal conditions and do such cultures ultimately undergo senescence once too many deletions have been acquired?

Minor points:

1. In the methods section the description of how the cell lines that are central to this work were generated is not clear. The authors start with a p53-/-PcnaK164R/loxP Rev1wt/wt background. Then the Rev1 was inactivated using CRISPR technology, but how the Pcnawt/- genotype in the WT was restored is unclear. It would be helpful to provide a schematic drawing of the gene targeting strategies as a supplementary figure.
2. The authors should describe whether (and how many) independent clones of the DM (and may be WT) cell lines were tested and used in the experiments.
3. The approach by which the genome-wide mutation load was assessed for each genotype is not described in sufficient detail. Did the authors compare WT before and after UV exposure and DM before and after UV exposure separately or were just the genomes of WT and DM after UV exposure compared.

Referees cross-commenting

It appears that our comments are mostly overlapping.

Significance

This manuscript is a continuation of the very systematic work by the Jacobs lab to dissect the molecular mechanisms by which DDT factors act and the role of DDT in DNA damage responses. Here the authors demonstrate that in complete absence of DDT factors is not lethal, but reveals the priming of replication as the last resort response to avoid cell death. The analyses of the human tumor genome sequences suggest that dysfunctional DDT response are likely intimately involved in the generation of a distinct set of genetic lesions found in many tumors. What remains unclear is how the DDT pathway is inactivated in tumors as there is no consistent pattern of DDT factors being mutated. Overall this manuscript is of broad general interest far beyond the DNA repair community. The novelty of this manuscript is how reduced by the fact that another group published similar data in the human RPE cells 2023 (see reference 79 as acknowledged by the authors), but observing the same phenomena in two distinct system provides additional weight to these discoveries.<br /> Expertise: My expertise is in the gene diversification processes that assemble and alter TCR and immunoglobulin genes. They involve a broad range of DNA repair factors and DDT plays a unique role in somatic hypermutation that allows for the generation of high affinity antibodies.

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Reply to the reviewers

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

Summary: In this work, Kant and co-workers describe a two drugs regimen for therapeutics treatment of SARS-CoV-2 infection. SARS-CoV-2 infection of cells is dependent on the cleavage of the spike S protein by cellular proteases that prime S allowing the envelop protein to fuse of host membrane during entry and delivery of the viral genome to the target cell. The most important cellular protease is TMPRSS2 located at the surface of the cell. However, in cells with low TMPRSS2 levels, Cathepsins, located in endosomes have been shown to be able to also prime S. The therapeutic strategy of the authors relies on the combined usage of an inhibitor of TMPRSS2 (nafamostat) together with a compound that impairs endosomal maturation (apilimod) which is a key step for the activation of cathepsin. The rationale is that a dual regimen would be more effective to inhibit SARS-COV-2 infection. Using cell lines and a combination of SARS-CoV2 infection and pseudotyped VSV particles (VSV virus where the glycoprotein has been replaced by the SARS-CoV-2 spike proteins), the authors could show that a two-drug regimen was more efficient in preventing SARS-CoV-2 infection compared to single drug regimen. The authors next employed a mouse model of SARS-CoV-2 infection and similarly could show that bi-therapy was more efficient in preventing infection. Importantly, the authors describe a new formulation of the drugs that improve stability of the compounds and shelve life which could be of great benefit with respect to storage needs in therapeutic setting of the population.

While the reviewer thinks the work is potentially very relevant, some of the conclusions are not fully supported by the data and additional experiments/quantifications should be performed to improve rigor and fully support the author conclusions.

Major comments:

• Throughout the paper, statistical analysis of the results should be performed to support the conclusion of the authors. Currently many experiments do not have statistical analysis and P values or statical significance are missing in most of the figures: Figure 1B, 1D, 4A, 5B, and S2. RESPONSE: As requested by the reviewer, the results of the statistical analysis of the differences are now reported for Figures 1B, 1D, 4A, 5B, and S2. There is no change in our conclusions as first reported in the original manuscript.

• Quantification of the various pathology observed in mice should be quantified and scored. In the current version, the authors provided a supplementary table describing the pathology observed in individual mice upon SARS-CoV-2 infection. Adapted scoring of the different pathologies should be performed to obtain a statistical view of the pathology induced by SARS-CoV-2 and how this is prevented by the mono and bi-therapy approaches. RESPONSE: The mouse model employed in the present study, i.e. SARS-CoV-2 Beta infection in BALB/c mice, is characterised by a limited and short-lived viral infection of the lungs and rather subtle pathological changes, as described in detail in our previous publication (Kant et al., 2021. Viruses).

We chose this model because it better mimics the typical (short-lived) respiratory infection observed in human patients than the K18-hACE2 model where infection is detected in nasal mucosa and lung parenchyma, generally sparing the respiratory epithelium, but also spreads to the brain (Seehusen et al., Viruses, 2022; De Neck et al., Viruses, 2023).

In our model, infection of the lungs (i.e., alveoli) occurs strictly in association with infection of the airways, including the tracheal, bronchial, and bronchiolar epithelium, like the in hamster model. Pulmonary infection is, however, short-lived and wanes off around day 4. The histopathological changes, i.e. degenerative changes, and an inflammatory response, are at best mild in the untreated mice and not observed at all in successfully treated mice. (as summarized for each individual animal in Supplementary Table 2). . For these reasons, this information cannot be quantified by morphometry (which would be the most objective, hence best approach) or scored (a more subjective approach that would only be valid with distinct quantitative differences).

Nevertheless, and in agreement with the reviewer that a quantitative approach is useful where possible we provide results from morphometry and to confirm the reduction in the degree of tissue damage (i.e., the extent of apoptotic death of infected respiratory epithelial cells; see comment below).

• Additionally, table 1, is very difficult to read as mice are classified in 3 experiments but this does not match with the individual figures, making it very hard to look for the phenotypes. Is it an order issue within the table or are murine infection experiments performed in the order described in table 1? In this case, can the data be compared between the experiments as some conditions belong to experiment 2 and other to experiment 3? Given the low number of mice, do the experiments have statistical power? RESPONSE: We agree with the reviewer’s assessment of the figure and have therefore modified the graphs in Figure 2 B, to specifically relate experiments and data, by using circles for Experiment set 1 and squares for Experiment set 2.

We can confirm the reported results have statistical power, particularly important given the constrain due to the low number of animals we were limited to use. As noted in the figure legends, that now includes the results from the statistical analysis, each of the three experiments included at least three control infected mice treated with vehicle. The infection levels in all the control vehicle treated infected mice are very similar in all three experiments.

• To show that treatment of mice at 3 or 6 hpi indeed reduce the number of clv-capsase3 positive cells, the authors should perform a complete quantification and not limit their analysis to one representative tissue section from one animal. RESPONSE: Following the reviewer’s recommendation, we have now taken a quantitative approach in addition to illustrating the difference in cleaved caspase-3 expression. We have kept the images that illustrate the effect in tissue sections (Figure 4C).

Briefly, we compared the extent of viral NP and cleaved caspase-3 expression between lungs of vehicle treated mice and mice treated with the drugs from 6 hpi onwards (3 mice per condition), using morphometry. Indeed, there was no significant difference in the extent of viral antigen NP expression in the lungs of the two groups of mice (Figure 4 B and C), which supports the PCR results representing viral RNA levels (Fig. Figure 4 A). However, there was a significant difference in the extent of cleaved caspase-3 expression in the consecutive sections. The results are shown in the new Figure 4D.

• the authors insist on the new formulation that improves drug stability. To make this statement, this will need to be actively tested both in cell culture and in animal models: currently, the authors test the drugs stored 3 months at 25c or -20c and show that they remain active, but in this experiment freshly made drug was not directly tested in parallel. RESPONSE: As requested by the reviewer, we have extended our tests, and confirm our original view that the new formulation improves drug stability. Now shown in revised Figure 1C and D, we found equivalent inhibition in the cell infection assay using freshly made drugs and drugs stored at room temperature for 2 months.

• Additionally, to make such a statement, different concentration of the drugs should be tested to calculate a IC50 for freshly prepared drug and stored drugs (as the current concentration tested might be at saturating concentration). RESPONSE: As requested by the reviewer, we have determined the IC50 for infection in cells of the drugs freshly prepared or stored. As reported in the revised Figure 1D, there were no differences detected.

• Finally, the mouse experiments are performed with freshly made compounds and if the authors want to highlight the new formulation and increased stability, experiments in mice should be performed also with stored compounds. RESPONSE: We respectfully disagree with the reviewer on the need to perform additional in vivo experiments. We find no differences in the IC50 antiviral activity of the drugs prepared with our formulation and tested with cells in culture, whether fresh or kept for up to 2 months at room temperature. Given these observations, we feel that we cannot justify further animal experiments, neither ethically nor financially, using the same drugs with the same ab initio antiviral activity.

• Alternatively, statement on drug stability should be removed or strongly tuned down from text. RESPONSE: We believe that the updated information included in the revised manuscript showing no difference in the IC50s of the compounds freshly prepared and stored at room temperature fully supports our original statement.

• Statistical analysis on figure 2b should be done between Nafamostat alone and dual treatment to show that both drugs are cooperative in term of antiviral activities RESPONSE: We have carried the requested statistical analysis (Figure 2 B and C) and confirm that dual treatment is not only cooperative, but it also shows synergy, as we originally showed in our published work (Kreutzberger et al., Journal of Virology, 2021).

• The authors state "A quantitative assessment of the in vivo synergy is shown here by the enhanced decrease of viral RNA in lungs of mice treated with both drugs at very low concentrations (Figure 2 B, compare using 2 mg/Kg apilimod dimesylate and 4 mg/Kg nafamostat mesylate alone, and in combination)." I guess, the authors want to comment on the fact that 0.2 mg/kg of apilimod and 0.4 mg/kg of nafamostat are as potent as 2 and 4 mg/kg. is that correct? If YES, to make this statement, bi therapy should be compared to mono therapy at the same concentration. RESPONSE: We apologise for not being clearer in the way we presented the information in our original version of the manuscript.

Briefly, we compared the effect of high and low bi-therapy doses to the effect of Apilimod or Nafamostat used as single drugs at the highest concentrations. When administered alone, high dose Apilimod did not reduce infection. Nafamostat alone, even at 4 mg/Kg, decreases but does not completely block infection. When combined, even at low doses, the two drugs have a stronger antiviral effect than Nafamostat alone (and of course Apilimod, which was ineffective). Importantly, if the combined effect of the two drugs was merely additive, i.e. the arithmetic sum of the single effects, the addition of Apilimod, which alone has no in vivo antiviral activity, would not have improved the effect of Nafamostat. Instead, even at 10 times lower doses, the bi therapy significantly outperformed the single drug Nafamostat. Thus, the effect is synergistic (i.e. the effect of combined drugs is stronger than the mere sum of effects of each single drug).

• when drugs are injected after infection (Fig 4), the drugs are not active. In fact, unless the reviewer mis-understood the plot, the mouse are even more infected compared to vehicle. The authors wrote that both regimes (3 and 6hpi) are equally less effective compared to drug administered during infection. The authors should write that both regimes are equally non protective. RESPONSE: We thank the reviewer for pointing out this imprecision. The modified text now reads “Both regimes, compared to drug administration at the time of virus inoculation, were equally ineffective in reducing the viral RNA load and NP expression in lungs as determined at 48 h.p.i. (Figure 4A, B).” (Line 236-238).

• If drugs are not active after infection, does this approach really represent a therapeutic solution. The authors suggest that it does by limiting pathologies, but this needs to be better quantified (see comment above). RESPONSE: Our results suggest that application of the drugs post infection reduced the cytopathic effect of the virus in the respiratory epithelium in the lungs, reflected by a reduced extent of apoptotic cell death in association with infection. The finding is supported by quantitative morphometric analysis as shown in the new Figure 4D (see also comment above).

• In the rebound experiment: unless the reviewer misunderstood, it appears that no conclusion can be driven from this experiment. Q-PCR data for vehicle animal a 4dpi show no sign of infection, so the experiment is not really interpretable since control animals are no longer positive. The authors suggest that there is less pathologies but this needs to be better quantified (see comment above). RESPONSE: We have tried to better word the rationale and interpretations of this experiment in the text. Following our drug treatments, viral antigen is still present in epithelial cells within the nasal mucosa, we also surmised that a small number of intact virions could have remained attached to the epithelial cells, trapped within their endosomes, or still within the environment surrounding the cells, any of them capable of triggering infection after removal of the drugs. Thus, the rationale behind the rebound experiment was to ask whether such remaining potentially intact virions could lead to a full reinfection of the lung two days after the treatment was stopped - which we found did not.

We found that the virus did not regain full infectivity once the drug treatment was interrupted, resulting in undetectable lung PCR signal and very limited, sporadic antigen signal in the lung tissue.

Minor comments:

• I__t will make reading easier if the authors always mentioned which drugs inhibit what. For example: addition of the TMPRSS2 inhibitor nafamostat etc.... or addition of apilimod to block cathepsins activities..... __RESPONSE: Done

• Figure 1: make a comment in the text that cells with low TMPRSS2 are more sensitive to the cathepsin inhibitor apilimod and vice versa, cells with high TMPRSS2 are more sensitive to nafamostat. This is expected and it could be highlighted. RESPONSE: Done

• Figure 2B: how are the data normalized? should not RdRp, E and SubE all have a mean at 100% for the vehicle? RESPONSE: Done. Data are now normalized to the mean of RdRp measurements (which is indicated as 100%).

• Line 211: something is missing here "when (Fig 2...) RESPONSE: Corrected

• Line 221 should figure 4c RESPONSE: Corrected

• Figure legends should only contain the details of the experimental design but should not contain description and interpretation of data. This is very minor and maybe a question of taste. __RESPONSE: __ Our figure legends are descriptive for some results and are in accordance with the style of PLOS Pathogens, the journal we are aiming this study.

Editorial note:

Referees cross-commenting: The other reviewers have highlighted the same limitations concerning the lack of quantifications of the immunochemistry and also the lack of robust statistical analyses. This should be highlighted to the authors as it appears to be the minimum to do prior publication. This should not take too much time as the data are in principle already available

Reviewer #1 (Significance):

The work by Kant and co-workers is potentially very significant but some limitations (as highlighted above) impair the impact of the work in his current version. The approach employing a two-drug regimen to combat SARS-COV-2 infection by targeting both TMPRSS2 and cathepsin activities is not new and was described before by the authors themselves. Employing this approach in an animal model is new and the new formulation improving drug stability and facilitating storage could be a game changer in therapeutic setting of patients. As such, this work could be highly significant and of broad interest. However, additional experiments and clarifications are needs to elevate this work to high impact standards. The reviewer believes that the requested experiments are easily achievable by the research teams of this project and think that the project will ultimately have a strong impact in the field.

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Reviewer #2 (Evidence, reproducibility and clarity):

In this paper, the authors tested the antiviral activity of a combination of compounds by intranasal instillation in a mouse model of SARS-CoV-2. The two compounds used are PIKfyve Kinase inhibitor apilimod dimesylate, which inhibits endosomal maturation, and TMPRSS2 protease inhibitor nafamostat mesylate. The authors have previously shown that a combination of these two inhibitors acts synergistically to prevent entry and infection of SARS-CoV-2 in cell culture. Here, they further investigated the anti-SARS-CoV-2 activity of their combination of compounds by in vivo testing. They used Balb/c mice intranasally inoculated with the Beta variant of SARS-CoV-2. Their data show that concurrent administration of the combo together with the virus prevented lung infection without blocking nasal replication. Delayed administration of the compounds did not reduce replication in the lungs. The only effect was a decrease in bronchiolar cell death. Furthermore, they also tested the stability of the combo at room temperature and their data indicate that these compounds can be kept at room temperature for at least 3 months without losing antiviral activity, at least when resuspended in water. These data are potentially interesting, but they need to be consolidated by additional experiments.

Major comments:

• The authors only present immunohistochemistry to investigate viral replication in the nose. A quantitative analysis of replication would allow for better conclusions concerning viral replication in this organ. RESPONSE: We appreciate the reviewer’s comment and the wish to see viral antigen expression quantified in the nasal mucosa. As described below, however, practicalities associated with sample preparation prevented us from performing morphometric analysis. The complementary quantification of viral replication requires viral RNA by PCR. Unfortunately, we had not planned this aspect of the study and therefore did not collect the required fresh samples from nasal turbinates required for this analysis. Although interesting to investigate, we feel this is not vital for reaching the interpretation and conclusions derived from the current study. We thereby don’t think that this would be sufficient reason to undertake another round of infections, particularly taking into consideration that it would require sacrificing another significant number of animals.

We could extend our morphometric analysis used in the lung and adapt it to the nasal mucosa. However, we are of the opinion that this would not provide trustworthy results. The main reason for this limitation is due to a problem that occurs during decalcification and paraffin embedding of the heads, which results in large variations in the area of the nasal mucosa as well as the olfactory epithelium in each section in different animals (Figure 3C provides some evidence of this).

Briefly, we cut the entire heads longitudinally in the midline with a diamond saw and then gently decalcify the two halves of the head. This is followed by paraffin embedding. At some point during the process some of the thin and soft bits of nasal mucosa can become twisted and distorted, moving away from the cut surface exposed to the microtome blade. Therefore, the paraffin sections (appr. 3 µm thick) will in their majority not comprise full sections of the nasal mucosa. An objective comparative quantification of the extent of NP expression in the nasal mucosa would require (nearly) the entire mucosa to be assessed.

• Complementary investigation on a potential anti-inflammatory effect of the drugs would also be welcome. Furthermore, it is surprising that the authors did not report potential weight changes. RESPONSE: Our mouse model, i.e. SARS-CoV-2 Beta infection in BALB/C mice, is characterised by the limited and short-lived viral infection of the lungs, rather subtle pathological changes and a limited inflammatory response strictly associated with the presence of viral antigens, as we previously described (Kant et al., 2021. Viruses). Hence, other animal models (for example the hamster model) would be more appropriate. Though potentially interesting, such investigations are beyond the current scope of our studies.

In our study, the animal weight did not change during infection, in agreement with our earlier published work with the same animal model (Kant et al., 2021. Viruses). These data is now included in this manuscript.

• It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission. RESPONSE: While it would be interesting to see whether the combined drugs also block viral transmission, such an experiment would require the use of a different animal model (possibly hamsters), an endeavour that is beyond the scope of our study. In our experience BALB/C mice infected with SARS-CoV-2 Beta variant do not transmit the virus. We have co-housed naïve BALB/C mice for 4 days with BALB/C mice intranasally challenged with 6 x 10^4 PFU SARS-CoV-2 Beta and have no evidence of virus transmission to the naïve mice (unpublished results). Similar results with C57BL/6 WT mice were obtained by Pan et al., Signal Transduction and Targeted Therapy, 2021).

Minor comments:

• The second paragraph of the introduction is not clear. It needs to be re-written. Furthermore, there is no evidence that Calu3 cells do not express cathepsins. RESPONSE: We have clarified this section of the introduction as follows:

“It has been shown previously that SARS-CoV-2 infection can be blocked by serine protease inhibitors such as nafamostat mesylate in cells that express high levels of TMPRSS2 but very low or undetectable levels of cathepsin B/L (e.g. Calu-3 cells)5-7. In cells that instead express cathepsins but not TMPRSS2 (e.g. VeroE6 or A549 cells), infection depends on the delivery of endocytosed viruses to endo/lysosomes, a process that can be efficiently inhibited by drugs that interfere with endosome maturation and acidification such as Bafilomycin A1, chloroquine or ammonium chloride”.

• Figure 4C: Is there any explanation for the lack of apoptosis? The authors should at least provide some hypotheses. Furthermore, this figure is quoted as Figure 4B in the text instead of Figure 4C. RESPONSE: For the revised manuscript, we have quantified the extent of apoptosis by a morphometric analysis of cleaved caspase-3 expression in the lung sections (now provided in new Figure 4C).

We presently do not have an explanation for the reduction in the cytopathic effect of the virus, particularly in respiratory epithelial cells. This is an area of research we plan to continue investigating in future. We have commented on this in the Discussion session of the revised manuscript (Line 301-307).

• Line 199: The authors claim that the effect of their combo is synergistic. However, this cannot be clearly concluded without appropriate additional experiments where they vary the concentration of the compounds. RESPONSE: The work we report here with mice is a follow up of our earlier work demonstrating the antiviral synergy of nafamostat and apilimod with cells in culture (Kreutzberger et al., Journal of virology, 2021). See comments to Reviewer 1.

• Line 211: The sentence is incomplete RESPONSE: Fixed.

• The lettering in the panels needs to be doublechecked. RESPONSE: Done.

Reviewer #2 (Significance):

__General assessment: __Finding new antiviral against SARS-CoV-2 remains a priority to fight against COVID-19. The validation of a combination of two molecules showing a partial antiviral activity in vivo is therefore of interest. However, this combo does not block viral replication in the nose and is inefficient when the treatment is added after infection, limiting the use of these molecules to prevent people in contact with COVID-19 patient of being infected. However, the authors should demonstrate that their molecules block viral transmission.

__ Advance:__ The number of antivirals used in the clinics to treat COVID-19 patients remains extremely limited. Increasing the number of drugs available is still sorely needed. Audience: This paper potentially of large interest since the general population has been well informed of and/or have experienced COVID-19. Therefore, it is of interest beyond the virology and infectiology fields.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary: In manuscript reference RC-2023-02113, the authors addressed the impact of inhibitors of cell host factors as therapeutics against SARS-CoV-2 infection. They tested the combined inhibition of the enzymatic activities of the endosomal PIKfyve phosphoinositide kinase and the serine protease TMPRSS2, known as essential to meditate viral entry pathways: Conclusion: They showed a reduction, as assessed in vitro experiment (cell line) and in lung infection in mice intranasally- infected with SARS-CoV-2 beta. Moreover, the reduced viral infection is, as expected, associated to lower cell damage.

Reviewer #3 (Significance (Required)):

Positive points:

• The topic is of interest.

• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing. Limitations:

• Such a robust level of infection in this model (female BALB/c mice) is surprising, owing that the ACE is not the appropriate homologue. RESPONSE: We respectfully disagree with this concern. The BALB/c strain employed in the current study can be infected by the natural Beta variant, with mutations in the viral spike that allow it to bind to the murine ACE2 receptor and hence can efficiently infect the mice, as we previously described (Kant et al., 2021. Viruses).

We chose the wt BalB/c model as it better mimics natural respiratory infection in human patients, while the transgene K18-hACE2 model also results in strong infection of the brain. As discussed above, while infection with the Beta variant is efficient, it is not associated with clinical signs, it has only limited pathological effects (mild tissue damage and very limited inflammatory response) and is naturally cleared after 4 days. The ancestral Wuhan strain of SARS-CoV-2 as well as most other variants, in contrast, are unable to bind murine ACE, hence would require the use of transgenic mouse models expressing the human ACE receptor.

• It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission. RESPONSE: We apologize for our oversight of not including the statistical analyses in the original version of the manuscript. As requested, it is now included. We are pleased to confirm that in all cases, the differences were statistically significant between presence and absence of combined drugs, and fully support our original conclusions.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In manuscript reference RC-2023-02113, the authors addressed the impact of inhibitors of cell host factors as therapeutics against SARS-CoVé infection. They tested the combined inhibition of the enzymatic activities of the endosomal PIKfyve phosphoinositide kinase and the serine protease TMPRSS2, known as essential to meditate viral entry pathways: Conclusion: They showed a reduction, as assessed in vitro experiment (cell line) and in lung infection in mice intranasally- infected with SARS-CoV-2 beta. Moreover, the reduced viral infection is, as expected, associated to level cell damage.

Positive points:

• The topic is of interest
• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing

Significance

Positive points:

• The topic is of interest
• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing

Limitation

• Such a robust levels of infection in this model (female BALB/c mice) is surprising, owing that the ACE is not the appropriate homologue.
• Statistical analysis are missing for most of the results

Should be improved to support the strong conclusions.

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Referee #2

Evidence, reproducibility and clarity

In this paper, the authors tested the antiviral activity of a combination of compounds by intranasal instillation in a mouse model of SARS-CoV-2. The two compounds used are PIKfyve Kinase inhibitor apilimod dimesylate, which inhibits endosomal maturation, and TMPRSS2 protease inhibitor nafamostat mesylate. The authors have previously shown that a combination of these two inhibitors acts synergistically to prevent entry and infection of SARS-CoV-2 in cell culture. Here, they further investigated the anti-SARS-CoV-2 activity of their combination of compounds by in vivo testing. They used Balb/c mice intranasally inoculated with the Beta variant of SARS-CoV-2. Their data show that concurrent administration of the combo together with the virus prevented lung infection without blocking nasal replication. Delayed administration of the compounds did not reduce replication in the lungs. The only effect was a decrease in bronchiolar cell death. Furthermore, they also tested the stability of the combo at room temperature and their data indicate that these compounds can be kept at room temperature for at least 3 months without losing antiviral activity, at least when resuspended in water. These data are potentially interesting but they need to be consolidated by additional experiments.

Major comments:

1. The authors only present immunohistochemistry to investigate viral replication in the nose. A quantitative analysis of replication would allow for better conclusions concerning viral replication in this organ.
2. Complementary investigation on a potential anti-inflammatory effect of the drugs would also be welcome. Furthermore, it is surprising that the authors did not report potential weight changes.
3. It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission.

Minor comments:

1. The second paragraph of the introduction is not clear. It needs to be re-written. Furthermore, there is no evidence that Calu3 cells do not express cathepsins.
2. Figure 4C: Is there any explanation for the lack of apoptosis? The authors should at least provide some hypotheses. Furthermore, this figure is quoted as Figure 4B in the text instead of Figure 4C.
3. Line 199: The authors claim that the effect of their combo is synergistic. However, this cannot be clearly concluded without appropriate additional experiments where they vary the concentration of the compounds.
4. Line 211: The sentence is incomplete
5. The lettering in the panels needs to be doublechecked.

Significance

General assessment:

Finding new antiviral against SARS-CoV-2 remains a priority to fight against COVID-19. The validation of a combination of two molecules showing a partial antiviral activity in vivo is therefore of interest. However, this combo does not block viral replication in the nose and is inefficient when the treatment is added after infection, limiting the use of these molecules to prevent people in contact with COVID-19 patient of being infected. However, the authors should demonstrate that their molecules block viral transmission.

Advance:

The number of antivirals used in the clinics to treat COVID-19 patients remains extremely limited. Increasing the number of drugs available is still sorely needed.

Audience:

This paper potentially of large interest since the general population has been well informed of and/or have experienced COVID-19. Therefore, it is of interest beyond the virology and infectiology fields.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this work, Kant and co-workers describe a two drugs regimen for therapeutics treatment of SARS-CoV-2 infection. SARS-CoV-2 infection of cells is dependent on the cleavage of the spike S protein by cellular proteases that prime S allowing the envelop protein to fuse of host membrane during entry and delivery of the viral genome to the target cell. The most important cellular protease is TMPRSS2 located at the surface of the cell. However, in cells with TMPRSS2 levels, Cathepsins, located in endosomes have been shown to be able to also prime S. The therapeutic strategy of the authors relies on the combined usage of an inhibitor of TMPRSS2 (nafamostat) together with a compound that impairs endosomal maturation (apilimod) which is a key step for the activation of cathepsin. The rational is that a dual regimen would be more effective to inhibit SARS-COV-2 infection. Using cell lines and a combination of SARS-CoV2 infection and pseudotyped VSV particles (VSV virus where the glycoprotein has been replaced by the SARS-CoV-2 spike proteins), the authors could show that a two drug regimen was more efficient in preventing SARS-CoV-2 infection compare to single drug regimen. The authors next employed a mouse model of SARS-CoV-2 infection and similarly could show that bi-therapy was more efficient in preventing infection. Importantly, the authors describe a new formulation of the drugs that improve stability of the compounds and shelve life which could be of great benefit with respect to storage needs in therapeutic setting of the population. While the reviewer think the work is potentially very relevant, some of the conclusions are not fully supported by the data and additional experiments/quantifications should be performed to improve rigor and fully support the author conclusions.

Major comments

• Throughout the paper, statistical analysis of the results should be performed to support the conclusion of the authors. Currently many experiments do not have statistical analysis and P values or statical significance are missing in most of the figures: Figure 1B, 1D, 4A, 5B,and S2.
• Quantification of the various pathology observed in mice should be quantified and scored. In the current version, the authors provided a supplementary table describing the pathology observed in individual mice upon SARS-CoV-2 infection. Adapted scoring of the different pathologies should be performed to obtain a statistical view of the pathology induced by SARS-CoV-2 and how this I prevented by the mono and bi-therapy approaches. Additionally, table 1, is very difficult to read as mice are classified in 3 experiments but this does not match with the individual figures, making it very hard to look for the phenotypes. Is it an order issue within the table or are murine infection experiments performed in the order described in table 1?. In this case, can the data be compared between the experiments as some conditions belong to experiment 2 and other to experiment 3? Given the low number of mice, do the experiments have statistical power? To show that treatment of mouse at 3 or 6hpi indeed reduce the number of capsase positive cells, the authors should perform a complete quantification and not limit there analysis to one representative tissue section from one animal
• the authors insist on the new formulation that improves drug stability. To make this statement, this will need to be actively tested both in cell culture and in animal models. Currently, the authors test the drugs stored 3 months at 25c or -20c and show that they remain active, but in this experiment freshly made drug was not directly tested in parallel. Additionally, to make such a statement, different concentration of the drugs should be tested to calculate a IC50 for freshly prepared drug and stored drugs (as the current concentration tested might be at saturating concentration). Finally, the mouse experiments are performed with freshly made compounds and if the authors want to highlight the new formulation and increased stability, experiments in mice should be performed also with stored compounds. Alternatively, statement on drug stability should be removed or strongly tuned down from text.
• Statistical analysis on figure 2b should be done between nafamostat alone and dual treatment to show that both drugs are cooperative in term of antiviral activities
• The authors state "A quantitative assessment of the in vivo synergy is shown here by the enhanced decrease of viral RNA in lungs of mice treated with both drugs at very low concentrations (Figure 2 B, compare using 2 mg/Kg apilimod dimesylate and 4 mg/Kg nafamostat mesylate alone, and in combination)." I guess, the authors want to comment on the fact that 0.2 mg/kg of apilimod and 0.4 mg/kg of nafamostat are as potent as 2 and 4 mg/kg. is that correct? If YES, to make this statement, bi-therapy should be compared to mono-therapy at the same concentration.
• when drugs are injected after infection (Fig 4), the drugs are not active. In fact, unless the reviewer mis-understood the plot, the mouse are even more infected compared to vehicle. The authors wrote that both regimes are equally less effective compared to drug administered during infection. The authors should write that both regimes are equally none protective. If drugs are not active after infection, does this approach really represent a therapeutic solution. The authors suggest that it does by limiting pathologies but this needs to be better quantified (see comment above)
• In the rebound experiment: unless the reviewer misunderstood, it appears that no conclusion can be driven from this experiment. Q-PCR data for vehicle animal a 4dpi show no sign of infection, so the experiment is not really interpretable since control animals are no longer positive. The authors suggest that there is less pathologies but this needs to be better quantified (see comment above)

Minor comments

• It will make reading easier if the authors always mentioned which drugs inhibit what. For example: addition of the TMPRSS2 inhibitor nafamostat etc.... or addition of apilimod to block cathepsins activities.....
• Figure 1: make a comment in the text that cells with low TMPRSS2 are more sensitive to the cathepsin inhibitor apilimod and vice versa, cells with high TMPRSS2 are more sensitive to nafamostat. This is expected and it could be highlighted.
• Figure 2B: how are the data normalized?. should not RdRp, E and SubE all have a mean at 100% for the vehicle?
• Line 211: something is missing here "when (Fig 2...)
• Line 221 should figure 4c
• Figure legends should only contain the details of the experimental design but should not contain description and interpretation of data. This is very minor and maybe a question of taste.

Referees cross-commenting

the other reviewers have highlighted the same limitations concerning the lack of quantifications of the immunochemistry and also the lack of robust statistical analyses.

this should be highlighted to the authors as it appears to be the minimum to do prior publication. this should not take too much time as the data are in principle already available

Significance

The work by Kant and co-workers is potentially very significant but some limitations (as highlighted above) impair the impact of the work in his current version. The approach employing a two-drug regimen to combat SARS-COV-2 infection by targeting both TMPRSS2 and cathepsin activities is not new and was described before by the authors themselves. Employing this approach in an animal model is new and the new formulation improving drug stability and facilitating storage could be a game changer in therapeutic setting of patients. As such, this work could be highly significant and of broad interest. However, additional experiments and clarifications are needs to elevate this work to high impact standards. The reviewer believes that the requested experiments are easily achievable by the research teams of this project and think that the project will ultimately have a strong impact in the field.

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Reply to the reviewers

Manuscript number: RC-2023-02224R

Corresponding author(s): Austin Smith

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.

We thank the reviewers for constructive comments and helpful suggestions which we have adopted to clarify and improve the manuscript. In addition, we have added a link to a web portal that will allow readers to visualise gene expression profiles and create their own plots using our early human embryo UMAP embedding (https://bioinformatics.crick.ac.uk/shiny/users/boeings/radley2024umap_app/). Stefan Boeing created this tool and is added to the author list with agreement of other authors.

2. Point-by-point description of the revisions

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

Summary In this manuscript, Arthur Radley and Austin Smith designed a new feature selection method for scRNA-Seq, which is a successor to ESFW previously proposed by the same authors. As an evolution of this earlier framework, cESFW is also based on the idea that informative genes share information with other genes, whereas non-informative genes have a more random relative expression. The authors emphasize the key importance of feature selection in the scRNA-Seq workflow and assess the current state of the art for this step. They also propose that better feature selection leads to less data transformation. They show that cESFW outperforms Scran and Seurat feature selection in most cases of synthetic datasets. cESFW is then used in the context of early human development, re-analysing data from several published datasets where they show that they do not require batch correction. They also further strengthen the conclusion that a "2-step" model for TE-ICM and EPI-Hyp differentiation is also present in human embyros. Finally, they map several types of in vitro pluripotent stem cells, in particular primed and naive, to their manifold and study the evolution of the gene signatures during early human development. Overall, the manuscript is well written and presents a solid methodology. The re-analysis of human early development is convincing and justified. The main critic is that the quality of figures can be greatly improved: their resolution is too low and they are hard to read. For instance, more contrasted color schemes could be used to improve clarity, and given the high number of clusters for some UMAPs, indicating the name of some cluster near their centroids should improve clarity.

We agree that the resolution of the figures should be improved. We had to compress the images to satisfy the size limit for uploaded documents to bioRxiv. Our final submission will be of higher quality (original figures are at 900dpi). With regards to colour schemes, this is a surprisingly difficult problem. We tried multiple colour palettes but could not achieve greater contrast. The suggestion to add key cluster names near to their centroids on the UMAPs is an excellent idea, which we have implemented.

Comments: Page 2 I think the criticism of PCA is unfair because it is not a true feature selection method, and it is mainly used for computational purposes. I believe that for most workflows, between 30 and 50 PCs are retained, which do not significantly change the results in the downstream analyses. The citation (Yeung and Ruzzo 2001) does not seem appropriate, as they examine cases where only a small number of PCs are retained, outside the context of scRNA-seq.

We agree that the criticism of PCA is insufficiently justified by the citation. We thank the reviewer for pointing this out and have removed the comment.

"Furthermore, HVG selection has been found to be biased toward selecting highly expressed genes over low expressed genes." Could the author justify or remove this statement, as the Seurat and Scran methods are specifically designed to consider average expression to determine HVG? The cited article (Yip, Sham, and Wang 2019) raises this issue for methods other than Seurat and scran.

The reviewer is correct that the provided citation highlights Seurat and Scran HVG selection as relatively insensitive to the average gene expression levels compared with other HVG selection methods. We again thank the reviewer and have deleted the comment.

More generally, we have shortened the introduction, focusing on cESFW as a new approach to feature selection rather than critiquing alternative methods.

Page 6 I might have missed it, but I do not understand the number of cells in the early human development dataset also shown in Figure S2B. The Petropoulos et al. dataset alone is larger than the sum of cells from different cell types. Is there some filtering step that is not described?

We have added text in the data availability section to clarify the cells used in our analysis:

“The pre-implantation raw counts scRNA-seq data from Yan et al. 2013, Petropoulos et al. 2016, Fogarty et al. 2017, and Meistermann et al. 2021, were compiled into a single gene expression matrix by Meistermann et al. 2021. For information regarding quality control and cell filtering of these 4 datasets, please refer to Meistermann et al. 2021.”

The unsupervised clustering used to annotate cell types is unconventional (especially with the high number of clusters chosen), which is not a problem, but should be clarified. Improving the figure 3D to make it clearer and providing a cell cluster correlation plot might help to better appreciate the relationship between cell types.

We agree that the gene expression heatmap in figure 3D contributed little to the interpretation of the data/results. As suggested, we have replaced this heatmap with a cell cluster correlation plot to help appreciate cell state similarities. (Changes in figure 3.)

It could be emphasized that the ICM/TE branch cell type is a major difference with the mouse topology, as the readers might not be aware that the ICM/TE is an unspecified blastocyst state that only exists in humans.

There appears to be some misunderstanding around the use of “ICM/TE branch”. The cluster comprises an uncommitted population at the branching point from morula to either ICM or TE, as also described in the mouse embryo. We have adjusted the discussion to make more clear that the two branching point clusters are heterogeneous populations, not unitary cell types or states:

“The branching populations reside at critical junctures in blastocyst formation, the partitioning of extraembryonic and embryonic lineages. These branchpoint clusters do not define unitary states. On the contrary, cells in these clusters are heterogeneous and may become specified to alternative fates. For example, PDGFRA, a hypoblast marker (Corujo-Simon et al. 2023), and NANOG, an epiblast marker (Allegre et al. 2022), are heterogeneously distributed in the Epi/Hyp branching population. Furthermore, branch cluster boundaries extend beyond the topological bifurcation, potentially indicating that cells remain plastic and may be redirected. This would be consistent with the demonstration in mouse embryos that cells expressing ICM genes remain capable of generating TE up to the late 32-cell stage (Posfai et al. 2017).”

Page 9 To further substantiate the stepwise ICM/TE and EPI/PrE specification events, authors could project cells from each embryo on the UMAP, and analyze what are the co-occurrence of cells (as performed for instance in Meistermann et al 2021). This should show as reported (and cited by the authors) that some GATA3 positive cells (TE fated) start appearing from late morula stage and that ICM cells almost never co-exist with EPI nor Hyp in embryos.

We appreciate this suggestion. We have generated the requested plots showing where cells from individual embryos at different developmental timepoints are positioned on our UMAP embedding. (new supplemental figure (New figure, Figure S6). We present a summary heatmap of cell co-occurrence in revised Figure 4. These results offer greater insight than the RNA velocity analysis, which we have moved to supplemental Figure S6. We have added discussion of these analyses in the “Lineage branching blastocyst development” Results section.

Reviewer #1 (Significance (Required)):

The presented methodology shows significant value especially in the field of scRNA-Seq, where the critical step of feature selection is often inadequately addressed. Furthermore, this field is characterized by a limited set of feature selection methodologies. cESFW appears to be an important alternative to HVG methods that could improve scRNA-Seq analysis in certain contexts.

The new findings on early human development are somehow incremental, but a welcome addition to solidify the two-step model and refine the concept of reject cells. The audience for this early development context is specialized, but cESFW will most likely have an impact to the entire field of scRNA-Seq analysis.

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

Here, Radley and Austin present a novel approach for feature weighting in scRNAseq data based on entropy sorting. Feature selection is a central part of scRNAseq analysis, and it is most likely the case that there is no single approach that outperforms all others across all datasets. Hence, innovation in this space is needed for the field. The cESFW method presented here has several appealing properties from a theoretical point of view, and it also performs well on the synthetic and real datasets considered. Nevertheless, there are several major issues that need to be addressed before I can recommend the manuscript for publication:

1 The original entropy sorting (eq 1 in SI 1) is based on only two discrete states. However, calculating entropy for continuous distributions can be more tricky and it is unclear to me what assumptions are made regarding the gene expression. Could the authors clarify what properties of the distribution are required for the updated ESE equation to be valid? Is the only assumption that values are drawn from the [0, 1] interval? What happens if values are highly skewed, ie forming a bimodal or power-law distribution rather than something close to a uniform distribution?

We agree that it is beneficial to clarify these points. We have added a section titled “Assumed properties of underlying sample distributions” to the supplemental information. Briefly, we show that the ESS correlation metric is directly linked to the commonly used correlation metric, Mutual Information (MI). A desirable properly of MI is that it is able to capture non-linear/skewed relationships between features. The ES framework and ESS share this property with MI, allowing the ES framework to be relatively robust to presence of non-uniform distributions.

The main assumption for applying ES is that the features can be meaningfully scaled between values of 0 and 1. For gene expression, an intuitive way of achieving this is to inspect each gene and designate 0 count values as having 0 expression activity, and the maximum counts as having activities of 1, and all values in between existing within the [0,1] interval. A useful property of ES is that we do not need to assume a particular shape or distribution of the samples within the [0, 1] interval. The ES framework is non-parametric and does not require an assumed distribution to calculate the conditional entropy (CE), even in the continuous form. This is possible because the ES framework is formulated by turning the probabilistic form of CE into an ordinary differential equation (ODE), where the only dependent variable, x, is the overlap between the minority state activities of each individual sample. This calculation is explicitly identifiable/calculable, and is permutation invariant, meaning the shape of the distributions of a reference feature (RF) and query feature (QF) does not need to be assumed/defined. In other words, the ES framework quantifies to what degree active expression states enrich/overlap with one another in a manner that is robust to different distribution shapes.

2 How robust is the procedure for the choice of percentile for normalizing the gene expression scores? Does one get roughly the same results for 90-99th percentile or is it sensitive to this choice?

We have carried out a sensitivity analysis on the choice of percentile for each of the synthetic datasets and added it to the manuscript. (New figure, Figure S11). We find that on each of our 4 synthetic datasets the final results of cESFW are robust to a wide range of normalisation percentiles.

3 Similarly, I am concerned about the procedure for how to choose the number of significant genes. How robust is this process? Also, it is not altogether clear how to generalize the procedure outlined on p19. Most potential users would benefit from more quantitative guidelines. In particular, having to rely on interpretation of GO terms typically requires a considerable amount of understanding about the system at hand which could make it challenging to apply the procedure for others. For most users it would be helpful to know how robust the procedure is to this step and also if there could be more stringent guidelines for how to decide which genes to include.

We understand the reviewers concern regarding the robustness of feature selection on real scRNA-seq datasets. We have now applied our cESFW workflow to peripheral blood mononuclear cells (PBMC) scRNA-seq data, and found cESFW feature selection to be comparable, and by one metric more robust, than Seurat and Scran HVG selection (New Figure S2).

As cESFW is applied to more scRNA-seq data, we will learn more about how results compare to highly variable gene selection, and how workflows may be adapted to optimise results in different scenarios. For example, we have found that supervising the selection of gene clusters using a small set of markers known to be important in the system of study can help identify which clusters of genes should be retained during gene selection. We have added this to the materials and methods with the following paragraph:

“Furthermore, we suggest supervising the selection of gene clusters using a small set of markers known to be important in the system of study. In this work, we found that genes known to be important during early human embryo development (FigS4) are enriched in the dark blue cluster of genes, further suggesting that this cluster of genes is more likely to separate cell type identities in downstream analysis.”

While gene cluster selection supervision in this manner requires a degree of domain expertise, we believe this is not unreasonable for most applications, and is the case for many scRNA-seq analysis pipelines.

Our primary software contribution is the cESFW algorithm which calculates the ESS and EP matrices. With this manuscript we provide 6 commented workflows for applying cESFW to different datasets (4 synthetic data, human embryo data, PBMC data). We believe these workflows provide a good balance of documented use cases and user flexibility for cESFW usage. This is important because it is advantageous to be able easily to adapt workflows to incorporate domain expertise and different methodologies. Although workflows such as Seurat and Scran are user-friendly, their rigidity can be difficult when wanting to deviate from their standard workflows. In summary, we believe that our provided workflows are suitable for users to implement cESFW, while providing the flexibility to apply adapted pipelines.

4 The comparison of the clusterings on p6 is not really fair is it? If I understand it correctly, the 3,012 genes identified by cESFW was used to define clusters in fig 3c through unsupervised clustering. The authors then use HVG methods to identify 3,012 genes and then carries out clustering based on those. To evaluate the methods the silhouette score is used, but the labels from the cESFW clustering is used as ground truth. This does not sound like a fair way to compare. Could the authors please clarify, and if needed come up with an approach where the three methods have a more level playing field if needed.

The reviewer raises a fair point regarding the comparison of cluster identities and ranked gene lists. This issue is a chicken and egg problem, in that we require a baseline to benchmark different methodologies but lack an explicitly defined ground truth. For that reason we used synthetic datasets for initial comparison.

For the human embryo data, we have presented substantial evidence that our cluster annotations are biologically coherent and consistent with prior knowledge. We therefore consider it legitimate to compare the ranked lists of Seurat, Scran and cESFW. However, we acknowledge the potential bias and have mentioned this in the “Limitations of the study” section.

In addition, we have now analysed the peripheral blood mononuclear cells (PBMC) scRNA-seq dataset that is used in the tutorial workflows of Seurat and Scran. This PBMC dataset is arguably better defined since it has more discrete populations of cells, and by using the Seurat generated cell type labels we bias the analysis towards Seurat rather than cESFW. The results show that cESFW performs comparably to Seurat and Scran, and that the cESFW ranked gene list may be more stable than Seurat and Scran. These results suggest that cESFW can be widely applicable as a suitable alternative for feature selection. We have included this analysis in the Results and as a supplemental figure (New figure, Figure S2).

5 The main cESFW.py file in the github repository is clearly well structured and commented. However, I would like to see a much better documentation so that one does not have to go through the source code to understand what functions there are and what they do. In particular, I would like to see a vignette to make it easier for others to incorporate cESFW into their workflows.

We thank the reviewer for the positive comments regarding our cESFW.py commenting. We accept that our initial submission failed to point the reader directly towards our example workflows that provide step by step, well commented vignettes for using cESFW to analyse scRNA-seq data. In our initial submission we provided 5 workflows (4 synthetic data and the human embryo data), and in the re-submission we have added a workflow for analysing PBMC data. We have updated our cESFW Github to guide users to these example workflows (https://github.com/aradley/cESFW/tree/main).

Please note, the embryo workflow will be easily accessible through GitHub, whereas the synthetic data and PBMC workflows will be provided through a Mendeley data link (referenced in the manuscript and on our GitHub). However, the content of the Mendeley link cannot be made public until the paper is finalised, as it cannot be changed after publication. We provide a temporary public Dropbox link for the reviewers so that they may access the additional workflows (https://www.dropbox.com/scl/fo/xr5o9xm6490ftjsa55wxg/h?rlkey=maindrxwdqnirsw1en3my5qsr&dl=0).

Minor:

Why are the figures not always in order? For example, fig S10 is mentioned before fig S2 on p 6

Thank you for pointing this out; we have amended the text.

I am not sure if the indexing in eq 1 (p 18) is correct. j is both on the LHS and it is also being summed over on the RHS. Should one of these be i instead?

The indexing is correct. Each column j of a matrix refers to gene/feature on the RHS, and in the calculation on the RHS we take the column averages, leading to vector on the LHS that is still indexed by genes/features j. We have clarified this in the text.

Reviewer #2 (Significance (Required)):

The work presents a new method for feature selection in scRNAseq. Feature selection is a very important step and can have a big impact on findings. The method presented here is theoretically sound and it seems to provide interesting result when applied to early embryo development. However, as cESFW is only tested for one dataset it is unclear how well the method generalizes to other problems and datasets.

Appreciation of the utility of cESFW will grow as it is applied to more datasets. However, we would like to highlight that the human embryo dataset consists of 6 independent scRNA-seq datasets from different laboratories, and that cESFW was able to identify common and differing structure between them without any batch correction, smoothing or feature extraction. We have added to our summary that we propose cESFW may be best suited to analysis of transcriptome trajectories in time course and developmental data. However, we have also now performed comparison of Seurat, Scran and cESFW feature selection in a different context, using a reference PMBC scRNA-seq dataset. The results demonstrate that cESFW is a viable alternative for feature selection in that static system also (New figure, Figure S2).

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Referee #2

Evidence, reproducibility and clarity

Here, Radley and Austin present a novel approach for feature weighting in scRNAseq data based on entropy sorting. Feature selection is a central part of scRNAseq analysis, and it is most likely the case that there is no single approach that outperforms all others across all datasets. Hence, innovation in this space is needed for the field. The cESFW method presented here has several appealing properties from a theoretical point of view, and it also performs well on the synthetic and real datasets considered. Nevertheless, there are several major issues that need to be addressed before I can recommend the manuscript for publication:

1. The original entropy sorting (eq 1 in SI 1) is based on only two discrete states. However, calculating entropy for continuous distributions can be more tricky and it is unclear to me what assumptions are made regarding the gene expression. Could the authors clarify what properties of the distribution are required for the updated ESE equation to be valid? Is the only assumption that values are drawn from the [0, 1] interval? What happens if values are highly skewed, ie forming a bimodal or power-law distribution rather than something close to a uniform distribution?
2. How robust is the procedure for the choice of percentile for normalizing the gene expression scores? Does one get roughly the same results for 90-99th percentile or is it sensitive to this choice?
3. Similarly, I am concerned about the procedure for how to choose the number of significant genes. How robust is this process? Also, it is not altogether clear how to generalize the procedure outlined on p19. Most potential users would benefit from more quantitative guidelines. In particular, having to rely on interpretation of GO terms typically requires a considerable amount of understanding about the system at hand which could make it challenging to apply the procedure for others. For most users it would be helpful to know how robust the procedure is to this step and also if there could be more stringent guidelines for how to decide which genes to include.
4. The comparison of the clusterings on p6 is not really fair is it? If I understand it correctly, the 3,012 genes identified by cESFW was used to define clusters in fig 3c through unsupervised clustering. The authors then use HVG methods to identify 3,012 genes and then carries out clustering based on those. To evaluate the methods the silhouette score is used, but the labels from the cESFW clustering is used as ground truth. This does not sound like a fair way to compare. Could the authors please clarify, and if needed come up with an approach where the three methods have a more level playing field if needed.
5. The main cESFW.py file in the github repository is clearly well structured and commented. However, I would like to see a much better documentation so that one does not have to go through the source code to understand what functions there are and what they do. In particular, I would like to see a vignette to make it easier for others to incorporate cESFW into their workflows.

Minor:

Why are the figures not always in order? For example, fig S10 is mentioned before fig S2 on p 6

I am not sure if the indexing in eq 1 (p 18) is correct. j is both on the LHS and it is also being summed over on the RHS. Should one of these be i instead?

Significance

The work presents a new method for feature selection in scRNAseq. Feature selection is a very important step and can have a big impact on findings. The method presented here is theoretically sound and it seems to provide interesting result when applied to early embryo development. However, as cESFW is only tested for one dataset it is unclear how well the method generalizes to other problems and datasets.

My expertise is in computational genomics.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, Arthur Radley and Austin Smith designed a new feature selection method for scRNA-Seq, which is a successor to ESFW previously proposed by the same authors. As an evolution of this earlier framework, cESFW is also based on the idea that informative genes share information with other genes, whereas non-informative genes have a more random relative expression. The authors emphasize the key importance of feature selection in the scRNA-Seq workflow and assess the current state of the art for this step. They also propose that better feature selection leads to less data transformation. They show that cESFW outperforms Scran and Seurat feature selection in most cases of synthetic datasets. cESFW is then used in the context of early human development, re-analysing data from several published datasets where they show that they do not require batch correction. They also further strengthen the conclusion that a "2-step" model for TE-ICM and EPI-Hyp differentiation is also present in human embyros. Finally, they map several types of in vitro pluripotent stem cells, in particular primed and naive, to their manifold and study the evolution of the gene signatures during early human development. Overall, the manuscript is well written and presents a solid methodology. The re-analysis of human early development is convincing and justified. The main critic is that the quality of figures can be greatly improved: their resolution is too low and they are hard to read. For instance, more contrasted color schemes could be used to improve clarity, and given the high number of clusters for some UMAPs, indicating the name of some cluster near their centroids should improve clarity.

Comments:

Page 2 I think the criticism of PCA is unfair because it is not a true feature selection method, and it is mainly used for computational purposes. I believe that for most workflows, between 30 and 50 PCs are retained, which do not significantly change the results in the downstream analyses. The citation (Yeung and Ruzzo 2001) does not seem appropriate, as they examine cases where only a small number of PCs are retained, outside the context of scRNA-seq. "Furthermore, HVG selection has been found to be biased toward selecting highly expressed genes over low expressed genes." Could the author justify or remove this statement, as the Seurat and Scran methods are specifically designed to consider average expression to determine HVG? The cited article (Yip, Sham, and Wang 2019) raises this issue for methods other than Seurat and scran.

Page 6 I might have missed it, but I do not understand the number of cells in the early human development dataset also shown in Figure S2B. The Petropoulos et al. dataset alone is larger than the sum of cells from different cell types. Is there some filtering step that is not described? The unsupervised clustering used to annotate cell types is unconventional (especially with the high number of clusters chosen), which is not a problem, but should be clarified. Improving the figure 3D to make it clearer and providing a cell cluster correlation plot might help to better appreciate the relationship between cell types. It could be emphasized that the ICM/TE branch cell type is a major difference with the mouse topology, as the readers might not be aware that the ICM/TE is an unspecified blastocyst state that only exists in humans.

Page 9 To further substantiate the stepwise ICM/TE and EPI/PrE specification events, authors could project cells from each embryo on the UMAP, and analyze what are the co-occurrence of cells (as performed for instance in Meistermann et al 2021). This should show as reported (and cited by the authors) that some GATA3 positive cells (TE fated) start appearing from late morula stage and that ICM cells almost never co-exist with EPI nor Hyp in embryos.

Significance

The presented methodology shows significant value especially in the field of scRNA-Seq, where the critical step of feature selection is often inadequately addressed. Furthermore, this field is characterized by a limited set of feature selection methodologies. cESFW appears to be an important alternative to HVG methods that could improve scRNA-Seq analysis in certain contexts.

The new findings on early human development are somehow incremental, but a welcome addition to solidify the two-step model and refine the concept of reject cells. The audience for this early development context is specialized, but cESFW will most likely have an impact to the entire field of scRNA-Seq analysis.

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Reply to the reviewers

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

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

We thank the Reviewer for this positive feedback on our study.

I have three comments

Q. Did the authors also measure the oxygenate activity of the enzyme? This is relevant to the evolution of carboxysomes and CCMs in general.

We agree that this is relevant but there are technical limitations for achieving this with the current framework. This pipeline’s emphasis on the carboxylation rate allows for the screening of a high number of rubisco variants covering a wide genetic diversity. It provides a way to approach the complexity of the kinetic constraints of this enzyme with a realizable and reproducible method. However, we agree that the measurements of oxygenase activity, as well as affinities to CO2 and O2 , would enrich our understanding of the evolution of rubiscos in the context of CCMs, and thus expanding our pipeline in the future to cover the other kinetic dimension would be worthwhile but cannot be achieved currently due to various technical constraints (other dimensions to explore, like the temperature effect, could also be included). In line also with the comment of reviewer #3, we have expanded our discussion in the manuscript to clarify this matter more thoroughly:

“By centering our analysis on the carboxylation rate, this pipeline systematically shows the particularity of carboxysome-associated rubiscos which are characterized by a poor affinity to CO2 (Badger et al, 1998; Falkowski & Raven, 2007) alongside a relatively high carboxylation rate (our data). This likely reflects the aforementioned catalytic tradeoff, suggesting that higher local concentrations of CO2 within CCMs probably allowed rubiscos to evolve towards higher kcat and KM. High-throughput measurements of other kinetic parameters beyond what was achieved here, such as the KM for both gasses or the oxygenation rate, would be valuable. It could provide values of the carboxylation efficiency, or even the enzyme specificity, which would enrich our understanding of this enzyme and of its adaptation to the atmospheric composition over geological timescales.”

1. How do predicted structures (e.g., using Alpha fold) vary with catalytic efficient?

We generated Alpha Fold structures of the 98 active variants revealed in this study and performed preliminary structural analysis of the active site. There was no strong correlation between measured rates and the active site structure. The RMSD of generated structures has a median RMSD of 2.7 Å for the large and small subunit together, and 1.3 Å for the active site, suggesting high conservation of the structure of rubisco, and probably explaining the difficulty to associate rate variation with any clear structural feature (especially coming from prediction algorithm already showing uncertainties on the order of magnitude of an angstrom (Jumper et al, 2021; Terwilliger et al, 2024)).

We added a paragraph about this new analysis in the Results and in the Materials and Methods sections of the manuscript, and we present the results in new Supplementary Fig. 12. We made these structures available on the gitlab folder associated with this paper.

1. The authors should note the paper by Tortell (not this reviewer) https://aslopubs.onlinelibrary.wiley.com/doi/pdfdirect/10.4319/lo.2000.45.3.0744

Thank you. We added a reference to this paper in the following sentence: “Another strategy consists of the evolution of rubisco towards stronger affinity for CO2 (Tortell 2000).”

Reviewer #1 (Significance (Required)):

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

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

I very much enjoyed reviewing this manuscript. de Pins et al provide a timely report on the catalytic turnover rate of a large number of Rubisco enzymes within the FormI group. These data provide novel insights into generalities of Rubisco function, specifically within certain phylogenies, and extend our understanding of carbon acquisition in these systems. In particular, the data presented by de Pins et al provide new insights into the relative carbon fixation rates of alpha-cyanobacteria, for which there are very few studies reporting catalytic turnover. It is apparent that the CO2 concentrating mechanisms (CCM) of cyanobacteria, especially the alpha-cyanobacteria (containing FormIA Rubisco) are a globally important contributor to CO2 capture into the biosphere via their carboxysomal Rubisco enzymes. This report provides then first broad selection of FormI Rubiscos to enable comparisons of catalytic turnover across this dominant enzyme family and shows that FormIA Rubiscos from phototrophic systems, and encapsulated in carboxysomes, are on average the fastest enzymes.

We thank the Reviewer for the positive remark on the novelty of the study.

de Pins et al use a high throughput screening technique that provides a highly correlative estimate of Rubisco turnover compared with traditional assays. This screen is based upon bulk expression of enzymes within E. coli from synthesised genes, and in some cases the co-expression of chaperonin factors to boost expression and solubility of holoenzymes. The assay process is sound and of high quality and the interpretations clear and uncomplicated.

The conclusions are sound and I only have a number of minor issues for consideration.

Minor comments: Temperature effects on 'true' Rubisco turnover rates. The authors quite reasonably note that a single measurement temperature was used in the assay and that this may not necessarily reflect the catalytic turnover of Rubiscos from thermophiles. Suppl. Fig 5b indicates a relatively large number of 'hot spring' species that have, generally, a low median kcat compared with, for example, both cyanobacterial classes. Can the authors comment on whether or not the thermophile set is not highly represented by one group (e.g. phototrophic alpha-cyanobacteria). Does this thermophile dataset have the potential to influence the generalities presented? Fig 2 would suggest this is not the case but it is not possible for the reader to know if all or any thermophiles are represented in Fig2 (as opposed to Suppl. Fig 4).

We indeed identify 3 groups of rubiscos that are either expressed by thermophilic bacteria (Supplementary Figure 10), and/or are associated with hot environments (hot spring and hydrothermal vent; see Supplementary Figure 5). These rubiscos show relatively lower rates. We grouped them together and reproduced our main analysis (from Figure 2) with and without rubiscos from this group to create a new Figure (Supplementary Fig. 11). Interestingly, alpha-cyanobacteria had no representatives among this group of thermophilic and hot-environments-associated rubsicos. However, this is unlikely to explain the result observed as removing them does not influence the obtained tendencies. We add the following sentences in the Results section:

“Additionally, the slightly lower carboxylation rate of rubiscos originating from thermophilic bacteria and isolated from hot environments (Supplementary Fig. 5 and 10) aligns with expectations, considering that these rubiscos naturally work at higher temperatures than in our in vitro assay (30°C). However, this is unlikely to explain the observed trends as the main results of this study are not affected by the removal of these rubiscos (Supplementary Fig. 11).”

We also noticed, while reviewing the study, that the code generating Supplementary Fig. 8 and 10 incorrectly duplicated some dots for a few rubiscos (less than 5), although this did not affect the overall results. We have fixed this issue and have now updated the figures accordingly.

Line 98: "in spite of" should be "despite"

Done.

Lines 171-173: There is an additional alpha carboxysomal Rubisco for which there are catalytic parameters described (Chapter 11 Engineering Photosynthetic CO2 Assimilation to Develop New Crop Varieties to Cope with Future Climates. RE Sharwood, BM Long - Photosynthesis, respiration, and climate change, 2021). This book chapter reports a kcat of 11.9 s-1 for the alpha carboxysomal Rubisco from Synechococcus WH8102, very much in line with the authors conclusions.

We added this rubisco to the list of previously characterized rubisco and updated Figure 1 accordingly. We also updated the following sentence:

“However, such statements were made based on scarce measurements, with only three kcat,C values currently available for both rubisco groups (Shih et al, 2016; Long et al, 2018; Sharwood & Long, 2021; Wilson et al, 2018; Aguiló-Nicolau et al, 2023).”

Lines 232-234: I note that ref 30 posits that low CO2 was the more likely driver of carboxysome evolution than high O2.

We agree that our phrasing did not point clearly enough that CO2 was more likely the driver of carboxysome evolution, rather than high O2. We rephrase the sentence to: “Carboxysomes likely evolved during the Proterozoic eon - in the context of the continuous decrease of carbon dioxide in Earth’s atmosphere (Flamholz & Shih, 2020)”

Line 235: The preferred term is either "CO2 concentrating mechanism" or "inorganic carbon concentrating mechanism"

We rephrased into “CO2 concentrating mechanisms”.

Lines 254-256: The relative saturation of carboxysomes with Rubisco is still somewhat undecided, although relatively new datasets enable more accurate comparisons. A number of papers from the Liu Lab (Liverpool) enable estimates of Rubisco active site concentrations for alpha and beta carboxysomes in the range of 2-6 mM. It appears at this stage that Rubisco active site concentrations may be highest in alpha-carboxysomes.

We thank the reviewer for drawing our attention to the work of the Liu lab which, while acknowledging potential inaccuracies in the estimates, tends to show a higher concentration of rubiscos in alpha-carboxysomes than in beta-carboxysomes (Sun et al, 2019; Sun et al, 2022). We removed this statement from the text.

Lines 312-318: That genes were codon optimized for E. coli expression raises an interesting question about the effect of Raf1 on Rubisco solubility. Assuming expression rates were not constrained, can any conclusions be made as to the amino acid sequence differences that led to lower solubility? One assumes that the Rubisco sequences had a high degree of identity?

We indeed note that the fact that every rubisco gene from this study was codon optimized for E. coli expression suggests that the solubility issues met here were post-translational. This suggests a post-translational role for Raf1 in rubisco folding/assembly that is in line with the mechanism proposed by Xia et al. of an interaction of Raf1 with rubisco large subunits dimer, further mediating the assembly of an octameric core and the recruitment of rubisco small subunits (Xia et al, 2020). We also note that insoluble rubiscos were met in all form I clades, suggesting that this property was not linked to a specific group of rubiscos sequences with a high identity degree.

We add that we also tested the effect of not performing codon optimization on 8 rubiscos that were insoluble following codon optimization (to assess whether the codon optimization could negatively affect the folding, for instance by making the translation too fast). This did not yield any improvement in solubility.

Lines 333-344: Was there an attempt to use acRAF (Raf2?) for FormIA Rubiscos that did not fold successfully in E. coli?

While only 33% of β-carboxysome-associated (IB) rubiscos were originally soluble (i. e. without the coexpression of Raf1 from E. natronophila), 85% of the tested α-carboxysome-associated (IAc) rubiscos were soluble in our experimental conditions. We therefore decided that testing for the effect of co-expressing them with the chaperone acRAF would be less cost-effective.

Reviewer #2 (Significance (Required)):

This manuscript presents a significant advance in our broader understanding of the major enzyme involved in carbon input into the biosphere, Rubisco. It will be of key interest to those studying carbon biogeochemistry, global CO2 modelling, cyanobacterial and proteobacterial CCMs, and those interested in using these systems to improve plant-based carbon capture for food security and global carbon abatement systems. It provides, for the first time, a large dataset of hitherto unknown Rubisco kinetics in a globally important group of organisms. The study is extremely well carried out and will likely form the basis of future Rubisco screens to provide greater clarity to our knowledge base of this globally important enzyme.

My expertise is in the study and application of CCMs as CO2 acquisition systems that can be used for Synbio applications.

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

Summary: The authors have presented a tremendous study into the diversity of carboxylation speed (kcatc) from bacterial Form I Rubisco enzymes. The authors identified some nice diversity in kcatc which resulted in the finding that Rubisco's originating from within a CCM were faster, which confirms what has been previously observed in the literature. The authors provided information on a pipeline to screen large numbers of Rubisco variants. In this manuscript, the authors tested 144 different enzymes with 112 of these successfully expressed in E.coli and of these 98 showed substantial catalytic activity. The authors showed that alpha cyanobacterial Rubisco possessed the fastest kcatc when compared to beta cyanobacterial counterparts which is contrary to that published in the literature so far. The authors have provided some nice insight into how they improved expression of soluble Rubisco with expressing bacterial chaperonin and Rubisco assembly factors such as Raf1 and rbcX. All which have been previously discovered plant and cyanobacteria. The authors also presented some nice correlations as shown in figure 2 and some weaker and non-correlations to various environmental parameters in the supplementary data.

Overall, the field will learn something from this large body of work that has characterized only one Rubisco catalytic parameter.

We thank the Reviewer for these positive comments.

Major points: 1) The authors only measured carboxylation speed using a spec assay. The Michaelis constant for CO2 measured in N2 and 21% Oxygen is also valuable to understand the diversity in Rubisco catalysis. The authors should perhaps mention this and that the carboxylation efficiency is also an important measure for comparing Rubisco enzymes.

In line with this and with the comment of reviewer #1, we have expanded the Discussion to include the following:

“By centering our analysis on the carboxylation rate, this pipeline systematically shows the particularity of carboxysome-associated rubiscos which are characterized by a poor affinity to CO2 (Badger et al, 1998; Falkowski & Raven, 2007) alongside a relatively high carboxylation rate (our data). This likely reflects the aforementioned catalytic tradeoff, suggesting that higher local concentrations of CO2 within CCMs probably allowed rubiscos to evolve towards higher kcat and KM. High-throughput measurements of other kinetic parameters beyond what was achieved here, such as the KM for both gasses or the oxygenation rate, would be valuable. It could provide values of the carboxylation efficiency, or even the enzyme specificity, which would enrich our understanding of this enzyme and of its adaptation to the atmospheric composition over geological timescales.”

2) The authors mentioned that they used E.coli lysates. Did the authors test for background activity due NADH dehydrogenases which are present in bacterial lysates? This could impact the catalytic rates measured.

The background activity due to dehydrogenases from the lysate is negligible compared to the measured reaction (see as an example, in Supplementary Fig. 16A, the gray curve, corresponding to a CABP concentration of 90 nM, fully inhibiting rubisco in the reaction). Moreover, the use of CABP in the spectroscopic assay allows to take into account any “background activity” that would come from an element independent of rubisco because this background would be identical at every CABP concentration. We modified Supplementary Note 1 to make this point clearer:

“We note that any NADH dehydrogenation due to other native E. coli proteins, while low (see the [CABP] = 90 nM gray curve of Supplementary Fig. 16A), is not influencing the measurement of the carboxylation rate which relies on the differential Vmax values at changing CABP concentrations (which should not affect the rates of these dehydrogenases).”

3) For the microtitre plate assay, did the authors correct for the different pathlength? This is crucial for the Beer-Lambert law which is used to calculate the consumption of NADH.

Because our assay is performed in a microwell plate instead of a standard 1 cm quartz cuvette, we indeed calibrated the assay to empirically determine the optical path length in our conditions. We add the following sentence in the Material and Methods section to better explain the measurement of NADH concentration in our assay:

“Knowing the NADH extinction coefficient at 340 nm (ε340 = 6220 M-1cm-1), and after measuring the optical path length (𝑙 = 0.26 cm) with an NADH calibration curve in our setting, we used Beer-Lambert law (𝐴340 = ε340 . 𝑙 . 𝑐) to measure the NADH concentration 𝑐.”

4) Did the authors consider studying the temperature response of kcatc for these enzymes? This could also reveal some interesting insight into their data.

We indeed considered this. With a high-throughput pipeline involving >100 enzymes to express and test in parallel, we had to limit the experimental testing conditions to be realistic both in terms of time and budget. However, the finding that rubisco variants from thermophiles tend to have lower carboxylation rates in our standardized conditions (30°C) suggest that they will probably show faster rates at temperatures closer to their optimal growth temperature. We therefore agree that the study of the temperature response of the carboxylation rate in further works could validate these hypotheses and bring more insight into the catalytic characteristics of rubisco. We further emphasize this point in the following modified sentence:

“Investigating the temperature response of rubisco carboxylation rate in further work could shed light on the importance of this parameter, especially among thermophilic or psychrophilic associated enzymes.”

5) With this new catalytic knowledge, what can the field now do with this data to inform new research directions?

We believe this new knowledge can inform new research directions in the field of microbial ecology, metabolic engineering, and machine learning in the context of kinetic parameters prediction. We modified a paragraph in the discussion to elaborate on this point:

“This study provides a systematic exploration of bacterial form I rubisco maximal rates and its relationship with various contextual factors that could have shaped the evolution of this most abundant enzyme on Earth. It holds potential for future metabolic and ecological studies about specific bacterial species – for instance among cyanobacteria for which 40 rubiscos have been characterized here. By enriching our knowledge on carboxylation rates and their connection to environmental factors, it can also contribute to more accurately modeling global carbon fluxes. Additionally, this dataset of rubisco sequences and their associated rates can facilitate linking sequence motifs to catalytic function. Ultimately, it can improve our understanding, and possible harnessing, of bacterial CCMs for the potential development of plant-based carbon capture strategies, the increase of agricultural yields and the support of sustainable food production in the face of a changing climate.”

Minor comments: The figures are of outstanding quality and easy to follow. This will set the bar high in the literature. I have no other minor comments.

We thank the Reviewer for noting the care taken in the graphic presentation of our results.

Reviewer #3 (Significance (Required)):

Overall, the authors have presented an excellent study into bacterial Form I Rubisco's that will further enhance our understanding of Rubisco evolution. The pipeline for expression of bacterial Rubisco's in E.coli is developed nicely by the authors and the next step will be to determine how other important catalytic parameters can be determined to have more detailed understanding of Rubisco catalysis.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

The authors have presented a tremendous study into the diversity of carboxylation speed (kcatc) from bacterial Form I Rubisco enzymes. The authors identified some nice diversity in kcatc which resulted in the finding that Rubisco's originating from within a CCM were faster, which confirms what has been previously observed in the literature. The authors provided information on a pipeline to screen large numbers of Rubisco variants. In this manuscript, the authors tested 144 different enzymes with 112 of these successfully expressed in E.coli and of these 98 showed substantial catalytic activity. The authors showed that alpha cyanobacterial Rubisco possessed the fastest kcatc when compared to beta cyanobacterial counterparts which is contrary to that published in the literature so far. The authors have provided some nice insight into how they improved expression of soluble Rubisco with expressing bacterial chaperonin and Rubisco assembly factors such as Raf1 and rbcX. All which have been previously discovered plant and cyanobacteria. The authors also presented some nice correlations as shown in figure 2 and some weaker and non-correlations to various environmental parameters in the supplementary data. Overall, the field will learn something from this large body of work that has characterized only one Rubisco catalytic parameter.

Major points:

1) The authors only measured carboxylation speed using a spec assay. The Michaelis constant for CO2 measured in N2 and 21% Oxygen is also valuable to understand the diversity in Rubisco catalysis. The authors should perhaps mention this and that the carboxylation efficiency is also an important measure for comparing Rubisco enzymes.

2) The authors mentioned that they used E.coli lysates. Did the authors test for background activity due NADH dehydrogenases which are present in bacterial lysates? This could impact the catalytic rates measured.

3) For the microtitre plate assay, did the authors correct for the different pathlength? This is crucial for the Beer-Lambert law which is used to calculate the consumption of NADH.

4) Did the authors consider studying the temperature response of kcatc for these enzymes? This could also reveal some interesting insight into their data.

5) With this new catalytic knowledge, what can the field now do with this data to inform new research directions?

Minor comments:

The figures are of outstanding quality and easy to follow. This will set the bar high in the literature. I have no other minor comments.

Significance

Overall, the authors have presented an excellent study into bacterial Form I Rubisco's that will further enhance our understanding of Rubisco evolution. The pipeline for expression of bacterial Rubisco's in E.coli is developed nicely by the authors and the next step will be to determine how other important catalytic parameters can be determined to have more detailed understanding of Rubisco catalysis.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

• I very much enjoyed reviewing this manuscript. de Pins et al provide a timely report on the catalytic turnover rate of a large number of Rubisco enzymes within the FormI group. These data provide novel insights into generalities of Rubisco function, specifically within certain phylogenies, and extend our understanding of carbon acquisition in these systems. In particular, the data presented by de Pins et al provide new insights into the relative carbon fixation rates of alpha-cyanobacteria, for which there are very few studies reporting catalytic turnover. It is apparent that the CO2 concentrating mechanisms (CCM) of cyanobacteria, especially the alpha-cyanobacteria (containing FormIA Rubisco) are a globally important contributor to CO2 capture into the biosphere via their carboxysomal Rubisco enzymes. This report provides then first broad selection of FormI Rubiscos to enable comparisons of catalytic turnover across this dominant enzyme family and shows that FormIA Rubiscos from phototrophic systems, and encapsulated in carboxysomes, are on average the fastest enzymes.

• de Pins et al use a high throughput screening technique that provides a highly correlative estimate of Rubisco turnover compared with traditional assays. This screen is based upon bulk expression of enzymes within E. coli from synthesised genes, and in some cases the co-expression of chaperonin factors to boost expression and solubility of holoenzymes. The assay process is sound and of high quality and the interpretations clear and uncomplicated.

• The conclusions are sound and I only have a number of minor issues for consideration.

Minor comments:

• Temperature effects on 'true' Rubisco turnover rates. The authors quite reasonably note that a single measurement temperature was used in the assay and that this may not necessarily reflect the catalytic turnover of Rubiscos from thermophiles. Suppl. Fig 5b indicates a relatively large number of 'hot spring' species that have, generally, a low median kcat compared with, for example, both cyanobacterial classes. Can the authors comment on whether or not the thermophile set is not highly represented by one group (e.g. phototrophic alpha-cyanobacteria). Does this thermophile dataset have the potential to influence the generalities presented? Fig 2 would suggest this is not the case but it is not possible for the reader to know if all or any thermophiles are represented in Fig2 (as opposed to Suppl. Fig 4).

• Line 98: "in spite of" should be "despite"

• Lines 171-173: There is an additional alpha carboxysomal Rubisco for which there are catalytic parameters described (Chapter 11 Engineering Photosynthetic CO2 Assimilation to Develop New Crop Varieties to Cope with Future Climates. RE Sharwood, BM Long - Photosynthesis, respiration, and climate change, 2021). This book chapter reports a kcat of 11.9 s-1 for the alpha carboxysomal Rubisco from Synechococcus WH8102, very much in line with the authors conclusions.

• Lines 232-234: I note that ref 30 posits that low CO2 was the more likely driver of carboxysome evolution than high O2.

• Line 235: The preferred term is either "CO2 concentrating mechanism" or "inorganic carbon concentrating mechanism"

• Lines 254-256: The relative saturation of carboxysomes with Rubisco is still somewhat undecided, although relatively new datasets enable more accurate comparisons. A number of papers from the Liu Lab (Liverpool) enable estimates of Rubisco active site concentrations for alpha and beta carboxysomes in the range of 2-6 mM. It appears at this stage that Rubisco active site concentrations may be highest in alpha-carboxysomes.

• Lines 312-318: That genes were codon optimized for E. coli expression raises an interesting question about the effect of Raf1 on Rubisco solubility. Assuming expression rates were not constrained, can any conclusions be made as to the amino acid sequence differences that led to lower solubility? One assumes that the Rubisco sequences had a high degree of identity?

• Lines 333-344: Was there an attempt to use acRAF (Raf2?) for FormIA Rubiscos that did not fold successfully in E. coli?

Significance

This manuscript presents a significant advance in our broader understanding of the major enzyme involved in carbon input into the biosphere, Rubisco. It will be of key interest to those studying carbon biogeochemistry, global CO2 modelling, cyanobacterial and proteobacterial CCMs, and those interested in using these systems to improve plant-based carbon capture for food security and global carbon abatement systems. It provides, for the first time, a large dataset of hitherto unknown Rubisco kinetics in a globally important group of organisms. The study is extremely well carried out and will likely form the basis of future Rubisco screens to provide greater clarity to our knowledge base of this globally important enzyme.

My expertise is in the study and application of CCMs as CO2 acquisition systems that can be used for Synbio applications.

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 excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

I have three comments

1. Q. Did the authors also measure the oxygenate activity of the enzyme? This is relevant to the evolution of carboxysomes and CCMs in general.

2. How do predicted structures (e.g., using Alpha fold) vary with catalytic efficient?

3. The authors should note the paper by Tortell (not this reviewer) https://aslopubs.onlinelibrary.wiley.com/doi/pdfdirect/10.4319/lo.2000.45.3.0744

Significance

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

We thank the three reviewers for their thoughtful and constructive comments. The changes to the text and figures made in response to the questions raised have made this a clearer and stronger manuscript. The additional citations suggested by the reviewers helped to further anchor our study within the growing literature on facultative parthenogenesis. Below we have responded to each comment in blue. We have added new data to the manuscript (Fig. 4C, Fig. S10B and Fig. S10D).

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. *

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

1. Summary: Here Ho et al. provide strong molecular evidence for the production of facultatively parthenogenetic whiptail lizards, through a gametic duplication. As evidenced through multiple routes, including microsatellites, WGS, RADseq, and RBC ploidy, and lines of evidence from multiple specimens, this study is timely in furthering our understanding of the mechanisms underlying FP. The findings are conclusive.

That said, I have several comments that should be addressed prior to publication. The introduction which addresses FP in other systems fails to cite several key studies that provide strongly molecular support for terminal fusion automixis. Similarly, the study pushes the idea that this is an adaptive trait, however without proving that the parthenogens can themselves reproduce, this is a moot point at this stage.

That said, my comments are minor. I found this to be an excellent study, well written, comprehensive in methodology, and one that I strongly advocate for publication.

We thank reviewer 1 for referring to our manuscript as an excellent study and strongly advocating for its publication. We concur with his/her points that evidence for automixis in other systems was not sufficiently referenced and that the adaptive trait hypothesis for FP is somewhat speculative. The text has been modified accordingly (see below).

Major comments - None.

Minor Comments: Should be addressed.

Line 36 - However, data that supports terminal fusion are no longer restricted to microsat data. Studies utilizing RADseq and whole-genome sequencing in snakes and crocodiles have now provided further evidence supporting terminal fusion.

See: Booth et al. 2023. Discovery of facultative parthenogenesis in a new world crocodile. Biology Letters. 19, 20230129.

Card et al. 2021. Genome-wide data implicate terminal fusion automixis in king cobra facultative parthenogenesis. Scientific Reports. 11, 1-9

Allen et al. 2018. Molecular evidence for the first records of facultative parthenogenesis in elapid snakes. R. Soc. Open. Sci. 5, 171901.

We have now included that automixis in other systems is supported by both microsatellite and NGS data in the abstract of our manuscript. The references have been included in the main text.

Ln 42 - Evidence suggesting that isolation from males was not a pre-requisite for FP has previously been reported in snakes.

See: Booth et al. 2011. Evidence for viable, non-clonal but fatherless Boa constrictors. Biology Letters. 7, 253-256.

Booth et al. Facultative parthenogenesis discovered in wild vertebrates. Biology Letters. 8, 983-985.

Booth et al. 2014. New insights on facultative parthenogenesis in pythons. Biol J Linn Soc. 112, 461-468.

Despite the prior evidence to the contrary cited by the reviewer, it is still a commonly held belief among scientists and science journalists that isolation from males promotes or triggers FP. We have placed our findings in the context of other studies, including those mentioned above, that came to the same conclusion that isolation from mating partners is not a requirement for FP. We thank the reviewer for the additional citations, which are now included in the discussion section.

Ln 48 - Is this really an argument. While an immediate transition to homozygosity will purge some deleterious alleles, given the genome-wide nature of this, there will also conversely have been strong selection for mildly deleterious alleles.

Even though many FP animals have congenital defects, our data, combined with that of others, show that seemingly healthy animals arise as well. Even if these healthy animals harbor slightly deleterious alleles, the most detrimental alleles would have therefore been purged especially for subsequent generations. We have modified the abstract to be clearer: “Conversely, for animals that develop normally, FP exerts strong purifying selection as all lethal recessive alleles are purged in one generation.”

Ln 56 - I would recommend the inclusion of both Allen et al. 2018. R. Soc. Open Sci, and Card et al. 2021. Sci Reports, here, as they are members of the elapids, not represented in the other examples.

These two citations have been added.

Ln 60 - Recent studies have highlighted the significance of sperm storage in reptiles. For example, Levine et al. 2021. Exceptional long-term sperm storage by a female vertebrate. PLos ONE. 16(6).e0252049, describe the storage of sperm by a female rattlesnake for ~70 months, with two instances of its utilization to produce healthy offspring during that period. Clearly, molecular tools are providing both support for long-term sperm storage, and an understanding of its utilization.

Recent work has indeed provided new evidence for instances of long-term sperm storage and the two mechanisms are no longer competing hypotheses, but it is clear that both mechanisms exist in nature. We have modified the text accordingly to include “Nevertheless, clear examples of long-term sperm storage have also been documented in the recent literature (29), underscoring the need for molecular methods such as MS analysis or sequencing data to elucidate the underlying mechanisms.”

Ln 68 - American Crocodile would also be suitable to include here.

This has now been included in the list of examples of endangered species.

Ln71 - The problem with this hypothesis is that parthenogens produced through FP tend to have very low viability. For example, Adams et al. 2023. Endangered Species Research, follow a cohort of sharks produced through FP and all survive. Similarly low levels of survival are reported across other systems for which FP was reported. More likely, FP is simply a neutral trait. The mother is not negatively impacted through producing parthenogens and can go on to produce sexual offspring. Few instances report successful reproduction of a parthenogen. See pers. Comm in Card et al. 2021. And Straube et al. 2016.

We thank the reviewer for the comment and agree that more data on the successful reproduction of parthenotes are needed to claim that FP is an adaptive trait. We have modified the text to include that studies on “the successful reproduction by FP offspring” are needed to support this hypothesis and have included the Straube et al. 2016 citation. We decided to omit the Card et al. 2021 citation as the reports of second-generation FP was through personal communication mentioned in this study and the results themselves have not yet been published.

Ln 79 - I doubt that there is a desperate need for this for conservation. However, I think there is a need to simply further our understanding of basic biological function, given that it is not uncommon, and is phylogenetically widespread in species lacking genomic imprinting.

We agree that understanding FP as a basic biological function is important in light of the realization that it occurs more commonly than previously thought. We have added this aspect to the text: “A better understanding of the triggers and molecular mechanisms underlying FP and the fitness of the resulting offspring are therefore needed in a variety of contexts. These include: to understand a fundamental biological mechanism and its significance in vertebrate evolution, to aid in conservation efforts including captive breeding programs, and to possibly harness FP in an agricultural context (28).”

Ln 85 - It would be worth citing Card et al. 2021., here given that they used genome-wide ddRAD markers to show support for terminal fusion.

The citation has been added.

Ln 91 - Better citations here are Card et al. 2021. Allen et al. 2018, and Booth et al. 2023, which all utilize either RADseq or WGS.

These citations have been added.

Ln 95 - The conclusion of genome duplication here was supported only by a small number of microsatellite loci. As such, given that terminal fusion has been supported through genome-wide markers in other species of snakes and crocodiles, the conclusion of genome duplication is likely incorrect.

In light of the other examples that show terminal fusion in snakes, we have removed this sentence.

Ln 96 - I would strongly disagree with this statement. Allen et al. 2018, Card et al. 2021, Booth et al. 2023, all provide evidence of heterozygous loci and thus support terminal fusion. While no species-specific chromosome level reference genome is available for any of these species, the fact that levels of heterozygosity are below 33% percent supports terminal fusion. Rates over 33% support central fusion, but have not been reported in any vertebrate to date. AS such, I would recommend the removal of this statement.

We agree that the studies listed by the reviewer all support terminal fusion in snakes and crocodiles and therefore, we have removed the statement.

Ln 121 - Recent work in Drosophila mercatorum and D. melanogaster suggest that three genes play a role in the activation of FP in unfertilized eggs. In this case, through the fusion of meiotic products. That said, it is plausible to assume that FP in these lizards has an underlying genomic mechanism that is not related to isolation from males. See Sperling et al. 2023. Current Biology. 33, P3545-P3560.E13.

Clearly isolation from males is not a key trigger in FP in whiptail lizards and other vertebrate species. With recent work from Sperling et al. 2023 and the fact that selection has led to increases in parthenogenesis in birds, an underlying genetic mechanism may well be at play. We have cited and addressed this in the discussion and propose identifying the genetic basis for FP in whiptail lizards in future studies.

“Recent work identifying key cell cycle genes inducing FP in two species of Drosophila (71) and selection resulting in higher incidences of parthenogenesis in birds (24, 33) suggest a genetic basis for the initiation of FP. [...] Additional whole-genome sequencing data for species with documented FP will aid in the understanding the genetic basis, propensity, and evolutionary significance of FP.”

Ln 126 - While these data strongly support FP of the two unusual A. marmoratus appearing offspring, can long term sperm storage be ruled out. Either through captive history or allelic exclusion of other males in the group?

We have added the following sentence to the text: “Given that all of these offspring are female, inherited only maternal alleles, and animal 122 had no history of being housed with a conspecific male during its lifetime, both interspecific hybridization and long-term sperm storage are all but ruled out and FP is strongly supported.”

Ln 171 - 191 - Given that the topic of this manuscript is the genomic mechanism underlying FP in this species, are these data necessary? These are not discussed later and as such I would recommend that they are moved supplemental material. Otherwise, they simply clutter that manuscript and detract from the key question. Indeed, they are important to show that the genome constructed is of high quality, but online Supp Mat is the place for that here.

We chose to keep this section in the main text for the following reasons: There is still a lack of published reference quality genomes for many reptile species and therefore we want to highlight that this A. marmoratus reference adds not only to the understanding of FP, but also expands the small list of reptile genomes and makes the first Aspidoscelis genome available to the community. The high quality and contiguity of the genome (as indicated by the high N50 value and BUSCO score) is important to emphasize in the main text because the absence of any heterozygous regions in FP animals supports a mechanism of post-meiotic genome duplication. We would not want to bury these key points in the supplement.

Ln 296 - Comparable estimates were made for parthenogenetic production in wild populations of two North American pitviper species. See Booth et al. 2012. Biology Letters.

In Booth et al. 2012, 2 out of 59 litters of the two pitvipers (3.39%) were identified to contain FP offspring and these results are very similar to our reported rate of FP in whiptail lizards. We have now included this similarity in our discussion. “Interestingly, these rates are similar to what has been reported for wild populations of two North American pitviper species (10)”.

Ln 312 - Again, can this really be suggested? Above, the authors state that most FP animals that hatched had congenital defects, and a large number failed to hatch. This does not sound like strong support for generating individuals that counter the effects of population bottlenecks and inbreeding depression. The authors need to take this study further and monitor the long-term viability of the FP individuals that survive.

We agree with the reviewer that the adaptive advantages of FP reproduction are dependent on the fitness and reproductive potential of FP offspring and present data is insufficient to clearly support this notion. We have modified the text to include that long-term studies are needed to support or refute this hypothesis: “However, support for this hypothesis is predicated on the fitness and reproduction of FP offspring and therefore more long-term studies on seemingly healthy individuals of FP origin are needed.”

Ln 348 - To be able to provide support for this, you need to track animals long term to understand their reproductive competence, and that of their offspring.

We have added the text: “To assess whether the co-occurrence of sexual and FP reproduction in vertebrates can indeed be considered a reproductive strategy rather than biological noise will require further studies to assess the reproductive competence and fecundity of offspring produced by either mode of reproduction.”

Ln 358 - But, the caveat is that the parthenogens must themselves reproduce. This must me stated.

The statement that parthenogens must be able to reproduce to support a hypothesis of FP as an adaptive trait has been added: “One must now consider the possibility that FP is an adaptive trait and that low rates of successful FP could contribute significantly to genome purification. Such a role for FP hinges on further studies demonstrating the ability of parthenogens to reproduce themselves either through further FP or sexually.”

Ln 359 - Note that FP can also fix mildly deleterious alleles. Only if it is strongly deleterious will it be lost.

We now make it clearer that selection only applies to strongly deleterious alleles.

Ln 361 - See above comments.

We have modified the text to include that “FP offspring will have low genetic load and only pass on neutral and mildly-deleterious alleles to the next generation.”

Reviewer #1 (Significance (Required)):

1. Significance:

While reports of parthenogenesis have been reported as far back as the early 1900's, it has only been over the last decade that reports are become common. Such that facultative parthenogenesis is no longer considered a rarity, but is recognized now as being relatively common and phylogenetically widespread in species that lack genomic imprinting - particularly reptiles, birds, and sharks. Reasons for this are both an increased understanding that the trait can occur, hence recognizing it as an alternative mechanism to long-term sperm storage, and the ease of using molecular approaches.

The fundamental questions of recent times have been understanding the mechanisms driving FP. Recent papers utilizing whole genome sequencing and ddRADseq have provided support for terminal fusion automixis in snakes and sharks. Here, this study provides evidence of gametic duplication in whiptails, a mechanism with an alternative outcome in regards to the levels of retained heterozygosity. As such, this study compares to the recent work of Card et al. 2021 (Scientific Reports), and Booth et al. 2023 (Biology Letters), in providing substantive advances in the field.

The audience for this will be broad. Parthenogenesis is a fascinating topic that attracts significant media attention. See the Altmetric score of recent papers on the topic, particularly Booth et al. 2023 (Altmetric score - ~3100). As such, the study will be of interest to both a broad readership, but will also be of great significance to a specialized group working on parthenogenesis. All round, an excellent paper that has promise to advance the field.

We thank reviewer 1 for this positive assessment and for putting our work into context.

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

Summary: The researchers bring together microsatellite and whole-genome sequencing data from long-term laboratory cultures of lizards to discover occasional production of parthenogenetic offspring by several species of otherwise sexually producing whiptail lizards ("facultative parthenogenesis, "FP") and to show that these FP-produced lizards have patterns of genomic homozygosity that are incompatible with currently held assumptions about mechanisms of FP. Instead, the FP lizards seem to have been produced by a mechanism that results in almost complete homozygosity, likely a consequence of post-meiotic duplication of genomes from haploid unfertilized oocytes. They also show that FP offspring were produced by females housed with males and along with sexually produced offspring, counter to prevailing assumptions that FP offspring are only produced in situations where mates are not available. Many of the FP-produced offspring did not survive to hatching or had major abnormalities, consistent with a situation where this high homozygosity exposes harmful alleles. Finally, the authors used reduced-representation sequencing (RAD-seq) to survey heterozygosity in 321 wild-collected whiptail lizards from 15 species, showing evidence for strikingly low homozygosity in at least one individual and perhaps up to 5, consistent with the potential for FP in nature. These data are of broad interest in demonstrating several exciting new possibilities. Most importantly, the data hint at a different mechanism of FP than previously assumed, and one that causes immediate near-complete homozygosity. This scenario would likely lead to immediate purging of harmful recessive alleles. If the selective load of this purging wasn't insurmountably high, a lineage with a history of purging could produce FP offspring of relatively high fitness. Other exciting possibilities suggested by the data include the existence of FP even in a setting where mating occurs and in natural populations, versus just captivity.

Major Comments:

I found it difficult to impossible to sort out exactly what the researchers did and with what lizards. For example, in line 107, they refer to a "systematic MS analysis" for all individuals of gonochoristic species in their laboratory, but where are these data? Indeed, at this early spot in the paper, the introduction from here on out suddenly reads like a discussion. What would be better here would be to summarize what was known and wasn't known about the system and questions involved, why gaps in knowledge were important, and what the researchers actually did for this paper. In my opinion, the paper would be a much easier read if the researchers left the results and interpretation for later in the paper.

As a consequence of the reviewers’ comments, the text of the manuscript has undergone major revision, and we trust that reviewer 2 will find this new version far more accessible. The MS data collection of more than 1000 individuals is the subject of another ongoing study and was only mentioned peripherally here to put the identification of FP into context. As most of the MS data relates to gonochoristic reproduction and interspecific hybridization, we are only presenting the data that are directly relevant to this manuscript as part of this study. To our knowledge, there is no common repository to upload raw MS data, but we have provided the data for the FP animals and controls discussed in this paper in the Github repository (see section “Data availability”).

Even with this suggested fix, however, the data are still too inaccessible and analyses too opaque. For example, in line 202, a critical definition is laid out regarding heterozygous sites as those having "equal support" for two alleles. What do the researchers mean by "equal support"? My presumption is that this is something about equal or close to equal numbers of reads, but this definition needs to be spelled out and justified because it underpins much of the downstream analyses. A similar problem occurs in line 208-209, where the authors make a statement about limiting further analysis to positions in the genome where the coverage is "equal" to the mean sequencing depth.

We have changed the text to “we defined heterozygous sites as those having two alleles supported by an equal number of reads. This stringent requirement was chosen to limit the search to apparent heterozygous sites with strong support, decreasing the chance of false positives.”. We further look at only sites where the coverage is equal to the average sequencing depth to exclude regions where over-assembly and collapse of repetitive elements would artificially increase the coverage.

Another data/analysis issue emerges with the components of the manuscript that deal with mixoploidy. As far as I can tell, these data come from one sexually produced lizard, one FP A. marmoratus, and one FP A. arizonae. While the reports of bimodality of nuclear size are certainly interesting, the data and discussion are no more than an anecdotal case study in the absence of careful replication across multiple FP lizards and comparison to sexually produced lizards. Without these data, the conclusion that “Animals produced by facultative parthenogenesis are characterized by mixoploidy” (Figure 4 caption; also see lines 324-331) is far too strong.

We have added animal IDs to figure legends 4 and S10 to clarify that these erythrocyte staining come from two FP A. marmoratus, and one FP A. arizonae. In addition, imaging from two sexually produced control animals (1 A. marmoratus and 1 A. arizonae) have now been included in S10 (as S10B and S10D). We also have included an extra panel of flow cytometry data (new Figure 4C) as a complementary methodology for ploidy determination. Both imaging and flow cytometry support similar amounts of haploid cells. With the additional data and clarification, we hope that the reviewer agrees that the observations of mixoploidy are well beyond “anecdotal”. Nevertheless, we have changed the title for Figure 4 to “Detection of mixoploidy associated with facultative parthenogenesis.” We hope that our observations here will indeed inspire future studies to see if mixoploidy is a widespread phenomenon in FP outside of whiptails as indicated by earlier work in birds.

I had a similar reaction to the discussion of developmental abnormalities and embryonic lethality of embryos of FP origin presented in lines 263-281 (also lines 307-309). What is the baseline level of such abnormalities and the frequency of lethality in sexually produced eggs/embryos/hatchlings, and especially those produced via inbreeding? These comparisons are needed to interpret the significance of the patterns observed in the FP eggs/embryos/hatchings. Analogously, the comparison of the ovaries and germinal vesicles from one FP individual relative to one sexual individual do not tell us anything nearly so definitive as the text in lines 279-281 (also see Fig. S12 title, which is too broad of a conclusion for N = 1). This overly ambitious conclusion also underpins the discussion regarding the potentially adaptive nature of FP with respect to genome purification (lines 341-363; also see lines 47-50). If FP does not actually increase the rate of purging in FP lizards relative to inbred sexual counterparts (sounds like inbreeding is common from line 339), it seems less likely that we can view FP as adaptive at least from this perspective.

We have now included a comparison between defects seen in sexually produced animals vs FP animals: “six out of 16 FP animals (37.5%) hatched with no discernable developmental defects (Fig. S11A-B). This is in stark contrast to sexually produced animals, where over 98% of hatchlings showed no abnormalities. Additionally, most of the defects noted in sexually produced animals were less severe than in FP animals including bulges in tails or truncated digits.”

We agree that our statement on the lack of differences between sexually produced and FP animals was too general. We have modified the title of Fig. S12 from “No differences between ovaries and germinal vesicles of Aspidoscelis marmoratus produced by facultative parthenogenesis or fertilization” to "Ovaries of Aspidoscelis marmoratus FP animal 8450 and germinal vesicles of FP sister 8449 revealed no differences in structure and anatomy compared to fertile sexually reproducing animals.” Due to instant complete homozygosity, FP would indeed have a higher rate of purging than inbreeding. While one hypothesis is that FP is adaptive (in large enough populations), our intentions were to highlight the alternative that FP could be detrimental in smaller populations (that already would likely experience high inbreeding rates). We would expect inbreeding to not be common in whiptails relative to other lizards given that they tend to have large population sizes and actively range across generalist habitats.

A final data concern is with the use of liver tissue for whole-genome sequencing and reference genome assembly (lines 389-390) and then using these data and the reference genome to make conclusions about ploidy/coverage. Liver tissue is very commonly endopolyploid, meaning that coverage could be artificially high for animals for which liver (vs. tail) tissue was used for DNA extraction. In particular, it would be helpful if the researchers consider whether endopolyploidy could have affected their ability to make accurate estimation of coverage and thus, heterozygosity, when libraries generated from diploid (tail) tissues are aligned to a reference genome generated from a polyploid tissue as was done here.

This is an interesting point and indeed hepatic cells in various organisms have been documented to be polyploid. The proportion of polyploid cells though vary and as far as we are aware, all published studies on polyploid hepatocytes are in mammals (DOI: 10.1016/j.tcb.2013.06.002). Reference genomes have been generated from a variety of tissue sources and liver is commonly used. As most assemblies are for haploid genomes, polyploidy (unlike aneuploidy) does not impact the assembly quality. The reference genome was also from an animal of FP origin and therefore has genome-wide homozygosity that aids in a more contiguous genome assembly by eliminating the phasing problem. For the 10 animals sequenced, genomic DNA was derived from liver for three animals and the rest from tail tissue. The sequencing data generated from either liver or tail resulted in similar coverage levels (Figure S6) and similar levels of heterozygosity (Figure 2A). Minor Comments:

Line 410: Please explain why the BLAST cutoff was changed from the default.

The BLAST cutoff was changed from the default 1e-03 to 1e-06 to be more stringent and thereby increase confidence in the BUSCO results.

Lines 441-443: Please explain why this dataset was seemingly larger than expected.

Animal 122 was sequenced on one flow cell without any multiplexing with other samples and therefore yielded more reads than other animals sequenced. We subsampled the reads from this animal for analysis, so it is directly comparable with the other WGS data.

Line 510: The link to the Github repository was broken, so I was unable to access the code and data denoted as available here.

We apologize for the unavailability of the link at the time of review. Review Commons did not request a reviewer token. The repository will be made public upon journal acceptance. We would be happy to provide a reviewer token in the meantime upon request by Review Commons.

Figure 1, and other figures featuring comparisons of MS data across parents and offspring: The authors need to engage here with the alleles that do not match either parent here (e.g., allele 282 at MS7), explaining the likelihood that these alleles indeed represent a binning error (or, perhaps, stepwise mutation from parental allele), and these alleles should be flagged. Instead, they bin these unique alleles with the most similar parental allele without any explanation or flagged. The authors do bring this point up in Figure S1, but this issue needs to be addressed in the main text (related point: the mix of red/green in MS16 offspring appear more green than red. Is this meant to denote a probability different than 50:50? If not, the authors should adjust the shading so that this shape is half green, half red).

We have added to the figure legend that single nucleotide differences are most likely binning errors and are therefore not considered “de novo” alleles. Instead, they are assigned it to the most similar parental allele, consistent with Figure S1. The shading at MS16 has been removed so that it is consistent with Figure 3.

Figure 3: Indicate that white background for alleles means that allelic inheritance is not determinable, or use the mix of colors applied in Fig. 1 to indicate as such. Unique offspring alleles should be flagged rather than just automatically assigned to the most similar parental allele. Finally, it would be helpful if the alleles were presented within loci from the shorter to the longer alleles.

We have included in the figure legend that non-shaded alleles are those for which multiple potential parents share the same allele and the inheritance therefore remains ambiguous for this locus. Single nucleotide differences are also now addressed, and sizes are ordered from smallest to largest.

Figure S7. Indicate visually which panels indicate FP animals.

We have now indicated which animals are FP and included this in Figure S6 as well.

Fig. S13. The 5 animals that had especially low heterozygosity should be flagged. The title of this figure should be toned down in light of the tentative nature of the conclusions regarding FP in nature: low heterozygosity could instead reflect, for example, a long history of inbreeding. My reaction to the data is also that the % heterozygosity distribution for many of the species looks continuous rather than the bimodality one might expect under FP vs. sexual reproduction.

Since FP has not been further confirmed in these animals, unlike those examples from our captive colony, there could indeed be other reasons for low heterozygosity. We have changed the title of the figure from “Facultative parthenogenesis in whiptail lizards collected in nature” to the more neutral “Heterozygosity estimates of whiptail lizards collected in nature.” Since there are so relatively few animals, one would not necessarily expect a bimodal distribution to be apparent in the current data. We did show that the animal with the lowest calculated level of heterozygosity (deppii LDOR30) was a statistical outlier when compared to other individuals of the same species though. Since these animals were sampled across different locations and habitats, the effective population sizes would be assumed to be different as well, reflecting the range of heterozygosity estimates seen here. This has been made clear in the text.

Reviewer #2 (Significance (Required)):

General assessment: strengths and limitations. The paper's strengths include the combination of data from lab and natural populations, the characterization of an unexpected means of achieving FP, with dramatic genetic consequences, and the data suggesting that this type of FP is fairly common and occurs even in the context of mating.

Audience: The biological questions of relevance to these discoveries are of broad interest, and the paper is likely to garner some attention from the life sciences community as whole and the popular press.

Advance: These data fill an important knowledge gap regarding the mechanisms potentially driving FP in vertebrates, how often FP is likely to occur, and its genetic consequences. The discoveries are potentially conceptual/fundamental, though the extent to which they are ground breaking is not clear in the absence of functional characterization of how FP occurs as well as the need for more rigorous comparisons and replication that I outlined above.

We thank reviewer 2 for summarizing the strengths of this manuscript, pointing out the broad interest and stating that this work fills an important knowledge gap.

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

Summary: The occurrence of facultative parthenogenesis has been described in a number of vertebrate lineages but the underlying cytological mechanism(s) have remained largely speculative due to sparsity of data. Here, Ho & Tormey et al. provide a detailed analysis of facultative parthenogenesis in gonochoristic species of the lizard genus Aspidoscelis. They show that parthenogenesis leads to a complete loss of heterozygosity (LOH) within a single generation. They attribute the LOH to diploidization through duplication of the oocytes haploid genome after completion of meiosis. This mechanism is consistent with their finding of mixoploidy in erythrocytes of asexually produced offspring. Based on LOH the authors additionally show that facultative parthenogenesis in Aspidoscelis is not condition dependent (no developmental switch): it can occur in the presence of males, alongside with sexual reproduction in the same clutch, and both in captivity and the wild. Finally, the authors show that facultative parthenogenesis is associated with developmental aberrations, likely caused by expression of homozygous recessive deleterious mutations.

Major comments: In my opinion, this study presents a very comprehensive, careful documentation of mechanistic aspects and consequences of facultative parthenogenesis in a vertebrate. The genomic and microsatellite results leave little to no doubt that facultative parthenogenesis has led to complete LOH in Aspidoscelis. I am particularly impressed by the meticulous analysis of genomic coverage to exclude e.g. false positive heterozygosity due to merged paralogs in the assembly. I also follow the authors conclusion that a post-meiotic "gamete duplication"-like mechanism is likely causative for the LOH (and the mixoploidy of erythrocytes; but I am no expert on that). I was wondering if terminal fusion automixis together with a complete absence of recombination would be worth mentioning as an (probably very unlikely) alternative in the discussion. It would be exciting to corroborate the conclusion of diploidization by genome duplication in the future, e.g. via early embryonic DNA stainings to show the duplication "in action" (if that is practically possible)...? As for this manuscript, I suggest emphasizing the indirect nature of the evidence for the mechanism of parthenogenesis a little bit more.

We thank the reviewer for highlighting the effort that went into the genomic analysis that led us to our conclusions. In terms of terminal fusion without recombination, we argue that this is not an obvious alternative explanation as a large body of work has established that at least one crossover per homologous chromosome pair is required to advance into meiosis I in many organisms (e.g. see https://doi.org/10.3389/fcell.2021.681123) and therefore the absence of recombination would likely not produce the polar bodies necessary for automixis.

We have added to the text: “In whiptail lizards, we have not been able to examine post-meiotic oocytes as locating the post-meiotic nucleus within a large yolked egg is inherently difficult. The difficulty is compounded by the unpredictability of which eggs will undergo FP development and the need to sacrifice animals to remove eggs.”

While the genome duplication mechanism we propose is indeed indirect because we are unable to visualize developing FP embryos, the most parsimonious explanation from the whole-genome sequencing analysis is genome duplication because of the lack of heterozygous regions associated with automixis. In the text, we have made sure to state genome-wide homozygosity as the basis for our conclusion.

I agree that facultative parthenogenesis in the presence of males hints at a baseline rate of parthenogenesis without requiring a developmental switch. However, this makes it difficult to rule out that sperm played a role in activation of embryonal development (gynogenesis; however I am only aware of gynogenesis in fishes and amphibians)... maybe, the authors want to take this up in the discussion. Were the five parthenogenetic individuals for whole genome sequencing actually produced in the presence of males, too?

FP has been reported to occur in isolated females for other reptile and bird species, suggesting that sperm activation is at least not a general requirement in FP of amniotes. (Watts, et al. 2006, W. W. Olsen, S. J. Marsden 1954). In all cases in this study, the female mothers were housed with conspecific or heterospecific males. While we cannot completely rule out a non-genetic contribution of sperm in these cases, it would seem to be an unlikely explanation in light of the sperm-independent reproduction by obligate parthenogenesis in other species of whiptail lizards (unlike the sperm-dependence of all unisexual reproduction in amphibians and fish). We decided to not include speculation on sperm-dependence in this manuscript as we have no evidence in favor of it, nor is there any evidence for this in the literature relating to other amniotes. In fact, most examples of FP were reported from isolated females, most likely because offspring were not expected in those cases and prompted further analysis as to their origin.

I agree with the interpretation of the LOH in the RADseq data as a likely case of facultative parthenogenesis in the wild. However, when looking at figure S13 I noticed some bimodal looking distributions (e.g. in A. guttatus). It may be interesting for future studies to look into what factors influence heterozygosity in natural populations of Aspidoscelis (e.g. inbreeding vs parthenogenesis). Could there be different mechanisms of facultative parthenogenesis in different Aspidoscelis species explaining different LOH intensities?

The continuous nature of the data may reflect natural variation between individuals and collection at various locations with possibly different effective population sizes and levels of hybridization. Low levels of heterozygosity could be indicative of inbreeding or FP in some cases. This is important to note in future studies and we have added this to the manuscript (“Further fieldwork and analysis will be required to assess the level of FP in natural populations of gonochoristic Aspidoscelis species (and other factors that could influence the observed heterozygosity such as population size, levels of hybridization, and inbreeding) …”). While there are different mechanisms of FP in other vertebrate groups, the most parsimonious hypothesis is that within a genus, the mechanism would be the same.

The manuscript is well written, the introduction nicely explains the significance of the study, the methods are fully appropriate and the results (and supplementary results) displayed comprehensibly and in great detail. The discussion might benefit from going a bit more generally into the occurrence and mechanism of obligate asexuality in Aspidoscelis. One might e.g. speculate on whether the ability for facultative parthenogenesis in gonochoristic species has facilitated the transitions to obligate parthenogenesis in the hybrid lineages and what peculiarities might predispose Aspidoscelis to parthenogenesis (e.g. are centrioles contributed by sperm required?). In addition, I think the occurrence of LOH due to gamete duplication (facultative and obligate) in invertebrates (e.g. due to Wolbachia) is worth mentioning in the discussion: e.g. there is a similar case in facultative asexual Bacillus rossius stick insects, where the early dividing cells are haploid. Some of them diploidize via duplication later and form the embryo.

Thank you for complimenting each section of the manuscript and referring to it as well-written. Our lab has a long-standing interest in obligate parthenogenesis. While it is interesting that both obligate and facultative parthenogenesis occur alongside each other in this genus, the mechanisms appear to be fundamentally different, and we would like to focus the discussion on FP in a variety of systems and its potential implications in conservation and evolution. Parthenogenesis in general is a fascinating topic for a broad audience and not discussing another form of parthenogenesis (obligate in this case), the focus remains on FP and keeps the manuscript more accessible for non-specialists. We have included the stick insect as another example of diploid restoration through genome duplication in the discussion.

Minor comments:

39-41: I am a bit puzzled by the usage of the term "post-meiotic" to contrast the diploidization through duplication with automixis. Wouldn't one consider polar body fusion after completion of meiosis II also post-meiotic? Maybe I am just not aware of how the term is usually used in this context here...

We use the term “post-meiotic” because the restoration of an entirely homozygous diploid cell can only occur after the completion of both meiotic divisions. It is our understanding that polar body fusion and meiotic restitution after meiosis I or meiosis II are generally considered meiotic mechanisms in the specialized literature, even though polar body fusion would also occur after the meiotic divisions.

65: isn't that gynogenesis (sperm-dependent parthenogenesis) in the amazon molly?

While sperm is required for parthenogenesis in the Amazon Molly, it is an all-female species that exclusively reproduces through gynogenesis. In this case, it is considered an example of obligate parthenogenesis rather than FP.

78: the term "economically viable" may be a bit puzzling for a biologist's audience. "Economically sustainable" could be an alternative.

This has been changed.

129: the Arizona male was referred to as ID 4272 above. Here it is ID 4238?

This has been corrected. The correct ID is 4272.

218: please define over-assembly (see line 207)

The definition of “over-assembly” is collapsing paralogous loci into a single representative sequence. This is now explained in the text.

263-281: please, indicate a hatching rate/ rate of malformations of sexually produced offspring for comparison.

A comparison has been added: “This is in stark contrast to sexually produced animals, where over 98% of hatchlings had no abnormalities noted.”

333: in the haploid cells recessive deleterious mutations would be exposed in the hemizygous state but in the diploid cells in the homozygous state.

The text has been modified to reflect the difference between haploid and diploid cells.

470: please, provide more detail for the RADseq analyses (variant calling, calculation of heterozygosity etc.)

We have elaborated on the analysis in the methods.

Figure 1B: please, mention in the legend that the shown mechanisms are not exhaustive, e.g. first polar body fusion could occur right after meiosis 1 or polar body formation could be skipped completely.

This has been added.

Figure 1C: it may be interesting for non-specialists to name the distinctive morphological characters setting apart the three species in the figure legend and highlight them e.g. with arrows in the figure.

We have now included in the figure legend characteristic color patterns for each species: “(C) Photographs of Aspidoscelis arizonae with characteristic blue ventral coloration (top), A. gularis with light spots in dark fields that separate light stripes on dorsum (middle), and A. marmoratus with light and dark reticulated pattern on dorsum (bottom).” Since the descriptions are specific and apparent, we did not add arrows to the pictures.

Reviewer #3 (Significance (Required)):

Significance: The study by Ho & Tormey et al. substantially enhances the understanding of (facultative) asexuality in vertebrates. In particular, while most reports of facultative parthenogenesis in vertebrates have been attributed to a form of automixis, the authors conclusively show an instance of diploidization through genome duplication, a mechanism functionally similar to "gamete duplication". The study is novel, very comprehensive and of interest for a general audience within the field of evolutionary biology.

We thank reviewer 3 for pointing out that our study substantially enhances the understanding of asexuality in vertebrates, is very comprehensive and of interest for a general audience within

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Referee #3

Evidence, reproducibility and clarity

Summary:

The occurrence of facultative parthenogenesis has been described in a number of vertebrate lineages but the underlying cytological mechanism(s) have remained largely speculative due to sparsity of data. Here, Ho & Tormey et al. provide a detailed analysis of facultative parthenogenesis in gonochoristic species of the lizard genus Aspidoscelis. They show that parthenogenesis leads to a complete loss of heterozygosity (LOH) within a single generation. They attribute the LOH to diploidization through duplication of the oocytes haploid genome after completion of meiosis. This mechanism is consistent with their finding of mixoploidy in erythrocytes of asexually produced offspring. Based on LOH the authors additionally show that facultative parthenogenesis in Aspidoscelis is not condition dependent (no developmental switch): it can occur in the presence of males, alongside with sexual reproduction in the same clutch, and both in captivity and the wild. Finally, the authors show that facultative parthenogenesis is associated with developmental aberrations, likely caused by expression of homozygous recessive deleterious mutations.

Major comments:

• In my opinion, this study presents a very comprehensive, careful documentation of mechanistic aspects and consequences of facultative parthenogenesis in a vertebrate. The genomic and microsatellite results leave little to no doubt that facultative parthenogenesis has led to complete LOH in Aspidoscelis. I am particularly impressed by the meticulous analysis of genomic coverage to exclude e.g. false positive heterozygosity due to merged paralogs in the assembly. I also follow the authors conclusion that a post-meiotic "gamete duplication"-like mechanism is likely causative for the LOH (and the mixoploidy of erythrocytes; but I am no expert on that). I was wondering if terminal fusion automixis together with a complete absence of recombination would be worth mentioning as an (probably very unlikely) alternative in the discussion. It would be exciting to corroborate the conclusion of diploidization by genome duplication in the future, e.g. via early embryonic DNA stainings to show the duplication "in action" (if that is practically possible)...? As for this manuscript, I suggest emphasizing the indirect nature of the evidence for the mechanism of parthenogenesis a little bit more.

• I agree that facultative parthenogenesis in the presence of males hints at a baseline rate of parthenogenesis without requiring a developmental switch. However, this makes it difficult to rule out that sperm played a role in activation of embryonal development (gynogenesis; however I am only aware of gynogenesis in fishes and amphibians)... maybe, the authors want to take this up in the discussion. Were the five parthenogenetic individuals for whole genome sequencing actually produced in the presence of males, too?

• I agree with the interpretation of the LOH in the RADseq data as a likely case of facultative parthenogenesis in the wild. However, when looking at figure S13 I noticed some bimodal looking distributions (e.g. in A. guttatus). It may be interesting for future studies to look into what factors influence heterozygosity in natural populations of Aspidoscelis (e.g. inbreeding vs parthenogenesis). Could there be different mechanisms of facultative parthenogenesis in different Aspidoscelis species explaining different LOH intensities?

• The manuscript is well written, the introduction nicely explains the significance of the study, the methods are fully appropriate and the results (and supplementary results) displayed comprehensibly and in great detail. The discussion might benefit from going a bit more generally into the occurrence and mechanism of obligate asexuality in Aspidoscelis. One might e.g. speculate on whether the ability for facultative parthenogenesis in gonochoristic species has facilitated the transitions to obligate parthenogenesis in the hybrid lineages and what peculiarities might predispose Aspidoscelis to parthenogenesis (e.g. are centrioles contributed by sperm required?). In addition, I think the occurrence of LOH due to gamete duplication (facultative and obligate) in invertebrates (e.g. due to Wolbachia) is worth mentioning in the discussion: e.g. there is a similar case in facultative asexual Bacillus rossius stick insects, where the early dividing cells are haploid. Some of them diploidize via duplication later and form the embryo.

Minor comments:

• 39-41: I am a bit puzzled by the usage of the term "post-meiotic" to contrast the diploidization through duplication with automixis. Wouldn't one consider polar body fusion after completion of meiosis II also post-meiotic? Maybe I am just not aware of how the term is usually used in this context here...

• 65: isn't that gynogenesis (sperm-dependent parthenogenesis) in the amazon molly?

• 78: the term "economically viable" may be a bit puzzling for a biologist's audience. "Economically sustainable" could be an alternative.

• 129: the Arizona male was referred to as ID 4272 above. Here it is ID 4238?

• 218: please define over-assembly (see line 207)

• 263-281: please, indicate a hatching rate/ rate of malformations of sexually produced offspring for comparison.

• 333: in the haploid cells recessive deleterious mutations would be exposed in the hemizygous state but in the diploid cells in the homozygous state.

• 470: please, provide more detail for the RADseq analyses (variant calling, calculation of heterozygosity etc.)

• Figure 1B: please, mention in the legend that the shown mechanisms are not exhaustive, e.g. first polar body fusion could occur right after meiosis 1 or polar body formation could be skipped completely.

• Figure 1C: it may be interesting for non-specialists to name the distinctive morphological characters setting apart the three species in the figure legend and highlight them e.g. with arrows in the figure.

Significance

Significance: The study by Ho & Tormey et al. substantially enhances the understanding of (facultative) asexuality in vertebrates. In particular, while most reports of facultative parthenogenesis in vertebrates have been attributed to a form of automixis, the authors conclusively show an instance of diploidization through genome duplication, a mechanism functionally similar to "gamete duplication". The study is novel, very comprehensive and of interest for a general audience within the field of evolutionary biology.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The researchers bring together microsatellite and whole-genome sequencing data from long-term laboratory cultures of lizards to discover occasional production of parthenogenetic offspring by several species of otherwise sexually producing whiptail lizards ("facultative parthenogenesis, "FP") and to show that these FP-produced lizards have patterns of genomic homozygosity that are incompatible with currently held assumptions about mechanisms of FP. Instead, the FP lizards seem to have been produced by a mechanism that results in almost complete homozygosity, likely a consequence of post-meiotic duplication of genomes from haploid unfertilized oocytes. They also show that FP offspring were produced by females housed with males and along with sexually produced offspring, counter to prevailing assumptions that FP offspring are only produced in situations where mates are not available. Many of the FP-produced offspring did not survive to hatching or had major abnormalities, consistent with a situation where this high homozygosity exposes harmful alleles. Finally, the authors used reduced-representation sequencing (RAD-seq) to survey heterozygosity in 321 wild-collected whiptail lizards from 15 species, showing evidence for strikingly low homozygosity in at least one individual and perhaps up to 5, consistent with the potential for FP in nature. These data are of broad interest in demonstrating several exciting new possibilities. Most importantly, the data hint at a different mechanism of FP than previously assumed, and one that causes immediate near-complete homozygosity. This scenario would likely lead to immediate purging of harmful recessive alleles. If the selective load of this purging wasn't insurmountably high, a lineage with a history of purging could produce FP offspring of relatively high fitness. Other exciting possibilities suggested by the data include the existence of FP even in a setting where mating occurs and in natural populations, versus just captivity.

Major Comments:

• I found it difficult to impossible to sort out exactly what the researchers did and with what lizards. For example, in line 107, they refer to a "systematic MS analysis" for all individuals of gonochoristic species in their laboratory, but where are these data? Indeed, at this early spot in the paper, the introduction from here on out suddenly reads like a discussion. What would be better here would be to summarize what was known and wasn't known about the system and questions involved, why gaps in knowledge were important, and what the researchers actually did for this paper. In my opinion, the paper would be a much easier read if the researchers left the results and interpretation for later in the paper.

• Even with this suggested fix, however, the data are still too inaccessible and analyses too opaque. For example, in line 202, a critical definition is laid out regarding heterozygous sites as those having "equal support" for two alleles. What do the researchers mean by "equal support"? My presumption is that this is something about equal or close to equal numbers of reads, but this definition needs to be spelled out and justified because it underpins much of the downstream analyses. A similar problem occurs in line 208-209, where the authors make a statement about limiting further analysis to positions in the genome where the coverage is "equal" to the mean sequencing depth.

• Another data/analysis issue emerges with the components of the manuscript that deal with mixoploidy. As far as I can tell, these data come from one sexually produced lizard, one FP A. marmoratus, and one FP A. arizonae. While the reports of bimodality of nuclear size are certainly interesting, the data and discussion are no more than an anecdotal case study in the absence of careful replication across multiple FP lizards and comparison to sexually produced lizards. Without these data, the conclusion that "Animals produced by facultative parthenogenesis are characterized by mixoploidy" (Figure 4 caption; also see lines 324-331) is far too strong.

• I had a similar reaction to the discussion of developmental abnormalities and embryonic lethality of embryos of FP origin presented in lines 263-281 (also lines 307-309). What is the baseline level of such abnormalities and the frequency of lethality in sexually produced eggs/embryos/hatchlings, and especially those produced via inbreeding? These comparisons are needed to interpret the significance of the patterns observed in the FP eggs/embryos/hatchings. Analogously, the comparison of the ovaries and germinal vesicles from one FP individual relative to one sexual individual do not tell us anything nearly so definitive as the text in lines 279-281 (also see Fig. S12 title, which is too broad of a conclusion for N = 1). This overly ambitious conclusion also underpins the discussion regarding the potentially adaptive nature of FP with respect to genome purification (lines 341-363; also see lines 47-50). If FP does not actually increase the rate of purging in FP lizards relative to inbred sexual counterparts (sounds like inbreeding is common from line 339), it seems less likely that we can view FP as adaptive at least from this perspective.

• A final data concern is with the use of liver tissue for whole-genome sequencing and reference genome assembly (lines 389-390) and then using these data and the reference genome to make conclusions about ploidy/coverage. Liver tissue is very commonly endopolyploid, meaning that coverage could be artificially high for animals for which liver (vs. tail) tissue was used for DNA extraction. In particular, it would be helpful if the researchers consider whether endopolyploidy could have affected their ability to make accurate estimation of coverage and thus, heterozygosity, when libraries generated from diploid (tail) tissues are aligned to a reference genome generated from a polyploid tissue as was done here.

Minor Comments:

• Line 410: Please explain why the BLAST cutoff was changed from the default.

• Lines 441-443: Please explain why this dataset was seemingly larger than expected.

• Line 510: The link to the Github repository was broken, so I was unable to access the code and data denoted as available here.

• Figure 1, and other figures featuring comparisons of MS data across parents and offspring: The authors need to engage here with the alleles that do not match either parent here (e.g., allele 282 at MS7), explaining the likelihood that these alleles indeed represent a binning error (or, perhaps, stepwise mutation from parental allele), and these alleles should be flagged. Instead, they bin these unique alleles with the most similar parental allele without any explanation or flagged. The authors do bring this point up in Figure S1, but this issue needs to be addressed in the main text (related point: the mix of red/green in MS16 offspring appear more green than red. Is this meant to denote a probability different than 50:50? If not, the authors should adjust the shading so that this shape is half green, half red).

• Figure 3: Indicate that white background for alleles means that allelic inheritance is not determinable, or use the mix of colors applied in Fig. 1 to indicate as such. Unique offspring alleles should be flagged rather than just automatically assigned to the most similar parental allele. Finally, it would be helpful if the alleles were presented within loci from the shorter to the longer alleles.

• Figure S7. Indicate visually which panels indicate FP animals.

• Fig. S13. The 5 animals that had especially low heterozygosity should be flagged. The title of this figure should be toned down in light of the tentative nature of the conclusions regarding FP in nature: low heterozygosity could instead reflect, for example, a long history of inbreeding. My reaction to the data is also that the % heterozygosity distribution for many of the species looks continuous rather than the bimodality one might expect under FP vs. sexual reproduction.

Significance

General assessment: strengths and limitations. The paper's strengths include the combination of data from lab and natural populations, the characterization of an unexpected means of achieving FP, with dramatic genetic consequences, and the data suggesting that this type of FP is fairly common and occurs even in the context of mating.

Audience: The biological questions of relevance to these discoveries are of broad interest, and the paper is likely to garner some attention from the life sciences community as whole and the popular press.

Advance: These data fill an important knowledge gap regarding the mechanisms potentially driving FP in vertebrates, how often FP is likely to occur, and its genetic consequences. The discoveries are potentially conceptual/fundamental, though the extent to which they are ground breaking is not clear in the absence of functional characterization of how FP occurs as well as the need for more rigorous comparisons and replication that I outlined above.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Here Ho et al. provide strong molecular evidence for the production of facultatively parthenogenetic whiptail lizards, through a gametic duplication. As evidenced through multiple routes, including microsatellites, WGS, RADseq, and RBC ploidy, and lines of evidence from multiple specimens, this study is timely in furthering our understanding of the mechanisms underlying FP. The fundings are conclusive.

That said, I have several comments that should be addressed prior to publication. The introduction which addresses FP in other systems fails to cite several key studies that provide strongly molecular support for terminal fusion automixis. Similarly, the study pushes the idea that this is an adaptive trait, however without proving that the parthenogens can themselves reproduce, this isa moot point at this stage.

That said, my comments are minor. I found this to be an excellent study, well written, comprehensive in methodology, and one that I strongly advocate for publication.

Major comments: None.

Minor Comments: Should be addressed.

• Line 36 - However, data that supports terminal fusion are no longer restricted to microsat data. Studies utilizing RADseq and whole-genome sequencing in snakes and crocodiles have now provided further evidence supporting terminal fusion.

See: Booth et al. 2023. Discovery of facultative parthenogenesis in a new world crocodile. Biology Letters. 19, 20230129.

Card et al. 2021. Genome-wide data implicate terminal fusion automixis in king cobra facultative parthenogenesis. Scientific Reports. 11, 1-9

Allen et al. 2018. Molecular evidence for the first records of facultative parthenogenesis in elapid snakes. R. Soc. Open. Sci. 5, 171901.

• Ln 42 - Evidence suggesting that isolation from males was not a pre-requisite for FP has previously been reported in snakes.

See: Booth et al. 2011. Evidence for viable, non-clonal but fatherless Boa constrictors. Biology Letters. 7, 253-256.

Booth et al. Facultative parthenogenesis discovered in wild vertebrates. Biology Letters. 8, 983-985.

Booth et al. 2014. New insights on facultative parthenogenesis in pythons. Biol J Linn Soc. 112, 461-468.

• Ln 48 - Is this really an argument. While an immediate transition to homozygosity will purge some deleterious alleles, given the genome-wide nature of this, there will also conversely have been strong selection for mildly deleterious alleles.

• Ln 56 - I would recommend the inclusion of both Allen et al. 2018. R. Soc. Open Sci, and Card et al. 2021. Sci Reports, here, as they are members of the elapids, not represented in the other examples.

• Ln 60 - Recent studies have highlighted the significance of sperm storage in reptiles. For example, Levine et al. 2021. Exceptional long-term sperm storage by a female vertebrate. PLos ONE. 16(6).e0252049, describe the storage of sperm by a female rattlesnake for ~70 months, with two instances of its utilization to produce healthy offspring during that period. Clearly, molecular tools are providing both support for long-term sperm storage, and an understanding of its utilization.

• Ln 68 - American Crocodile would also be suitable to include here.

• Ln71 - The problem with this hypothesis is that parthenogens produced through FP tend to have very low viability. For example, Adams et al. 2023. Endangered Species Research, follow a cohort of sharks produced through FP and all survive. Similarly low levels of survival are reported across other systems for which FP was reported. More likely, FP is simply a neutral trait. The mother is not negatively impacted through producing parthenogens and can go on to produce sexual offspring. Few instances report successful reproduction of a parthenogen. See pers. Comm in Card et al. 2021. And Straube et al. 2016.

• Ln 79 - I doubt that there is a desperate need for this for conservation. However, I think there is a need to simply further our understanding of basic biological function, given that it is not uncommon, and is phylogenetically widespread in species lacking genomic imprinting.

• Ln 85 - It would be worth citing Card et al. 2021., here given that they used genome-wide ddRAD markers to show support for terminal fusion.

• Ln 91 - Better citations here are Card et al. 2021. Allen et al. 2018, and Booth et al. 2023, which all utilize either RADseq or WGS.

• Ln 95 - The conclusion of genome duplication here was supported only by a small number of microsatellite loci. As such, given that terminal fusion has been supported through genome-wide markers in other species of snakes and crocodiles, the conclusion of genome duplication is likely incorrect.

• Ln 96 - I would strongly disagree with this statement. Allen et al. 2018, Card et al. 2021, Booth et al. 2023, all provide evidence of heterozygous loci and thus support terminal fusion. While no species-specific chromosome level reference genome is available for any of these species, the fact that levels of heterozygosity are below 33% percent supports terminal fusion. Rates over 33% support central fusion, but have not been reported in any vertebrate to date. AS such, I would recommend the removal of this statement.

• Ln 121 - Recent work in Drosophila mercatorum and D. melanogaster suggest that three genes play a role in the activation of FP in unfertilized eggs. In this case, through the fusion of meiotic products. That said, it is plausible to assume that FP in these lizards has an underlying genomic mechanism that is not related to isolation from males. See Sperling et al. 2023. Current Biology. 33, P3545-P3560.E13.

• Ln 126 - While these data strongly support FP of the two unusual A. marmoratus appearing offspring, can long term sperm storage be ruled out. Either through captive history or allelic exclusion of other males in the group?

• Ln 171 - 191 - Given that the topic of this manuscript is the genomic mechanism underlying FP in this species, are these data necessary? These are not discussed later and as such I would recommend that they are moved supplemental material. Otherwise, they simply clutter that manuscript and detract from the key question. Indeed, they are important to show that the genome constructed is of high quality, but online Supp Mat is the place for that here.

• Ln 296 - Comparable estimates were made for parthenogenetic production in wild populations of two North American pitviper species. See Booth et al. 2012. Biology Letters.

• Ln 312 - Again, can this really be suggested? Above, the authors state that most FP animals that hatched had congenital defects, and a large number failed to hatch. This does not sound like strong support for generating individuals that counter the effects of population bottlenecks and inbreeding depression. The authors need to take this study further and monitor the long-term viability of the FP individuals that survive.

• Ln 348 - To be able to provide support for this, you need to track animals long term to understand their reproductive competence, and that of their offspring.

• Ln 358 - But, the caveat is that the parthenogens must themselves reproduce. This must me stated.

• Ln 359 - Note that FP can also fix mildly deleterious alleles. Only if it is strongly deleterious will it be lost.

• Ln 361 - See above comments.

Significance

Significance:

• While reports of parthenogenesis have been reported as far back as the early 1900's, it has only been over the last decade that reports are become common. Such that facultative parthenogenesis is no longer considered a rarity, but is recognized now as being relatively common and phylogenetically widespread in species that lack genomic imprinting - particularly reptiles, birds, and sharks. Reasons for this are both an increased understanding that the trait can occur, hence recognizing it as an alternative mechanism to long-term sperm storage, and the ease of using molecular approaches.

• The fundamental questions of recent times have been understanding the mechanisms driving FP. Recent papers utilizing whole genome sequencing and ddRADseq have provided support for terminal fusion automixis in snakes and sharks. Here, this study provides evidence of gametic duplication in whiptails, a mechanism with an alternative outcome in regards to the levels of retained heterozygosity. As such, this study compares to the recent work of Card et al. 2021 (Scientific Reports), and Booth et al. 2023 (Biology Letters), in providing substantive advances in the field.

• The audience for this will be broad. Parthenogenesis is a fascinating topic that attracts significant media attention. See the Altmetric score of recent papers on the topic, particularly Booth et al. 2023 (Altmetric score - ~3100). As such, the study will be of interest to both a broad readership, but will also be of great significance to a specialized group working on parthenogenesis. All round, an excellent paper that has promise to advance the field.

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Reply to the reviewers

We appreciate the thoughtful comments of the reviewers. We have revised the manuscript according to these comments as detailed below.

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

Efficient proteostasis in cells demands efficient clearing of damaged or misfolded proteins, and an important pathway involved in such clearance is the ubiquitin-proteasome pathway. In this system, proteins are tagged with ubiquitin to target them for degradation by the 26S proteasome complex. The conventional 26S proteasome complex consists of a core particle (CP or 20S proteasome) and one or two regulatory particles (RP, or 19S proteasome) to form the singly or doubly-capped proteasome, respectively. Proteasome assembly is a well-orchestrated process that requires proper stoichiometry of proteasome subunits and dedicated proteasome assembly chaperones. This is maintained by fine-tuning their transcriptional and translational regulation.

This manuscript elucidates an important aspect of how the different proteasome components are transcriptionally regulated upon denervation in mouse muscles for timely and efficiently assembling 26S proteasome. The authors present data that point out towards the model whereby a two-phase transcriptional program (early: day 3-7 and late: day 10-14) activates genes encoding proteasome subunits and assembly chaperones to boost an increase in proteasome content. This involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1) which were important for both early and late phase of the transcriptional program. Their roles were not redundant as loss of one transcription factor was sufficient to prevent induction of various proteasome genes in muscle after denervation.

In summary, the authors report a novel bi-phasic mechanism elevating proteasome production in vivo, which involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1).

Major points: 1) It is not clear why PAX4 and alpha-PAL(Nrf1) are both fully required for the transcriptional induction of some proteasome genes upon denervation (with good overlap), while only PAX4 is important for increased proteasome assembly. The authors speculate that this could be due to a stoichiometry problem but an alternative scenario where translation is increased upon alpha-PAL(Nrf1) inhibition would also be possible. This would explain why, for example, the induction of PSMC1 gene expression upon denervation is abolished upon alpha-PAL(Nrf1) inhibition (Fig. 5C) while the protein level is still increased (Fig. 6H). Is that also true for PSMD5 and Rpn9? Could it also be that the loss of function of alpha-PAL(Nrf1) is too detrimental for the muscle so that they induce an alternative stress response pathway increasing proteasome subunit translation?

We thank the reviewer for this comment. To better clarify this important point, we conducted further experiments to examine the differential effects between PAX4 vs. α-PALNRF1 on proteasome assembly chaperons (Fig. S4b). Our new data show that PAX4 promotes the induction of the assembly chaperone, PSMD5 (S5b) at 3 days after denervation (Fig. S4B). This induction is critical for the increase in PSMD5 protein levels because PAX4 knockout results in decreased PSMD5 protein levels at both 3 and 10 days after denervation (Fig. 4K). α-PALNRF1, however, does not affect the mRNA levels of this chaperone (Fig. S4A). This new result strengthens our conclusion that induced expression of assembly chaperones by PAX4 is key to raising proteasome levels after denervation.

We cannot rule out an indirect effect of α-PALNRF1 knock-down on protein synthesis, and therefore this potential alternative mechanism is now discussed in the text. It appears unlikely, however, that α-PALNRF1 knock-down is too detrimental to muscle as we do not find any evidence phenotypically for any type of stress or abnormalities.

2) Pax4 controls Rpt1-2 transcription and these two Rpt proteins form a pair. As Rpt4 is also regulated by Pax4, is Rpt5 also controlled by Pax4?

We believe the reviewer meant to request the data for Rpt4, because the data for Rpt5 was already included in original Fig. 4G-H. Therefore, we repeated the RT-PCR analysis of PAX4 KO mouse muscles for Rpt4 and now show that its induction requires PAX4 at 10 d after denervation, just when proteasome content is increased (Fig. 4G). At 3 d after denervation, Rpt4 induction is probably regulated by other transcription factors because its mRNA levels at this early phase were similar in muscles from WT and PAX4 KO mice (Fig. 4H). These data, strengthen our conclusions that coordinated functions of multiple transcription factors control proteasome gene expression in vivo. In future studies, we will investigate the specific mode of cooperation and mechanisms by which various transcription factors and co-factors collaborate to enhance the expression of proteasome genes in the early and delayed stages of gene expression within a living organism.

What about the assembly chaperone for these two pairs: PSMD5 and p27? It would be very interesting to know if there is a transcriptional coregulation based on proteasome assembly intermediates.

The referee raises an important point, which we also discuss in the text. We now present data showing that PAX4 promotes the induction of the assembly chaperon PSMD5 at 3 d after denervation (Fig. S4B), correlating nicely with the observed changes in protein levels of this chaperon (Fig. 4K). The expression of PSMD9 (p27) however, does not require neither PAX4 nor α-PALNRF1 (Fig. S4). Consequently, we conclude that PAX4 promotes proteasome biogenesis by promoting PSMD5 induction, and in the absence of α-PALNRF1 proteasome subunits can still efficiently assemble into the proteasomes (even though their expression is reduced), due to the induced expression and increased action of the assembly chaperone PSMD5. Our data highlight the intricacy in controlling proteasome levels, through transcriptional regulation of proteasome genes and assembly chaperones during muscle atrophy. We now further document and discuss the regulation of proteasome biogenesis by these two transcription factors in the text and Discussion (p.28).

3) Fig. 4J: PSMD5 and PSMD13 are not tested in Fig. 4A, G and H. This needs to be done if the authors want to draw the parallel mRNA-protein levels, as in their conclusion. Moreover, the protein levels seem to be much more induced than the mRNA levels, could that be due to increased translation? This could be discussed.

We accepted this thoughtful suggestion and now present the mRNA levels for PSMD5 and PSMD13 in Figs. 4A, G and H and Fig. S4. The new data does not change our conclusion that protein abundance largely correlate with the transcript levels (Figs. 2 and 4K).

The reviewer raises an important question that we hope to resolve in the future. As we point out in the revised Discussion section, “the substantial rise in protein levels compared to mRNA levels after denervation suggests potential increased protein translation due to PAX4 loss. Whether PAX4 regulates protein synthesis and thus can affect protein levels beyond gene expression are intriguing questions for future research”.

4) The conclusion is not correct in this sentence: "Moreover, analysis of innervated and 10 d denervated muscle homogenates from WT, alpha-PAL(Nrf1) KD or PAX4/alpha-PAL(Nrf1) KD mice by native gels and immunoblotting or LLVY-cleavage indicated that loss of both transcription factors is necessary to effectively block accumulation of active assembled proteasomes on denervation (Fig. 6H)". This is not correct, as the loss of PAX4 is sufficient to block accumulation of active assembled proteasomes on denervation (Fig. 4K). So, it could just be that alpha-PAL(Nrf1) KD has no effect on the induction of proteasome assembly after denervation and that all the effect of the double mutant is due to PAX4 loss. This needs to be corrected.

We thank the reviewer for this thoughtful comment. The text has been revised accordingly.

Minor points:

1) I would rephrase the sentence "baseline at 14 d after denervation and showed a sustained low mRNA levels until 28 d (Fig. 2A-F).", as the mRNA levels are still significantly higher that the basal levels for most proteasome genes. Same for the sentence: "RNA sequencing (RNA-Seq) analysis of TA muscles at 14 d after denervation indicated that expression of most proteasome genes is low at 14 d (Fig. S1)". Expression is low compared to what and not being induced doesn't mean they are low. This needs to be rephrased.

We revised the text accordingly and thank the reviewer for these suggestions.

2) Microscopy images need more explanation: define the green and red channel and what they are used for in the legend.

The legends have been updated as requested.

3) Columns have moved from the Table 2.

The tables have now been submitted as separate files.

4) Fig. S3: RT-PCR on NRF-1(NFE2L1) need to be performed to see the extent of inhibition by shRNA.

We thank the reviewer for this important comment. The data, which was added as new Fig. S3A, shows an efficient knockdown of NRF-1NFE2L1 with shNFE2L1.

5) In the sentence: "PAX4 maintaining subunit stoichiometry for increased proteasome assembly.", could it be due to the much higher levels of PSMB8, 9 and 10 immunoproteasome subunits upon alpha-PAL(Nrf1) KD (Fig. 6F)?

We addressed this aspect in Major Point #1, regarding the difference between PAX4 and α-PALNRF1; please see our response. As for the Reviewer’s comment concerning Fig. 6F, we think that the increased expression of PSMB 8, 9, and 10 in α-PALNRF1-KD compared to the double KD or PAX4 KO further suggests a distinct cooperative interaction between these transcription factors in promoting proteasome expression, assembly, and function, which we plan to thoroughly investigate in future separate studies. However, the increased expression of PSMB 8, 9, and 10 can affect the composition of the CP (by replacing their normal ounterpart), but not the RP assembly. CP and RP are known to assemble separately with their own dedicated chaperones; RP and CP then associate to complete the assembly of proteasome holoenzyme (RP-CP complex). Thus, it is unlikely that increased CP assembly alone would increase overall RP-CP assembly.

**Referees cross-commenting**

All other comments are relevant.

Reviewer #1 (Significance (Required)):

Overall, the work is impactful and timely, reporting the participation of a novel transcription factor, alpha-PAL(Nrf1), along with PAX4, in regulating the transcription of proteasome genes and the subsequent assembly of conventional proteasomes in mouse muscle upon denervation. One limitation is that alpha-PAL(Nrf1) kockdown is only inhibiting proteasome genes expression but proteasome assembly, the reason being still unknown. Most of the conclusions drawn in the manuscript are supported by the experimental data. Better understanding how proteasome homeostasis is regulated upon stressful conditions is an important fundamental aspect of proteasome biology. I would support publication of this manuscript providing the more specific concerns listed are addressed.

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

The main limitation of this study is that is based on a single model of muscle atrophy: that induced by cut of the sciatic nerve. Another one will nicely complement the findings as fasting atrophy or cancer cachexia model, to see if the two phase is recapitulated with regard to proteasome modulation.

The referee raises an interesting point, but as we explained throughout the manuscript, we did not use denervation in this study as a model for atrophy but rather as an in vivo model system to investigate mechanisms of protein degradation and proteasome homeostasis in a whole organism in vivo. The reason we selected denervation as an in vivo model for accelerated proteolysis is due to the gradual nature of muscle loss, which allows us to dissect the various phases of proteasome homeostasis effectively. Fasting, as an alternative model, is too rapid for addressing the specific questions that we asked in this study. In addition, in the rapid atrophy induced by fasting the primary physiological mechanism to increase protein degradation in vivo is believed to be through post-synthetic modification of proteasomes, rather than the production of new proteasomes (VerPlank et al., 2019). In future separate studies, we will thoroughly investigate whether the mechanisms discovered here are applicable to other types of atrophy (e.g. diabetes, aging, cancer). The obtained results will be published and fully discussed separately, in part because covering all types of atrophy within a single paper is impractical and goes beyond the scope of the current manuscript.

Another major concern is that the author do not measure over time during denervation atrophy the mRNA and protein content expression of the two transcription factors that they found crucial in the proteasome induction and assembly.

We agree with the reviewer that time course would strengthen our conclusions that the two transcription factors are important for proteasome gene induction and assembly. We have added these data showing that PAX4 (Fig. 4I) and α-PALNRF-1 (Fig. 6E) both accumulate in the nucleus at 7 d after denervation, just when proteasome content is maximal (Fig. 3A) and protein breakdown is accelerated (Cohen 2009; Volodin 2017; Aweida 2021). The mRNA levels of PAX4 were presented as original Fig. 4F and indicate that PAX4 is induced already at 3 d after denervation. We have added new RT-PCR data for α-PALNRF-1 showing that α-PALNRF-1 is induced at 7 d and 10 d after denervation (Fig. 6D).

Major and minor concerns are as follows:

Typos now and then are present all over the text, as holoemzyme shall be replaced with holoenzyme on page 9, on page 12 proteasome is misspelled on mid page, as well as cellls. By cotrast shall be corrected on page 19. References on page 22 shall be formatted.

We have corrected the typographical errors.

• reference 29 on page 7 seems out of context together with the sentences it is coupled with.

The reference is appropriately located within the text in terms of context, and precisely aligns with the sentence to which it is associated. Reference 29 (Boos 2019) describes a cellular state in which all proteasome genes rise simultaneously.

• muscle electroporation of plasmid shall be replaced by AAV9 injection that causes less inflammation and more expressing fibers

We do not understand and see no basis for the referee’s assertion that the “muscle electroporation of plasmid shall be replaced by AAV9 injection”. On the contrary, the electroporation methodology is widely used by many labs because of its many advantages. This in vivo gene transfection approach is extremely useful to study transient gene (or shRNA) effects in adult muscles, while avoiding the developmental effects of genes (or shRNA) that are often seen in transgenic or knockout animals (e.g., the inducible knockout of α-PALNRF-1 caused lethality, see Fig. 6B-C).

In addition, the electroporation technique offers great advantages from its speed and major cost savings. We have been using it routinely in our lab for in vivo studies, and articles using it from many laboratories worldwide have appeared in all major journals, e.g. see our papers in Nature Communications, J Cell Biol, PNAS, EMBO rep, and papers from late Alfred Goldberg (Harvard), Marco Sandri (Padova, Italy), Jeff Brault (Indiana Univ.) and others. In all studies included in this manuscript that involve electroporation, contrary to the reviewer’s impression, there was no damage or inflammation to the muscles, and we routinely examined histological sections. Finally, for our studies, we always use muscles that are at least ~70% transfected, which has proven adequate for observing gene effects in mouse muscle. In each experiment, transfected muscles are always compared and analyzed in parallel to control muscles (transfected with scrambled shLacz control). In fact, the validity of the in vivo electroporation technique is further confirmed herein by our investigations of transgenic inducible knock-down mice, showing similar effects on proteasome gene expression.

• the shGankyrin data shall be complemented with overexpression of the same chaperone to see the effects of proteasome expression and assembly.

We understand the reviewer’s concern but do not believe that such an experiment is necessary since it is well known and there is already extensive evidence in the literature showing that the chaperon Gankyrin is essential for proteasome assembly (Kaneko et al. Cell 137, 914–925, May 29, 2009 (DOI 10.1016/j.cell.2009.05.008). Thus, various Gankyrin mutants have often been used as an inactive control for proteasome assembly in vitro and in vivo (Kaneko et al. Cell 137, 914–925, May 29, 2009 (DOI 10.1016/j.cell.2009.05.008). In fact, Gankyrin’s known function in ensuring not only the proper subunit composition, but also proper conformation of the proteasome holoenzyme (Lu et al., Mol Cell. 2017 Jul 20;67(2):322-333.e6).

• another important transcription factor driving MuRF1 expression is Twist and it is totally ignored in the discussion, please add it.

We regret this oversight. We did not mean to slight any authors, although our major new discoveries and focus is on proteasome genes and not MuRF1. However, to satisfy the reviewer, we now discuss in the text Twist and other transcription factors (including SMAD2/3, glucocorticoid receptors and NFkB) capable of inducing the major atrophy-related genes (among them MuRF1).

• WB in Fig 2 shall be complemented by one in the Supp with more replicates per timepoint

We accepted this thoughtful suggestion and now present blots from additional normal and atrophying denervated mouse muscle samples as new Fig. S1B. This approach, however, does not change any of our conclusions.

• please justify why only PSMD10 (gankyrin) has been silenced and not any of the others (POMP, PSMD5, PSMD9)

We silenced PSMD10 (Gankyrin) as a representative RP assembly chaperone, since it is better characterized than the other RP assembly chaperones (PSMD5 and PSMD9). We kept POMP (a CP assembly chaperone) intact. Since the formation of one proteasome holoenzyme (RP2-CP) requires two RPs and one CP, increasing proteasome assembly is expected to be more demanding for RP assembly than CP. This led us to predict that disrupting RP assembly should be sufficient to block the induced proteasome assembly. This prediction is supported by our data (Fig. 3), and this justification was also added to the revised text to enhance clarity.

The originality is limited by the fact that Pax4 was already shown to have a role in muscle atrophy and drives the expression of p97 by the same authors. I would be curious to see if treatments in vitro know to induce the proteasome as starvation etc acts through the biphase mechanism showed in this paper, to understand how extendable to other kinds of atrophy is.

We respectfully disagree that the originally of the present findings is limited, because previously we validated a single proteasome subunit (Rpt1) as a target gene for PAX4 (Volodin 2017), and here we discover novel global coordination of proteasome gene expression by multiple transcription factors.

As we mention above, muscle denervation was used here as an in vivo model system of catabolic conditions. Unlike prior reports that were limited to cultured cells, our studies focus on the physiological setting in vivo to reveal mechanisms of proteasome homeostasis. In any case, regulation of proteasome gene expression by multiple transcription factors in other types of atrophy has not been investigated but is possible because common transcriptional adaptations activate protein breakdown in different types of muscle atrophy, including a coordinated induction of numerous components of the ubiquitin proteasome system (Jagoe 2002; Lecker 2004; Gomes 2001). In future independent research, we intend to investigate if the two-phase mechanism reported here can in fact be generalized to other atrophy (or stress) conditions.

Reviewer #2 (Significance (Required)):

The authors Gilda and co-workers made a great attempt to dissect the induction of proteasome activity during denervation muscle atrophy and discovered a two-phase process which involves two transcription factors Pax4 and NRF1. The manuscript is clearly written and the experiments fully delineated.

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

Using denervated mouse muscle as a model, Gilda et al. demonstrated that a two-step transcriptional program operates in the process of muscle atrophy after denervation and that proteasome expression-induced enhancement of protein degradation is important. Gilda et al. clarified that the transcription factors PAX4 and PAL/NRF-1 act on this proteasome expression induction and that the induction of these transcription factors and the expression induction of the proteasome gene cluster after denervation are necessary for muscle atrophy using an in vivo mouse model. The experiments were logically designed, and the results presented are considered clear and reliable. However, some of the descriptions in the text lack accuracy and courtesy, and some experiments require additional data to support and strengthen the author's claims. In particular, it is unclear whether PAX4, FOXO3, and NRF-1 work together or whether they have distinct functions. Although the authors claim that there are two stages of proteasome expression induction after denervation, this remains unclear. The authors should clarify the differences in target sequence or target genes and the substitutability of each transcription factor.

Major comments: 1: In Figure 3A, the results of the immunoblot of SDS-PAGE against 20S proteasome subunits should also be shown to confirm the increase in proteasome activity and amount.

We would like to clarify this aspect. We show the increased levels of proteasome holoenzyme complex (RP2-CP) by immunoblotting of the native gel, rather than SDS-PAGE gel. This is because the blots of the native gel can assess the levels of the actual proteasome complex, not simply subunit levels in their denatured state as in SDS-PAGE; SDS-PAGE cannot distinguish between free subunits and ones that are incorporated into the proteasome.

If proteasome activity was increased due to some other mechanisms, proteasome levels would remain relatively constant, while proteasome activity would have increased. However, this is not the case here since our data demonstrates that both RP2-CP activities and levels peak at day 7. Furthermore, the in-gel peptidase assay (Fig. 3A panel b) directly tests the 20S CP activity within the proteasome holoenzyme (RP2-CP complex) using the fluorogenic model substrate, LLVY-AMC. The 20S CP is activated for substrate degradation, only upon its association with RP (RP2-CP complex), since RP opens the substrate entry gate of the 20S. Free 20S itself is inactive, as its gate for substrate entry is closed; for this reason, free 20S can be detected, only after its substrate entry gate is artificially opened by SDS (see free 20S in panel b, but not in panel a).

2: In Figure 3, the reviewer assumed the conflict between the results of peptidase activity and SDS-PAGE in 14d. Therefore, quantification and statistical analysis should be performed on the results of proteasome peptidase activity and immunoblots to clarify the relationships between proteasome activity and amounts. Immunoblotting against ubiquitin is also needed to confirm the requirement and efficiency of proteasome induction.

As the reviewer pointed out, it might seem discrepant that peptidase activity at 14 d denervation is lower than its peak at 7d (Fig. 3A, panel a), but SDS-PAGE signal for proteasome subunits seems still high (Fig. 3A, panel d, Rpn2). SDS-PAGE detects total cellular content of proteasome subunits (free subunits as well as ones assembled within proteasomes). However, at any given moment, these subunits are not only in the proteasome holoenzyme complex, but also in different assembly intermediates. When proteasome subunits are transcriptionally induced as in this study, proteasome assembly process is also increased. However, proteasome assembly is a multi-step process, and the fold-induction for each specific subunit is different (Fig. 2A-B). This means that the rate of a certain assembly step would be differently affected for a given subunit, depending on their fold-induction. For this reason, some subunits seem to exist at a high level at 14d (e.g. Fig. 3A, panel d, Rpn2), but they are not yet incorporated into the proteasome complex, because they might be still undergoing assembly process.

As for the ubiquitin blot, it can be a good indicator for proteasome activity, when proteasome activity is decreased than normal. In such situations, ubiquitinated proteins accumulate (i.e. their signals increase as compared to control), due to their deficient degradation. However, our present study pertains to the opposite situation, where proteasome activity is increased in degrading ubiquitinated proteins. In normal cells, ubiquitinated proteins are hardly detectable due to their rapid degradation. Thus, when proteasome activity is greater than normal, ubiquitinated protein levels will be further decreased than normal. Data become unreliable when the signals are below the detection threshold. For this reason, we provided functional readouts involving the number of muscle fibers (for example, Fig. 3D).

3: In Figure 3C, the sample labels of shGankyrin and shLacZ are repeated. Would it be mislabeled?　In addition, NATIVE PAGE immunoblot analysis against Gankyrin and proteasome subunits are needed to prove the knockdown efficiency and to reveal the assembly defect of proteasome by Gankyrin knockdown.

To present our findings more clearly, we show one of each sample in the revised figure, rather than the duplicates as in the previous figure (Fig. 3C). We also included the immunoblot data to show that Gankyrin knockdown disrupts proteasome assembly, as seen by the reduced proteasome complex activity and level (Fig. 3C, panels a, b, c, lane 3, see RP2-CP). In Gankyrin knockdown samples, proteasome holoenzyme complex exhibited smeary appearance (Fig. 3C, panel c, see bracketed region in lane 3), as opposed to a discrete band in the controls (lanes 1, 2). This smeary appearance reflects more heterogeneous proteasome populations, due to defects in their composition and/or conformation. This is in line with Gankyrin’s known function in ensuring not only the proper subunit composition, but also proper conformation of the proteasome holoenzyme (Lu et al., Mol Cell. 2017 Jul 20;67(2):322-333.e6).

4: In Figures 4A, 4G, 4H, 4J, and 4K, the results of shPAX4 against innervated muscle should be shown to estimate the contribution of PAX4 in steady-state conditions. To clarify the innervated muscle-specific function of PAX4, histological analysis and quantification of proteasome gene expression in multiple organs in PAX4 KO mice are needed.

The reviewer raises an interesting point, but as we explained above, we concentrate here on the major new discovery that multiple transcription factors increase proteasome content in a catabolic condition in vivo, correlating directly with the accelerated protein loss. Regulation of the basal levels of proteasome in normal conditions in various types of cells and tissues is certainly an important issue meriting in depth study and will be the subject for future studies, but it is beyond the scope of this lengthy paper. This point is now discussed in the revised text.

The tissue distribution of PAX4 and the detailed description of the phenotype of KO mice are also needed to understand and evaluate the role of PAX4 in muscle.

We added the requested data about PAX4 distribution as Fig. 4I. These data shows that PAX4 accumulates in the nucleus already at 3 d after denervation. Furthermore, we are happy to add further information about the knock-out mouse model. The requested information and a detailed description of how PAX4 KO mice were generated were added to the text. The PAX4 KO mice showed no abnormalities and did not appear in any way different from the wild type littermates.

5: In Figure 4C, immunoblot analysis against PAX4 is essential to confirm the PAX4 protein knockout.

We agree and representative blots were added to Fig. 4C.

6: In Figure 5, peptidase activity and immunoblotting in NATIVE PAGE are needed to reveal the contribution of FOXO3 and NRF-1 in denervated muscle as shown in Figure 4.

The requested data for FOXO3 using FOXO3 dominant negative (as in Fig. 5A-B) were added as new Fig. 5C-D, showing no effect on proteasome content by FOXO3 inhibition. These new data are consistent with our findings that the expression of only two proteasome subunit genes was affected by FOXO3 inhibition at 10 d after denervation (Fig. 5B). The data for α-PALNRF-1 and the effects of its knockdown on proteasome content and activity were shown as original Fig. 6H (now Fig. 6J).

The expression of FOXO3 and NRF-1 should also be shown by RT-PCR and immunoblotting as shown in Figure 4.

We thank the reviewer for this thoughtful suggestion, and as requested, we now show representative blots of transfected muscles to support the graphical data (Figs. 5C-F). These data confirm the efficient expression of HA-FOXO3ΔC or FLAG-α-PALNRF-1 dominant negative inhibitors in transfected muscles. It is important to note that these inhibitors are mutant forms designed to interfere with the normal function of the wild-type endogenous FOXO3 or α-PALNRF-1 proteins, without affecting their transcript levels. Given this mechanism, we believe that Western blotting is a more appropriate technique for assessing their impact, as it provides direct insights into protein expression. In the revised main text and methods, we have now clarified this point.

Similar to previous comments, the expression of the dominant negative form of Foxo3 and NRF-1 should be performed in innervated muscles to reveal the significance and specificity of Foxo3 and NRF-1 function in denervated muscles.

As mentioned above, regulation of the normal basal levels of proteasomes is certainly an important issue meriting in depth study and will be the subject for future studies, but it is beyond the scope of this lengthy paper, which focuses on the mechanisms increasing protein content in catabolic conditions in vivo. With respect to FOXOs, there is a large literature on its regulation and roles in normal muscle (please see papers by late Alfred L Goldberg, Marco Sandri and others). Under normal conditions FOXO3 is largely inactive via phosphorylation by insulin-PI3K-AKT signaling (Stitt 2004; Latres 2005; Zhao 2007).

7: In Figure 6D, the list of genes should be served especially about 27 genes and 69 genes that show common features between NRF-1 KD and PAX4 KO.

The requested data is now presented as new Table 4.

8: In Figure 6F, the list of genes that change expression in PAX4 and NRF-1 KD mice is needed.

We agree and the requested data has now been added to table 5.

9: In Figure 6H, immunoblotting against ubiquitin is needed to evaluate the contribution of proteasome induction to protein degradation.

We clarified this aspect in the Major Point #2. Please see our response.

10: This study lacks the detailed mechanisms by which PAX4, Foxo3, and NRF-1 regulate the expression of proteasome genes. The contribution of these transcription factors is revealed by experiments, but the specific sequence that these transcription factors bind and how transcription factors are induced in denervated muscles is not clarified. As shown in the figures, the ChIP assay provides convincing results, but the detailed sequence or map of the promoter region of proteasome genes must be shown in the figures to clarify the target sequences of NFE2L1 and PAX4, FOXO3, and NRF-1. In addition, the luciferase assay would support the results of the ChIP assay.

Again, the reviewer raises an important question that we plan to resolve in the future. As mentioned, our findings strongly suggest a novel coordinated mechanism involving multiple transcription factors that control proteasome content in catabolic states in vivo. The enclosed revised manuscript primarily focuses on elucidating the contributions of individual transcription factors (α-PALNRF-1, PAX4, NRF-1NFE2L1 and FOXO3) to the induction of proteasome genes, revealing a significant overlap in genes regulated by multiple transcription factors. The specific mode of cooperation among these and other transcription factors and cofactors is certainly an important question for future studies, but it is beyond the scope of this lengthy paper. In the revised text we have now clarified this point (page 27). In addition, we agree that clarifying how the transcription factors are induced in denervated muscles merits some considerations and a paragraph was added to the Discussion (page 26) concerning possible mechanisms. For example, it is possible that the transcription factor STAT3 is involved in PAX4 induction because, based on previous microarray and ChIP data in cultured NIH3T3 cells, PAX4 was identified as a target gene of STAT3 (Snyder et al., 2008), and STAT3 becomes activated after denervation (Madaro et al., 2018).

We are delighted that the reviewer found the results obtained through the ChIP assay convincing. Given the extensive scope of our investigation and rigorous analyses of dozens of genes, it is not feasible to generate luciferase-encoding plasmids for all of them. However, in response to the reviewer's request, we have carried out predictions of the binding sites of the 4 transcription factors within the minimal promoter regions (300 up- and 1000 down-stream to TSS) of the 64 proteasome sequences. The predicted binding sites are now listed in Table 2A-D. These new data further support our key findings that multiple transcription factors control proteasome gene expression in a catabolic physiological state in vivo.

11: The results of the loss of transcription factors are well done, but the authors should also try to estimate the effect of overexpression of transcription factors in muscle. If the overexpressed transcription factors cause proteasome induction and muscle fiber mass reduction, these results strongly support the importance of transcription factor-mediated proteasome enhancement.

We understand the reviewer’s comment but do not believe that such an experiment is necessary to support our key findings about proteasome gene induction by multiple transcription factors in vivo. In fact, we have specifically refrained from pursuing overexpression studies in this context due to the apparent coordination and some potential interdependence between the functions of PAX4 and α-PALNRF-1 transcription factors in inducing proteasome genes. Manipulating one specific gene through overexpression could potentially disrupt this delicate coordination and yield misleading results.

In addition, there are several limitations of gene overexpression in mouse muscle, as it may not be as efficient and does not represent physiological conditions. Therefore, to validate gene functions in a physiological setting in vivo, we generated transgenic animals with the gene of interest specifically knocked-out or knocked-down. Utilizing transgenic mice lacking the gene of interest, though time-consuming, is a widely accepted and common approach that proves to be the most suitable method for specifically demonstrating the involvement of a particular gene in a physiological process, enabling a targeted and controlled investigation of its role and providing valuable insights into its contribution to the observed effects.

Minor comments:

12: The authors should describe the inducible KO mice more carefully and correctly. In the Results section on P12, the description of "whole body Cre+ mice" confuses the readers in understanding the mechanism of inducible Cre-mediated KO.

We agree and have added the information requested about the KO mice to the main text and a detailed description in the methods section.

13: In Figures 6B and 6C, the number of mice and the meaning of the asterisk should be described correctly. Is it statistically significant?

We agree. By accident the number of mice and sign for statistical significance were omitted during processing. The correct sign was added to Fig. 6B-C, and the number of mice used, and the meaning of asterisks were added to the corresponding legend. N=10 mice per condition. **, P

14: There is no description of Figure 6E in the manuscript. The authors should include it.

In the original version of this paper, we refer to Fig. 6E in the text on pages 21 and 25. Also, the presented illustration is fully described in the corresponding legend.

Reviewer #3 (Significance (Required)):

This paper clarified a novel mechanism of proteasome induction by transcription factors in denervated muscles other than Nrf1 (NFE2L1), which has been shown to contribute to the induction of proteasome gene expression in cultured cells. This is an important paper for expanding the understanding of the field. It is also important because it has demonstrated the potential for new therapeutic targets in diseases such as type 2 diabetes and cancer.

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

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Referee #3

Evidence, reproducibility and clarity

Using denervated mouse muscle as a model, Gilda et al. demonstrated that a two-step transcriptional program operates in the process of muscle atrophy after denervation and that proteasome expression-induced enhancement of protein degradation is important. Gilda et al. clarified that the transcription factors PAX4 and PAL/NRF-1 act on this proteasome expression induction and that the induction of these transcription factors and the expression induction of the proteasome gene cluster after denervation are necessary for muscle atrophy using an in vivo mouse model. The experiments were logically designed, and the results presented are considered clear and reliable. However, some of the descriptions in the text lack accuracy and courtesy, and some experiments require additional data to support and strengthen the author's claims. In particular, it is unclear whether PAX4, FOXO3, and NRF-1 work together or whether they have distinct functions. Although the authors claim that there are two stages of proteasome expression induction after denervation, this remains unclear. The authors should clarify the differences in target sequence or target genes and the substitutability of each transcription factor.

Major comments:

1. In Figure 3A, the results of the immunoblot of SDS-PAGE against 20S proteasome subunits should also be shown to confirm the increase in proteasome activity and amount.
2. In Figure 3, the reviewer assumed the conflict between the results of peptidase activity and SDS-PAGE in 14d. Therefore, quantification and statistical analysis should be performed on the results of proteasome peptidase activity and immunoblots to clarify the relationships between proteasome activity and amounts. Immunoblotting against ubiquitin is also needed to confirm the requirement and efficiency of proteasome induction.
3. In Figure 3C, the sample labels of shGankyrin and shLacZ are repeated. Would it be mislabeled?　In addition, NATIVE PAGE immunoblot analysis against Gankyrin and proteasome subunits are needed to prove the knockdown efficiency and to reveal the assembly defect of proteasome by Gankyrin knockdown.
4. In Figures 4A, 4G, 4H, 4J, and 4K, the results of shPAX4 against innervated muscle should be shown to estimate the contribution of PAX4 in steady-state conditions. To clarify the innervated muscle-specific function of PAX4, histological analysis and quantification of proteasome gene expression in multiple organs in PAX4 KO mice are needed. The tissue distribution of PAX4 and the detailed description of the phenotype of KO mice are also needed to understand and evaluate the role of PAX4 in muscle.
5. In Figure 4C, immunoblot analysis against PAX4 is essential to confirm the PAX4 protein knockout.
6. In Figure 5, peptidase activity and immunoblotting in NATIVE PAGE are needed to reveal the contribution of FOXO3 and NRF-1 in denervated muscle as shown in Figure 4. The expression of FOXO3 and NRF-1 should also be shown by RT-PCR and immunoblotting as shown in Figure 4. Similar to previous comments, the expression of the dominant negative form of Foxo3 and NRF-1 should be performed in innervated muscles to reveal the significance and specificity of Foxo3 and NRF-1 function in denervated muscles.
7. In Figure 6D, the list of genes should be served especially about 27 genes and 69 genes that show common features between NRF-1 KD and PAX4 KO.
8. In Figure 6F, the list of genes that change expression in PAX4 and NRF-1 KD mice is needed.
9. In Figure 6H, immunoblotting against ubiquitin is needed to evaluate the contribution of proteasome induction to protein degradation.
10. This study lacks the detailed mechanisms by which PAX4, Foxo3, and NRF-1 regulate the expression of proteasome genes. The contribution of these transcription factors is revealed by experiments, but the specific sequence that these transcription factors bind and how transcription factors are induced in denervated muscles is not clarified. As shown in the figures, the ChIP assay provides convincing results, but the detailed sequence or map of the promoter region of proteasome genes must be shown in the figures to clarify the target sequences of NFE2L1 and PAX4, FOXO3, and NRF-1. In addition, the luciferase assay would support the results of the ChIP assay.
11. The results of the loss of transcription factors are well done, but the authors should also try to estimate the effect of overexpression of transcription factors in muscle. If the overexpressed transcription factors cause proteasome induction and muscle fiber mass reduction, these results strongly support the importance of transcription factor-mediated proteasome enhancement.

Minor comments:

1. The authors should describe the inducible KO mice more carefully and correctly. In the Results section on P12, the description of "whole body Cre+ mice" confuses the readers in understanding the mechanism of inducible Cre-mediated KO.
2. In Figures 6B and 6C, the number of mice and the meaning of the asterisk should be described correctly. Is it statistically significant?
3. There is no description of Figure 6E in the manuscript. The authors should include it.

Significance

This paper clarified a novel mechanism of proteasome induction by transcription factors in denervated muscles other than Nrf1 (NFE2L1), which has been shown to contribute to the induction of proteasome gene expression in cultured cells. This is an important paper for expanding the understanding of the field. It is also important because it has demonstrated the potential for new therapeutic targets in diseases such as type 2 diabetes and cancer.

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

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Referee #2

Evidence, reproducibility and clarity

The main limitation of this study is that is based on a single model of muscle atrophy: that induced by cut of the sciatic nerve. Another one will nicely complement the findings as fasting atrophy or cancer cachexia model, to see if the two phase is recapitulated with regard to proteasome modulation.

Another major concern is that the author do not measure over time during denervation atrophy the mRNA and protein content expression of the two transcription factors that they found crucial in the proteasome induction and assembly.

Major and minor concerns are as follows:

Typos now and then are present all over the text, as holoemzyme shall be replaced with holoenzyme on page 9, on page 12 proteasome is misspelled on mid page, as well as cellls. By cotrast shall be corrected on page 19. References on page 22 shall be formatted.

• reference 29 on page 7 seems out of context together with the sentences it is coupled with.
• muscle electroporation of plasmid shall be replaced by AAV9 injection that causes less inflammation and more expressing fibers
• the shGankyrin data shall be complemented with overexpression of the same chaperone to see the effects of proteasome expression and assembly
• another important transcription factor driving MuRF1 expression is Twist and it is totally ignored in the discussion, please add it.
• WB in Fig 2 shall be complemented by one in the Supp with more replicates per timepoint
• please justify why only PSMD10 (gankyrin) has been silenced and not any of the others (POMP, PSMD5, PSMD9)

The originality is limited by the fact that Pax4 was already shown to have a role in muscle atrophy and drives the expression of p97 by the same authors. I would be curious to see if treatments in vitro know to induce the proteasome as starvation etc acts through the biphase mechanism showed in this paper, to understand how extendable to other kinds of atrophy is.

Significance

The authors Gilda and co-workers made a great attempt to dissect the induction of proteasome activity during denervation muscle atrophy and discovered a two-phase process which involves two transcription factors Pax4 and NRF1. The manuscript is clearly written and the experiments fully delineated.

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

Learn more at Review Commons

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Referee #1

Evidence, reproducibility and clarity

Efficient proteostasis in cells demands efficient clearing of damaged or misfolded proteins, and an important pathway involved in such clearance is the ubiquitin-proteasome pathway. In this system, proteins are tagged with ubiquitin to target them for degradation by the 26S proteasome complex. The conventional 26S proteasome complex consists of a core particle (CP or 20S proteasome) and one or two regulatory particles (RP, or 19S proteasome) to form the singly or doubly-capped proteasome, respectively. Proteasome assembly is a well-orchestrated process that requires proper stoichiometry of proteasome subunits and dedicated proteasome assembly chaperones. This is maintained by fine-tuning their transcriptional and translational regulation.

This manuscript elucidates an important aspect of how the different proteasome components are transcriptionally regulated upon denervation in mouse muscles for timely and efficiently assembling 26S proteasome. The authors present data that point out towards the model whereby a two-phase transcriptional program (early: day 3-7 and late: day 10-14) activates genes encoding proteasome subunits and assembly chaperones to boost an increase in proteasome content. This involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1) which were important for both early and late phase of the transcriptional program. Their roles were not redundant as loss of one transcription factor was sufficient to prevent induction of various proteasome genes in muscle after denervation.

In summary, the authors report a novel bi-phasic mechanism elevating proteasome production in vivo, which involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1).

Major points:

1. It is not clear why PAX4 and alpha-PAL(Nrf1) are both fully required for the transcriptional induction of some proteasome genes upon denervation (with good overlap), while only PAX4 is important for increased proteasome assembly. The authors speculate that this could be due to a stoichiometry problem but an alternative scenario where translation is increased upon alpha-PAL(Nrf1) inhibition would also be possible. This would explain why, for example, the induction of PSMC1 gene expression upon denervation is abolished upon alpha-PAL(Nrf1) inhibition (Fig. 5C) while the protein level is still increased (Fig. 6H). Is that also true for PSMD5 and Rpn9? Could it also be that the loss of function of alpha-PAL(Nrf1) is too detrimental for the muscle so that they induce an alternative stress response pathway increasing proteasome subunit translation?
2. Pax4 controls Rpt1-2 transcription and these two Rpt proteins form a pair. As Rpt4 is also regulated by Pax4, is Rpt5 also controlled by Pax4? What about the assembly chaperone for these two pairs: PSMD5 and p27? It would be very interesting to know if there is a transcriptional coregulation based on proteasome assembly intermediates.
3. Fig. 4J: PSMD5 and PSMD13 are not tested in Fig. 4A, G and H. This needs to be done if the authors want to draw the parallel mRNA-protein levels, as in their conclusion. Moreover, the protein levels seem to be much more induced than the mRNA levels, could that be due to increased translation? This could be discussed.
4. The conclusion is not correct in this sentence: "Moreover, analysis of innervated and 10 d denervated muscle homogenates from WT, alpha-PAL(Nrf1) KD or PAX4/alpha-PAL(Nrf1) KD mice by native gels and immunoblotting or LLVY-cleavage indicated that loss of both transcription factors is necessary to effectively block accumulation of active assembled proteasomes on denervation (Fig. 6H)". This is not correct, as the loss of PAX4 is sufficient to block accumulation of active assembled proteasomes on denervation (Fig. 4K). So, it could just be that alpha-PAL(Nrf1) KD has no effect on the induction of proteasome assembly after denervation and that all the effect of the double mutant is due to PAX4 loss. This needs to be corrected.

Minor points:

1. I would rephrase the sentence "baseline at 14 d after denervation and showed a sustained low mRNA levels until 28 d (Fig. 2A-F).", as the mRNA levels are still significantly higher that the basal levels for most proteasome genes. Same for the sentence: "RNA sequencing (RNA-Seq) analysis of TA muscles at 14 d after denervation indicated that expression of most proteasome genes is low at 14 d (Fig. S1)". Expression is low compared to what and not being induced doesn't mean they are low. This needs to be rephrased.
2. Microscopy images need more explanation: define the green and red channel and what they are used for in the legend.
3. Columns have moved from the Table 2.
4. Fig. S3: RT-PCR on NRF-1(NFE2L1) need to be performed to see the extent of inhibition by shRNA.
5. In the sentence: "PAX4 maintaining subunit stoichiometry for increased proteasome assembly.", could it be due to the much higher levels of PSMB8, 9 and 10 immunoproteasome subunits upon alpha-PAL(Nrf1) KD (Fig. 6F)?

Referees cross-commenting

All other comments are relevant.

Significance

Overall, the work is impactful and timely, reporting the participation of a novel transcription factor, alpha-PAL(Nrf1), along with PAX4, in regulating the transcription of proteasome genes and the subsequent assembly of conventional proteasomes in mouse muscle upon denervation. One limitation is that alpha-PAL(Nrf1) kockdown is only inhibiting proteasome genes expression but proteasome assembly, the reason being still unknown. Most of the conclusions drawn in the manuscript are supported by the experimental data. Better understanding how proteasome homeostasis is regulated upon stressful conditions is an important fundamental aspect of proteasome biology. I would support publication of this manuscript providing the more specific concerns listed are addressed.

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Reply to the reviewers

Manuscript number: RC-2023-02199 Corresponding author(s): Cornelis, Calkhoven

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.

• *

We would like to thank the reviewers for their comments that will help to improve the manuscript and the editor(s) for taking care of the process.

Text revisions and corrections in the manuscript are in red font.

To keep oversight, see below the distribution of the comments and our replies per category:

Reviewer 1

Major comment 1: see 2. planned revisions

Major comment 2: see 3. already incorporated

Major comment 3: see 2. planned revisions

Major comment 4: see 4. prefer not to carry out

Minor comment 1: see 3. already incorporated

Minor comment 2: see 4. prefer not to carry out

Reviewer 2

Major comment 1: see 4. prefer not to carry out

Major comment 2: see 4. prefer not to carry out

Major comment 3: see 3. already incorporated

Major comment 4: see 4. prefer not to carry out

Minor comment 1: see 3. already incorporated

Minor comment 2: see 3. already incorporated

Minor comment 3: see 3. already incorporated

Minor comment 4: see 3. already incorporated

Minor comment 5: see 3. already incorporated

Reviewer 3

Major comment 1: see 3. already incorporated

Major comment 2: see 3. already incorporated

Major comment 3: see 4. prefer not to carry out

Minor comment 1: see 4. prefer not to carry out

Minor comment 2: see 4. prefer not to carry out

Significance comments by the three reviewers

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

*Major comment 1: The reviewer is not convinced that FTO-CEBPB regulation is direct (data Figure 5). *

Reply: We offer to perform immunoprecipitation of FTO from wt cells to examine interaction with CEBPB mRNA to resolve this. HPRT mRNA will be used as negative control (like in the MeRIP-RT-qPCR experiments in the manuscript).

Major comment 3: FTO effect on proliferation and migration in less aggressive / normal breast epithelial cells (data Figure 1) (reviewer writes “cancer cells” and “MCF-10A”, but these are untransformed epithelial cells).

Reply: We offer to perform proliferation and migration assays in MCF-10A wt and FTO-knockdown cells.

Reviewer #2 – see below.

Reviewer #3 – see below.

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

Major comment 2: The reviewer asks to discuss the relevance of the findings for m6Am biology.

Reply: We now discuss this in the discussion session at page 18.

Here we mention that Sun et al (https://doi.org/10.1038/s41467-021-25105-5) performed m6Am-seq in HEK293T cells and detected no m6Am for C/EBPβ (Supplementary Data 2). These experiments were well controlled using m6A-IP experiments with PCIF1-KO HEK293T cells and compared with m6Am-Exo-seq and miCLIP published data.

• *

Minor comment 1: Mistake in Figure 5 legend and beyond.

Reply: Legend of Figure 5 has been updated (text in red) and data for Supplementary Figure 5 has been added, together showing that FTO-CEBPB regulation takes place in MDA-MB-231, MCF-7 and MEFs.

Reviewer 2

Major comment 3: The reviewer noticed duplication of figures in Figure 6A and Supplementary Figure 6A.

Reply: The data presented in the bar graphs of Figure 6 and Supplementary Figure 6 are from two independent experiments. Unfortunately, the pictures of the cells at the bottom for supplementary Figure 6A were the wrong ones and now are replaced by the proper pictures belonging to this experiment.

*Minor comment 1: Statistic analysis in several panels is missing. *

Reply: All significant events are clearly marked by *: p0.05).

Minor comments 2 and 3: Issues in Figure 2E.

Reply: The “E” is removed. We have included the cell type information in the panels D (MDA-MB-231) and E (MDA-MB-231 – shFTO1).

Minor comment 4: Textual description belonging by Figure 2E.

Reply: We have re-written the text describing the data, at page 6.

Minor comment 5: Missing explanation about WTAP.

Reply: We have extended the explanation about WTAP function at page 13.

Minor comment 5: Layout of images needs improvement.

Reply: we have to guess here what the reviewer means, but we have included the requested information in panels 2E and D (see under Minor comments 2 and 3).

For Figure 4 we matched colours for bars representing shFTO1 and shFTO2 throughout the figure.

In Figure 1, panel D we now label the cells as MDA-MB-231 – shTFO (instead of FTO-kd), in line with labelling throughout the paper.

In Figures 1D and 2E we now use +FTO (instead on just FTO) for clearness.

Concerning the reviewers remark under “significance”:

*From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells. *

Reply: We do not understand what the reviewer means with “normal breast cancer cells”, maybe the reviewer means untransformed breast epithelial cells (MCF-10A), or really breast cancer cells derived from patients?

We now added supplementary data FTO knockdown decreases C/EBPβ-LIP levels in MCF-7 (luminal A type breast cancer) and in MEFs (Supplementary Figure 5A and B). This indicates that the FTO- C/EBPβ regulation is conserved in different cell lines of different origin. Still, FTO- C/EBPβ could play a more prominent role in breast cancer with high expression of FTO correlated with high C/EBPβ-LIP levels, and the possibility to suppress this.

Reviewer 3

Major comment 1: Disconnect between findings presented in Figure 1 and Figure 5.

Reply: We have improved the reasoning at page 12.

Major comment 2: In vivo phenotype of FTO deficiency.

Reply: We already discussed the paper by Niu et al (https://doi.org/10.1186/s12943-019-1004-4) in the discussion, page 18.

We have now added information about FTO knockout and overexpression mice and how the phenotypes of FTO knockout mice and CEBPB uORF deficient mice relate to each other at page 19.

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

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

Major comment 4: To support the data on the FTO and WTAP regulation of C/EBPβ isoform expression analysis of the correlation in expression between FTO/ C/EBPβ and WTAP/ C/EBPβ could be performed using the cancer cell encyclopedia (CCLE) dependency map portal.

Reply: The CCLE map uses transcript expression data. Our observation is that mRNA-stability is not affected, but the protein C/EBPβ-LIP/-LAP ratio is. Therefore, CCLE analysis is not informative since it does not provide information on C/EBPβ-LIP/LAP protein ratios.

*Minor comment 2: For the C/EBPβ-LIP overexpression-mediated rescue of the migration phenotype of figure 6 an additional replicate for shFTO1 may be helpful as only one of the two replicates presented is statistically significant. *

Reply: Taken together the results presented in the main and supplementary figure show:

• significant downregulation of migration for all shFTO1 and shFTO2 knockdowns (EV vs. EV-shFTO1 or EV-shFTO2).

• Significant upregulation of migration in FTO-knockdown cells by ectopic LIP expression in three of the four FTO knockdown samples (shFTO1/2-EV vs. LIP).

• Significant further upregulation of migration in one of the control (scr) cells by ectopic LIP expression (scr cells EV vs. LIP).

• Throughout the experiments the observed changes in migration are consistent with shFTO knockdown and LIP expression.

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

Major comment 1: 1. The authors focused on FTO and its function of RNA demethylation but the m6A-seq is not used at all. It is not likely to find the direct down stream effector of FTO without m6A-seq if you believe demethylation is the key function of FTO.

Reply: In Figure 5A we show collective m6A sites based on experiments of others by miCLIP, DART-seq, and SRAMP prediction software. In combination with MeRIP-RT-qPCR in response to FTO KD this shows regulation of CEBPB-mRNA m6A modification by FTO, but without knowledge of the exact m6A sites affected. This study aimed to examine the way FTO affects cell proliferation and migration in different breast cancer cell lines. We revealed the FTO-C/EBPβregulation and will further examine the FTO-C/EBPβ interaction as proposed under session 2, planned revisions. Determination of specific m6Am sites in relation to the translational mechanism involved would be subject of a future study.

*Major comment 2: Related to above concerns, the authors claimed that FTO regulated C/EBPβ-LIP. But how FTO regulated the protein expression is missing. As is known to all, FTO mainly affect RNA m6A. There is a gap between C/EBPβ-LIP protein and the RNA of this gene. *

Reply: It is true we do not understand the mechanism of how m6A modification affects the differential translation of the CEBPB mRNA in the different protein isoforms. Examining this is a major effort and would take considerable time, which is beyond this study, but would be subject of further study.

*Major comment 4: The authors claimed that EMT related genes are affected upon FTO knock down, but Figure 2C do not seem to align with the EMT process. Also, if the authors believe EMT process is regulated, another GSEA enrichment panel like Figure 2B should be included. *

Reply: we have difficulty in understanding this comment. Relevance of the EMT-process is clearly shown by GSEA in panel 2B. GSEA uses a ranked list of gene expression (including all genes in the RNA-seq data set, also the ones not significantly changed in expression) and is thereby a powerful and comprehensive technique to identify relevant pathways since all data in the dataset is used. The GO-term analysis in Figure 2C looks at significantly regulated genes and maps these to GO-terms for biological process (BP), molecular function (MF) or cellular component (CC). Here we used BP, and find many GO-terms involved in ECM/cell membrane/cell adhesion/cell migration (linked to cell migration and thereby EMT since the cells are of epithelial origin). GO-term analysis only requires a list of genes that were found to be significantly regulated (It doesn’t know where your list of genes has been derived from and does not take into account the p-value of a specific gene or the fold change in expression observed between SCR and shFTO cells, in contrast to GSEA). GSEA and GO-term analysis are therefore complementary analyses based on different principles to help indicate what biological processes are changed upon FTO knock-down; their results cannot be directly compared.

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

Major comment 3: The lack of clear impact of FTO KD on the translatome is surprising. Maybe the reverse experiment (over expression) would lead to more relevant findings. Likewise, use of the mutant FTO could differentiate between the demethylase function of FTO vs other non-enzymatic functions.

Reply: Although we agree the proposed experiments are interesting, we believe them to be beyond the scope and time of this manuscript – Major point 3.

Minor comment 1: baseline FTO level in MDA MB231 seems inconsistent (1A vs 1D--controls). It would be useful to see FTO expression across breast cancer cell lines and normal mammary cells to justify choice of cell lines in which experiments were carried out.

Reply: It is due to unfortunate choice of blots with different exposures: The immunoblot in Figure 1A shows wild-type MDA-MB-231 cells with scr-shRNA with expected expression of FTO, compared to shFTO knockdowns with low expression of FTO. Figure 1D are MDA-MB-231 cells with knockdown of FTO and therefore very low FTO expression, compared to FTO knockdown cells with re-expression of FTO. The exposure was a bit unnecessary low, and we changed the blot with a higher exposure blot.

Niu et all (https://doi.org/10.1186/s12943-019-1004-4) have analysed breast cancer samples form patients and breast cancer cell lines and showing a general upregulation of FTO in breast cancer compared to healthy tissue or other cancer cell lines, respectively.

Minor comment 2: lack of data from human specimens.

Reply: Not available. Very difficult to realize since immunostaining techniques cannot discriminate between C/EBPβ-LAP and -LIP isoforms because LIP shares all possible antibody epitopes with LAP. This means that one needs enough material for western blotting which is difficult to arrange.

Significance

Reviewer #1: Despite the interest in the finding that FTO knockdown influences cellular proliferation and migration, the authors do not have enough mechanistic insights on how FTO regulates this process, leaving uncertainty on the study's relevance.

Reply: We agree, but we feel that performing detailed mechanistic study would take considerable time and therefore should be part of future work.

*From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells. *

Reply same as under section 3: We do not understand what the reviewer means with “normal breast cancer cells”, maybe the reviewer means untransformed breast epithelial cells (MCF-10A), or really breast cancer cells derived from patients?

We now added supplementary data FTO knockdown decreases C/EBPβ-LIP levels in MCF-7 (luminal A type breast cancer) and in MEFs (Supplementary Figure 5A and B). This indicates that the FTO- C/EBPβ regulation is conserved in different cell lines of different origin. Still, FTO- C/EBPβ could play a more prominent role in breast cancer with high expression of FTO correlated with high C/EBPβ-LIP levels, and the possibility to suppress this.

*From a molecular point of view, FTO can influence m6A and m6Am. The authors do not mention the relevance of their findings in terms of m6Am biology. *

Reply: See above under 3. Description revisions already incorporated - Major comment 2.

*Reviewer #2: The study's significance is somewhat unclear. The initial sections in the main body present primarily negative or statistically insignificant results. While the explanations in later sections are insightful, they may give the impression of an attempt to justify these negative findings, leaving the study's significance somewhat ambiguous. *

Reply: This raises the issue whether we as a scientific community should present “negative” results. In our opinion this is important since it informs about what is probably not involved (regulation of translation efficiency by FTO) and it leads the way to other hypothesis and explanations of a biological phenomenon. How can – in the reviewers’ words - insightful explanations by labelled as just justifying? They are what they are; insightful and contributing to the topic. Currently the role of FTO in cancer and/or translation regulation is not clear and different views exist (see for example our review https://doi.org/10.1158/0008-5472.CAN-21-3710). In this manuscript we provide evidence that FTO might not be significantly involved in global regulation of mRNA translation efficiency in MDA-MB-231 cells, these results seem quite relevant to share. Furthermore, we provide a possible mechanism that could explain part of the effects observed, and already indicate ourselves future work is needed to further strengthen these findings.

Reviewer #3: * Well written report on the functions of FTO in breast cancer pointing to an oncogenic role and regulation of transcripts related to EMT. Data are well done and well presented, 2 shRNA transfected cell lines are included in the experiments; methodology is clear.*

Reply: we are grateful for this assessment and hope the reviewer will find the manuscript further improved after revision.

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Referee #3

Evidence, reproducibility and clarity

The strengths are the well written manuscript, robust and well presented data, study of the effects of FTO on both transcriptome and translatome.

Major weaknesses:

1. There is a big disconnect between the findings presented in Figures 1-3 and the focus on CEBP in Figure 5. This needs to be reconciled either by demonstrating a link between CEBP and the transcripts found to be dysregulated in Fig 2 or some other way.
2. There are no in vivo data. Does the phenotype caused by FTO KD lead to an in vivo phenotype?
3. The lack of clear impact of FTO KD on the translatome is surprising. Maybe the reverse experiment (over expression) would lead to more relevant findings.Likewise, use of the mutant FTO could differentiate between the demethylase function of FTO vs other non-enzymatic functions.

Minor weaknesses:

1. baseline FTO level in MDA MB231 seems inconsistent (1A vs 1D--controls). It would be useful to see FTO expression across breast cancer cell lines and normal mammary cells to justify choice of cell lines in which experiments were carried out.
2. lack of data from human specimens.

Significance

Well written report on the functions of FTO in breast cancer pointing to an oncogenic role and regulation of transcripts related to EMT. Data are well done and well presented, 2 shRNA transfected cell lines are included in the experiments; methodology is clear.

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Referee #2

Evidence, reproducibility and clarity

The authors are trying to demonstrate the oncogenic role of FTO in breast cancer. RNA-seq was used to explore the effect of FTO on gene transcription and translation. And it turned out that the protein expression ratio of LIP/LAP is the most prominent effect of FTO on breast cancer development. While the oncogenic roles of FTO in breast cancer cell lines look well supported, several key questions remain to be answered before it can be considered to publish.

major comment:

1. The authors focused on FTO and its function of RNA demethylation but the m6A-seq is not used at all. It is not likely to find the direct down stream effector of FTO without m6A-seq if you believe demethylation is the key function of FTO.
2. Related to above concerns, the authors claimed that FTO regulated C/EBPβ-LIP. But how FTO regulated the protein expression is missing. As is known to all, FTO mainly affect RNA m6A. There is a gap between C/EBPβ-LIP protein and the RNA of this gene.
3. Data quality is not convincing, the transwell migration assay image in figure 6 and Supplementary Figure 6 is identical, which is unacceptable.
4. The authors claimed that EMT related genes are affected upon FTO knock down, but Figure 2C do not seem to align with the EMT process. Also, if the authors believe EMT process is regulated, another GSEA enrichment panel like Figure 2B should be included.

Minor concerns

1. Statistic analysis in several panels is missing. Normally, every date should include statistic analysis, even its not significant.
2. Issues in Figure 2E, there is a "E" above the first column, which is not supposed to be there.
3. Also in Figure 2E, these results conducted in FTO-knocked down cells, but the panel did not show clearly.
4. In Figure 2E, the textual description does not entirely correspond with the image results, and there is a lack of information about the expression levels of COL12A1, FN1, MMP1, and TNC.
5. Furthermore, while the article conveys the meaning of WTAP, it lacks a thorough textual explanation. Additionally, the layout of the article's images needs improvement.

Significance

The study's significance is somewhat unclear. The initial sections in the main body present primarily negative or statistically insignificant results. While the explanations in later sections are insightful, they may give the impression of an attempt to justify these negative findings, leaving the study's significance somewhat ambiguous.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors investigated the effect of FTO knockdown in triple-negative breast cancer (TNBC) cells. They show that FTO knockdown reduces the proliferation and migration of two breast cancer cell lines using clonogenic and transwell migration assays. Through transcriptome analysis of FTO-depleted cells, they showed a negative enrichment of the epithelial-to-mesenchymal transition (EMT) signature and showed that this decrease is not mediated at a transcript stability level. Through ribosome profiling experiments they demonstrated that the translatome is only mildly affected by FTO depletion and using differential ribosomal codon reading (diricore) analysis showed that FTO knockdown does not cause specific tRNA or amino acid shortages. They show that FTO and WTAP knockdown reciprocally regulate the expression of C/EBPβ isoform. Finally, through rescue experiments, the authors showed that C/EBPβ-LIP overexpression rescues the decreased migration phenotype observed upon FTO knockdown.

Major comments:

The authors showed that upon FTO knockdown, the C/EBPβ-LIP protein levels decrease, and conversely, upon WTAP knockdown, the levels of C/EBPβ-LIP protein increase (figure 5b and 5d) and suggest that a reversible WTAP- and FTO-controlled m6A modification of CEBP mRNA alters its translation. Upon FTO knockdown, however, the stability of CEBP mRNA is not affected, and despite a clear trend in the increase of the CEBP transcript m6A levels from MeRIP-RT-qPCR (figure 5E), this is not statistically significant. It remains unclear whether the regulatory effect of FTO on the CEBP mRNA transcript is a direct, m6A-mediated effect or an indirect effect. For this reason, further experiments may help to strengthen this result. It would be helpful to clarify if m6A levels increase in the CEPB mRNA level with more replicates of the MeRIP-RT-qPCR or using other quantitative techniques. Moreover, to clarify whether this is directly mediated by FTO a RIP-qPCR for the FTO protein and CEPB mRNA in wild-type cells could be performed.

Additionally, the authors never consider the possibility that FTO could regulate CEBP because of a possible m6Am site. Does CEBP have an m6Am site? Would PCIF1 knockdown cause the same effect that FTO knockdown? Also, the authors should consider classifying mRNAs based on the number of m6A sites or m6Am sites and determine if mRNAs with an m6Am site or an m6A site show a difference in their translation or expression levels compared to non-methylated sites.

It would be interesting to see if the effect of FTO on proliferation and migration impact less aggressive form of cancer or normal breast cancer cells, such as MCF-10A.

To support the data on the FTO and WTAP regulation of C/EBPβ isoform expression analysis of the correlation in expression between FTO/ C/EBPβ and WTAP/ C/EBPβ could be performed using the cancer cell encyclopedia (CCLE) dependency map portal.

Minor comments:

The figure 5 legend is missing the description of the MeRIP-RT-qPCR experiment.

For the C/EBPβ-LIP overexpression-mediated rescue of the migration phenotype of figure 6 an additional replicate for shFTO1 may be helpful as only one of the two replicates presented is statistically significant.

Significance

Despite the interest in the finding that FTO knockdown influences cellular proliferation and migration, the authors do not have enough mechanistic insights on how FTO regulates this process, leaving uncertainty on the study's relevance.

From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells.

From a molecular point of view, FTO can influence m6A and m6Am. The authors do not mention the relevance of their findings in terms of m6Am biology.

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Reply to the reviewers

1. General Statements [optional]

We would like to thank all three reviewers for their careful and comprehensive reviews of our manuscript. We have taken on board all the comments and have made appropriate changes to improve the manuscript. The more substantive changes are to the structuring of the text in Introduction section, and to improving the clarity of Figure 2 after reviewers’ comments (we have added extra panels to A, F and G). Other minor changes are individually signposted in each paragraph of the point-by-point response attached below.

We performed a number of pieces of additional analysis to address reviewer comments. To be as transparent as possible we make these and all other data analyses available in the form of .html files exported by Rmarkdown, hosted at https://joebowness.github.io/YY1-XCI-analysis/.

2. 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. *

• *

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

Summary: This manuscript uses differentiation of the highly informative inter-specific hybrid mouse ESC to follow features of genes that inactivate slowly. Resistance to silencing is reflected in reduced change in chromatin accessibility and the authors identify YY1 and CTCF as enriched amongst these 'slow' genes. This finding is provocative as these factors have been reported to enrich at both human and mouse escape genes. The authors go on to demonstrate that eviction of YY1 is slowly evicted from the X, and that removal of YY1 increases silencing.

Minor Comments: Overall, the manuscript's conclusions are well supported; however, the brevity of the presentation in some places made it difficult to follow, and in other places seemed a missed opportunity to more fully examine or present their data.

1. Introduction is only 2 paragraphs and half of the last is their new findings. First part of results/discussion is then forced to be very introductory. In addition, some discussion of escapees, even if predominantly human, seems warranted in the introduction. There are multiple studies that have tried to identify features enriched at genes that escape inactivation that could be mentioned.

We have now written the introduction as 3 paragraphs instead of 2. In doing this, we have moved the sentence introducing chromatin accessibility from the results section to the introduction. Additionally, we now discuss the studies that focus on escapees (in mouse XCI) in the second introduction paragraph.

Variation in silencing rates. 'Comparable rankings' cites multiple studies (oddly previous sentence cites only two) - how concurrent are they? Developing this further (perhaps a supplementary table) would inform whether the genes assessed are ones that routinely behave similarly across different studies/lines; and also serve as a resource for future studies.

To avoid double-citing, we have made this one sentence and have cited at the end of the sentence 7 studies which describe gene-by-gene variability in rates of silencing. The majority of these studies include comparisons of their categories of fast and slow-silencing gene with previous classifications, and they all conclude that there is substantial concurrence. Some examples:

• Marks et al, 2015, Table S3,
• Loda et al, 2017, Figure 5,
• Barros de Andrade E Sousa et al. 2019, Figure 2
• Pacini et al. 2021, Figure 6e,i We believe this is sufficient evidence for our claim that these studies report “comparable categories” (“ranking” changed to “categories” as not all studies strictly rank). A comprehensive gene-by-gene comparison table would likely serve only to highlight differences due the various silencing assays/model systems/classification approaches used in the studies. If required, however, we would be willing to include a supplemental table which collates where gene silencing categories are discussed in each publication, and links to any supplemental files which provide full lists of X-linked genes.

It would be helpful to give insight into informativity of cross - what proportion of ATAC-seq peaks were informative with allelic information (and similarly, what proportion of genes expressed had allelic information?

Of the 2042 consensus ATAC-seq peaks we defined on ChrX via aggregating macs2 peaks over all time course samples, n = 821 passed our initial criteria for allelic analysis in the iXist-ChrX-Dom model line (ie they are proximal to the Xist locus in ChrX 0-103Mb, overlap SNPs, and contain sufficient allelic reads). A small number of peaks were additionally filtered out during fitting of the exponential decay model, leaving a final ATAC-seq peak set of n = 790 elements (38.6%) which we focus on in this study. We have added this information to the text (first Results paragraph).

Our collections of ChrX genes amenable to allelic analysis were not redefined for this study. We used lists of genes defined in our previous ChrRNA-seq study (10.1016/j.celrep.2022.110830). In general, allelic analysis of gene expression is not as limited by the frequency of SNPs, because the sequence length of transcripts (including introns, which are a significant fraction of the reads in ChrRNA-seq data) is much greater than for ATAC-seq peaks. Only a few very lowly expressed genes are not amenable to allelic ChrRNA-seq analysis.

P5: "can be influenced by Xist RNA via a variety of mechanisms" seems like it this sweeping statement could use expansion, or at least a reference. Authors could also clarify that 'distal elements assigned by linear genomic proximity is their definition of nearest gene.

The statement that “both [chromatin accessibility and gene expression] can be influenced by Xist RNA via a variety of mechanisms” is intentionally broad to support a negative argument that we do not wish to mechanistically over-interpret the observation that Xi chromatin accessibility loss occurs slower than gene silencing. Nonetheless, we have added two references to studies which report mechanisms for how Xist may influence chromatin accessibility; via recruiting PRC1 (Pintacuda et al 2017) or antagonising BRG1 (Jegu et al 2019). That multiple molecular pathways simultaneously contribute towards the effect of Xist RNA on gene silencing is well established in the field (see reviews such as Brockdorff et al 2020, Boeren et al 2021, Loda et al 2022).

We have clarified in the text that our definition of “distal” is all REs which do not overlap with promoter regions (TSS+/-500bp). We have also made it clearer that our definition of “nearest” gene refers to linear genomic proximity in both the Results and Methods sections.

Figure S1 - there are 6-8 other regions that fail to become monoallelic - what are they?

The regions which stand out most by the colour scheme of the heatmap in Figure S1 are those where accessibility increases on Xi, most notably the loci of Firre, Dxz4 and Xist, which are known to have unique features related to the 3D superstructure of the inactive X chromosome. A few other regions which do not become monoallelic harbour classic “escapee” genes. We have now labelled the locations of escapees Ddx3x, Slc25a5 and Eif2s3x in FigS1.

The other regions noticeable in the heatmap have no obvious features which explain why they fail to become monoallelic. We have highlighted a region containing intragenic peaks within Bcor (a gene which is silenced in iXist-ChrX mESCs), but many other regions are not in the vicinity of genes. Some of the persistently Xi-accessible peaks within these regions contain strong YY1 or CTCF sites, although many others do not.

It is also possible that some Xi-accessible peaks are artefacts of mismatches between the Castaneous or Domesticus/129Sv strain SNP databases and ground truth iXist-ChrX genome sequence. The number of these cases are small, and if a misannotated SNP is the only SNP present in a single peak, the peak is discarded by our allelic filtering criteria as it will appear monoallelic in uninduced mESCs.

Is there any correlation between silencing speed and expression (as previously reported)? If yes, then is there also a correlation with YY1 presence - and is this correlation greater than or less than seen on autosomes?

The data we present here pertaining to gene silencing kinetics is reused from our previous study. In that work we did indeed observe a significant association between silencing rate and initial gene expression levels (10.1016/j.celrep.2022.110830, Supplemental Information Figure S5F), which has also been reported by multiple groups previously.

To correlate YY1 binding with gene expression levels, we calculated transcripts per million (TPM) for all genes from our genome-wide mRNA-seq data of uninduced iXist-ChrX-Dom cells (GSE185869). It is indeed true that, on average, X-linked genes classified as “direct” YY1-targets in our analysis have higher levels of initial expression (median TPM 70.8, n=64) compared to non-target genes (median TPM 30.7, n=346). Autosomal YY1 targets are also relatively higher expressed (median TPM 29.6, n=1882) than non-YY1 genes (median TPM 8.0, n=9983). Within the list of YY1-targets, there is no additional correlation between quantitative levels of YY1 ChIP enrichment (calculated in this study using BAMscale (Pongor et al, 2020)) and gene expression (R=-0.05, Spearman correlation).

Therefore, we appreciate that this correlation between YY1-binding and gene expression levels may be a covariate in the correlation we report in this study between YY1-target genes and slow-silencing. This does not invalidate a potential functional role for YY1 in impeding silencing, as it could affect both variables via common or distinct mechanisms. Nevertheless, in an attempt to account for initial expression level as a covariate, we compared the silencing halftimes of YY1-targets versus non-targets within genes grouped by similar expression levels (low, medium and high-expressed genes). YY1-targets have slower halftimes in each comparison, and this difference is highly significant (p=1.9e-05, Wilcoxon test) for the “medium-expressed” gene group. This implies that YY1 contributes towards slower gene silencing kinetics independently of initial gene expression levels. We have added this panel to Fig2 with an associated sentence in the Results section.

These new analyses are also appended to the documentation of the R scripts used to generate the main figures in this study (Figure2_YY1association.Rmd), which will all be published to Github.

It is also important to note that this analysis approach is complicated by the methodology we use to classify YY1 target genes. In this study, we define YY1 targets based on the presence of ChIP-seq peaks overlapping the gene promoters, which is reasonable and widely accepted practice when defining targets of transcription factors. However, as briefly discussed in the Methods, in YY1 ChIP-seq data samples with very high signal:noise (eg Fig3), minor peaks of YY1 enrichment can be detected at almost every active promoter. As enrichment at these peaks is typically much less than at peaks with occurrences of the YY1 consensus DNA motif, we hypothesise that these small peaks result from secondary YY1 cofactors enriched at promoters (eg P300, BAF, Mediator) rather than direct sites of binding to DNA/chromatin. Therefore, for annotating genes as “direct” YY1 targets, we chose to use the YY1 peak set defined from lower signal:noise ChIP-seq data in iXist-ChrX produced with the endogenous YY1 Ab. Nevertheless, this behaviour is likely to confound any analysis correlating YY1 ChIP binding with gene expression.

Figure 2: Have the authors considered using quartiles rather than an arbitrary division into depleted and persistent?

We primarily chose this binary classification of REs as either Xi-“persistent” or Xi-“depleted” to maximise the numbers of sequences that could be used in each group as input for the HOMER motif enrichment software.

It is also not trivial to separate REs into quartiles because our “Xi-persistent” classification includes peaks defined as “biallelically accessible in NPCs”, as well as peaks with slow accessibility halftimes. This is explained in both the Results and Methods but we now have edited Fig2A to make it clearer. Instead of quartiles, we have performed an analysis which keeps “biallelically accessible REs” as a separate category and subdivides the remaining peaks into three groups by halftimes (slow, intermediate and fast accessibility loss). The same trends are evident with this four-category approach as with the two-category approach.

Importantly, our follow-up analyses which confirm the association between YY1 binding and slow Xi accessibility loss (Fig2E) and slow silencing (Fig 2F-H) are independent from categorisations of REs which rely on arbitrary thresholds.

1. Could simplify secondary labels to solely YY1 and CTCF. D & F do not print in black and white. Overall the mESC versus NPC can be confusing, perhaps mESC (no diff) would be helpful?

We have simplified the secondary labels in Fig2B and modified the colour scheme of FIg2D and Fig2F as suggested. “mESC” is now modified to “mESC no diff” in Fig2H, FigS2B, Fig3C and Fig3E to reduce the potential for confusion.

The numbers appear to suggest YY1 is generally enriched on X, but not at promoters?? Is this true?

The explanation for this is that clear peaks of YY1 ChIP are found at young LINE1 elements in iXist-ChrX mESCs (specifically over L1Md_T subfamilies). These elements are highly enriched (>2-fold) on the mouse X chromosome compared to autosomes (Waterston 2002), and the majority are not promoter-associated. We chose not to include a discussion of YY1 enrichment at repetitive LINE1 elements in this study primarily because of a) issues related to multiple-mapping reads, such as difficulties distinguishing ChrX vs autosomal reads, and b) the absence of strain-specific SNPs within annotated ChrX L1Md_Ts means that none of these elements are amenable to allelic analysis so we cannot compare Xi versus Xa. However, these LINE1 peaks are a significant fraction (262/521) of the numbers of YY1 ChIP-seq peaks in Fig2C.

For Figure 2f, it might be helpful to show autosomal genes - are Fast depleted or Slow enriched for YY1 relative to autosomes?

We have calculated these numbers as part of the analysis of gene expression on ChrX and autosomes above. Overall, the fraction of genes defined as YY1-targets is the same on ChrX as on autosomes (~0.16). Accordingly, fast-silencing genes are depleted for YY1 compared to autosomes, whereas slow-silencing genes are enriched for YY1 compared to autosomes. Fig2F is now redesigned to include the total numbers of YY1-target genes on ChrX and autosomes.

More generally, is YY1 binding on the X lost more slowly than YY1 binding on autosomes, or is the slow loss a feature of YY1. While I agree YY1 could have direct up or down-regulatory roles, Figure S3 could also be reflecting a secondary impact.

We agree that many of the differentially regulated genes after 52 hours of YY1 degradation could be secondary effects and have added a sentence on this to the relevant paragraph in the text.

Figure 3, 4 and supplementary - the chromosome cartoon introduces the LOH in iXist, but this needs to be described in text. Describing the reciprocal as a biological replicate seems challenging given this LOH.

It is true that the reciprocal lines iXist-ChrX-Dom and iXist-ChrX-Cast are not true biological replicates, and we try to avoid referring to them as such. Writing this in the legend of Fig3 was an error which we have corrected. We have now also mentioned the recombination event in the iXist-ChrX-Dom cell line at the point where data from this line is first discussed (paragraph 1 of Results section).

For the latter parts this work (Figs 3 and 4), we made the conscious decision to proceed with two YY1-FKP12F36V cell lines from different reciprocal iXist-ChrX backgrounds (aF1 in iXist-ChrX-Dom, cC3 in iXist-ChrX-Cast), rather than “biological replicate” clones from either iXist-ChrX-Dom or iXist-ChrX-Cast. Our reasoning was to control against potential confounding effects of strain background on our experiments related to the role of YY1. Although there were some minor differences between the clones, aF1 and cC3 demonstrated essentially equivalent phenotypes in all analyses we performed.

Could a panel of TFs be used rather than OCT4 which has its own unique properties to emphasize that YY1 is unique?

This would indeed be worthwhile, and we did consider attempting to perform ChIP-seq for additional TFs other than OCT4 in order to collect more points of comparison for the slow rate of loss of YY1 binding to Xi. However, it is admittedly hard to identify appropriate candidate TFs in mESCs which a) have similar numbers of discrete peaks of binding in promoters and distal elements on ChrX and b) it is possible to reliably perform ChIP-seq for at sufficiently high signal:noise to allow for quantitative allelic analysis.

We have changed the text to acknowledge that our comparison only to OCT4 limits the scope of the statements we can make about unique properties of YY1 binding.

Figure 4 - by examining 'late' genes, a change in allelic ratio is observed, but what about escape genes (e.g. Kdm5c, Kdm6a)? Do they now become silent? It would be helpful to have all this data as a supplementary table so people could query their 'favourite' gene.

YY1 degradation experiments performed for Figure 4 were performed on mESCs without cellular differentiation (YY1-ablated cells do not survive in our mESC to NPC differentiation protocol). In undifferentiated mESCs, silencing of the inactive X does not reach completion, and in fact all X-linked genes are residually expressed at a higher level than in equivalent timepoints of Xist induction with NPC differentiation (see Figure 4D, Bowness et al 2022). We write in the text “slow-silencing genes are residually expressed from Xi” because genes of this category account for the majority of expression under these conditions, and indeed almost all slow genes would all be classed as “escape genes” in this setting by a conventional definition of >10% residual expression from Xi (see also Figure 4D, Bowness et al 2022). Our analysis in Fig4D (of this study) includes all genes, and we share processed .txt files of allelic ratio and allelic fold changes in GEO, so querying the behaviour of a favourite gene would be easy (GSE240680).

Incidentally, when we do perform NPC differentiation of iXist-ChrX NPC, at late stages very few genes show any expression from Xi (Ddx3x, Slc25a5, Eif2s3x and Kdm5c clearly escape, but even Kdm6a is entirely silenced). Unfortunately, with such a small number of “super” escapees it is hard to make any general conclusions, so in this study we can only make inferences about escape via the transitive property that many “slow-silencing” genes are facultative escapees in other settings without induced Xist overexpression. We now write about this consideration in the introduction and final paragraph of the main text.

It seems surprising that loss of YY1 has no demonstrative impact on the Xa. Figure S3B suggests that over 1000 genes are significantly impacted - primarily down regulated. How many of those are X-linked? Perhaps they could be colored differently?

For the broad-brush differential expression testing in FigS3B, we use all the ChrRNA-seq samples (6 x untreated, 6 x dTAG) as “pseudo-replicates”, disregarding any confounding effects related to induced Xist-silencing as effecting untreated and dTAG sample groups equivalently. We did specifically investigate the behaviour of X-linked genes in this volcano plot, however only a very small number of genes were differentially expressed (n=22 X-linked genes appeared significantly downregulated compared to n=4 genes upregulated). This can be seen in our analysis records uploaded to Github.

Additionally, there is actually a minor effect of YY1 loss on expression of YY1-target genes on Xa. This can be seen in Fig4F, where the median lines of YY1-target boxes lie below the horizontal line of 0-fold change.

Since XIST+/undifferentiated cells retain YY1, is YY1 binding sensitive to DNAme? Indeed, are X chromosome bound sites in islands that become methylated? Figure S4 shows YY1-targetted X genes in SMCHD1 knockout; can CTCF targets also be shown? While identified in Figure 2, CTCF was not examined the way YY1 was, although it has also been identified in somatic studies of genes that escape X inactivation.

Binding of YY1 is indeed sensitive to DNA methylation; specifically it is reported to be blocked by CpG methylation (see refs (Kim et al, 2003; Makhlouf et al, 2014; Fang et al, 2019). Thus, crosstalk with the DNA methylation pathways, which deposit de novo CpG island methylation as a late event of XCI (Lock 1987, Gendrel 2012), did appeal to us as a potential mechanism of YY1 “eviction”. However, preliminary analysis we performed to investigate this revealed limited overlap between YY1 binding sites and de novo meythlated CpG islands in the iXist-ChrX model cell line.

FigS4 presents ATAC-seq data from two iXist-ChrX SmcHD1 KO clonal cell lines, comparing the accessibility loss kinetics between YY1-binding and non-YY1 REs in these cells.

Although FigS4 in this paper does not show genes, we have previously published ChrRNA-seq data from these SmcHD1 KO lines over a similar Xist induction + NPC differentiation time course (Figure 6, Bowness et al, 2022). A reanalysis of this ChrRNA-seq data by YY1-target vs non-target genes shows a similar trend to the accessibility data, although this is expected from the strong overlap of both “YY1-target” and “SmcHD1-dependent” genes with slow-silencing genes in our model.

With respect to CTCF, we have performed a similar analysis of this data separating ATAC-seq peaks by CTCF-binding rather than YY1-binding. This shows a similar trend to YY1, but is overall less pronounced, and is now included in our analysis records. We have reported previously that loss of CTCF from many binding sites on Xi requires SmcHD1 (Gdula et al, 2019).

When the authors use cf. do they simply mean see also, or as wikipedia suggests: "the cited source supports a different claim (proposition) than the one just made, that it is worthwhile to compare the two claims and assess the difference". Perhaps it would be worth spelling out to clarify for the audience.

We used “cf.” in the text to mean “compare with”, when referring to a plot/observation/piece of data outside of the figure being immediately discussed (either in another study or different section of the paper). We were not aware of the recommendation to only use the cf abbreviation when the two items are intended to be contrasted. We do not believe this to be a universal grammatical convention, but nevertheless have changed incidences of cf. to “see also”.

Reviewer #1 (Significance (Required)):

General assessment: An important question in human biology is how much the sex chromosome contributes to sex differences in disease frequency. Genes that escape X inactivation in humans seem to have considerable impact on gene expression genome-wide. While there are not as many genes in mouse that escape inactivation, the use of the mESC cell differentiation approach allows detailed assessment of the timing of silencing during inactivation. The authors utilize an inter-specific cross and it would be interesting to know the limitations of such a system (in terms of informative DHS/genes that are informative).

Advance: As the authors note, there are multiple studies of similar systems that have revealed differences in the speeds of silencing of genes. However, this is the first study to my knowledge that has then tried to assess timing with gene-specific factors. There are multiple studies in humans comparing escape and subject genes for TFs, but lacking the developmental timing that this study incorporates.

Audience: While generally applicable to a basic research audience interested in gene regulation, the applicability to human genes that escape inactivation may interest cancer researchers or clinical audiences interested in sex differences.

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

The authors studied the molecular basis of a variation in the rate of individual gene silencing on the X undergoing inactivation. They took advantage of ATAC-seq to observe the kinetics of chromatin accessibility along the inactive X upon induction of Xist expression in mESCs. They demonstrated a clear correspondence between the decrease in chromatin accessibility and the silencing of nearby genes. Furthermore, they found that persistently accessible regulatory elements and slow-silencing were associated with binding of YY1. YY1 tended to associate longer with genes that required more time to be silenced than those that became silenced fast on the inactive X during XCI. The acute loss of YY1 facilitated silencing of slow genes in a shorter period. They suggest that whether or not the transcription factors stay associated longer is another factor that impacts the variation in the rate of gene silencing on the Xi.

Reviewer #2 (Significance (Required)):

It has been suggested that the rate of gene silencing during XCI is varies depending on the distance of individual genes from the Xist locus or the entry site of Xist RNA on the X, as well as their initial expression levels before silencing. This study provides another perspective on this issue. The persistent association of transcription factors during XCI affects the rate of gene silencing. Although the issued addressed here might draw attention from only the limited fields of specialists, their finding advances our understanding of how the efficiency of silencing is controlled during the process of XCI. The experimental data essentially support their conclusion, and the manuscript was easy to follow. However, I still have some comments, which I would like the authors to consider before further consideration.

Major concerns 1. Based on the results shown in Figure 3E and F, the authors concluded that YY1 was more resistant than other TFs against the eviction from the X upon Xist induction. I am not still convinced with this. YY1 binds DNA via the zinc finger domain, while Oct4 binds DNA via the homeodomain. The difference in the binding module between them might affect their dissociation or the response to Xist RNA-mediated chromatin changes. In addition, given that YY1 has been reported to bind RNA, including Xist, as well, Oct4 might not be a good TF to compare.

We acknowledge and agree that our singular comparison between YY1 and OCT4 is insufficient to support a general conclusion that YY1 is unique with respect to its binding properties on Xi. This was also alluded to by Reviewer #1 (see 10.), where in response we write about the difficulties of selecting other appropriate/feasible candidate TFs for ChIP-seq in order to widen the comparison beyond OCT4. In consideration of this concern, we have re-phrased our conclusions regarding this point in the text, both at the point where it is first presented (Fig3F) and in the first discussion paragraph.

Furthermore, the difference in allelic ratio change between YY1 and OCT4 is admittedly not dramatic, and this metric can be influenced somewhat by the properties of the sets of peaks used (which is also why we have not tried to add statistical significance to this comparison in Fig3F). In order to make the comparison with OCT4 (a classic pluripotency factor), we were also limited to using mESC culture without differentiation conditions. It is possible that more pronounced differences between YY1 and other TFs would be observed under conditions where XCI is able to proceed further.

Even so, we contend that our observation that YY1 binding is lost from the Xi relatively slowly likely stands without a requirement for a comparison with OCT4 or other transcription factors. The decrease in allelic ratio for YY1 ChIP occurs more slowly than overall loss of chromatin accessibility from REs, which is arguably a more general proxy for TF binding, and much slower than kinetics of gene silencing (Fig3D and FigS2C). In addition, no other TF motifs (except CTCF, which has its own unique properties) were found significantly enriched within persistently-accessible REs, which would be an expectation if a different factor had similar properties of late-retained Xi binding as YY1.

Thus, overall we have tried to write the paper without overstating in isolation the importance of our claim that YY1 binding on Xi is relatively resistant to Xist-mediated inactivation, instead emphasising that it should be considered alongside the other pieces of data in the study.

I don't think that Kinetics of YY1 eviction upon Xist induction in SmcHD1 KO cells during NSC differentiation fit the phenotype of Smchd1mutant cells. Although their previous study by Bowness et al (2022) showed that Smchd1-KO cells fail to establish complete silencing of SmcHD1-dependnet genes, their silencing still reached rather appreciable levels according to Figure 6 of Bowness et al (2022). This is, in fact, consistent with the idea that XCI initially takes place in the mutant embryos, at least to an extent that does not compromise early postimplantation development. On the other hand, a significant portion of YY1 appears to remain associated with the target genes on both active and inactive X (Figure S4), which I think suggests that the presence of YY1 is compatible with silencing of SmdHD1-dependent genes. This is contradictory to the proposed role of YY1 that sustains the expression of X-linked genes in this context.

At any given timepoint of XCI, our data sets of gene silencing (ChrRNA-seq) consistently show a more pronounced allelic skew compared to chromatin accessibility (ATAC-seq). This behaviour is discussed in relation to Figure 1 in the text (see Results paragraph 2). We do not wish to overinterpret this quantitative difference because the assays are technically different and accessibility is not linearly correlated with gene expression. With this in consideration, we interpret the ATAC-seq data presented in Figure S4 to be fully consistent with the iXist-ChrX SmcHD1 KO ChrRNA-seq data in Figure 6 of our previous publication ie. a small increase in residual Xi gene expression from SmcHD1 KO NPCs is accompanied by a more appreciable increase in residual Xi chromatin accessibility. In line with this, it would not be contradictory for substantially increased Xi YY1 binding to sustain a quantitively small (but nonetheless meaningful) increase in residual gene expression from Xi.

Additionally, the context in which we include this SmcHD1 KO ATAC-seq data in the current paper is to hypothesise a potential role for SmcHD1 in contributing towards the eventual removal of YY1 binding from Xi. This hypothesis is essentially based on two observations; 1.) There is substantially more residual YY1 binding to Xi in mESC no diff conditions (Figure 3) and 2.) One difference between no diff and diff conditions is absence of SmcHD1 recruitment in the former (Figure 5 in our previous study). The new SmcHD1 KO ATAC-seq data adds a third observation which supports the hypothesis - that YY1-bound REs are appreciably more accessible from Xi in SmcHD1 KO. However, none of these observations are direct evidence of a link between SmcHD1 and YY1, and more experiments would be required to substantiate this potential mechanism. If confirmed, it would be logically reasonable to suggest a role for YY1 in contributing towards the residual expression of X-linked in the context of SmcHD1 KO, but we do not yet claim this, and a potential link with SmcHD1 KO is not the main focus of the paper.

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

In this manuscript, Bowness and colleagues describe the interesting finding that the transcription factor YY1 is associated with slow silencing genes in induced X-Chromosome Inactivation (XCI). The authors have conducted a comprehensive characterization of X-linked gene silencing and the loss of chromatin accessibility of regulatory elements in induced XCI in ESCs and during NPC differentiation. X-linked gene silencing was classified into four categories, ranging from fast-silenced genes to genes that escape silencing. Motif enrichment analysis of regulatory elements associated with slowly silenced genes identified YY1 as the transcription factor most significantly enriched. The separation of YY1-target and non-target genes confirmed that most genes bound by YY1 indeed exhibit slower silencing kinetics. A comparison of the binding kinetics of YY1 to another transcription factor, OCT4, during XCI revealed that YY1 is evicted more slowly compared to OCT4 on the inactive X, suggesting that slower eviction is a unique property of YY1. Conditional knock-outs of YY1 using protein degradation during induced XCI in mESCs demonstrated that the loss of YY1 at target genes enhances silencing. This supports the hypothesis that YY1 serves as a crucial barrier for slow-silenced genes during XCI. Finally, the authors propose a hypothesis regarding the mechanism of YY1 eviction, suggesting a potential connection to the role of SmcHD1 during XCI.

The authors provide an in-depth analysis of the role of YY1 in gene silencing kinetics during induced XCI and believe this manuscript should be published if our comments are addressed.

Major comment:

Based on the allelic ratio in figure 3C only minor loss of YY1 binding occurs in induced XCI in mESCs on the Xi, while silencing is established properly as shown in figure 4C (left panel, red boxplots). This suggests that YY1 eviction is not necessarily required for these genes to be effectively silenced. Could the authors explain this discrepancy in the data regarding their manuscript conclusions? It seems this is true for XCI happening during differentiation towards NPCs, but not if cells are stuck in the pluripotency stage?

Whilst indeed substantial, we do not consider the silencing seen for 6-day mESCs in Fig4C to be “established properly”. We refer to our previous publication (Figure 4 Bowness et al., 2022), which shows that silencing at equivalent timepoints under differentiation conditions (d5-d7) is significantly more pronounced (near-“complete”). Indeed, the level of silencing reached by YY1-FKBP mESCs (Xist induced but no dTAG treatment) aligns with the plateau of silencing in undifferentiated mESCs we describe in our previous study (median allelic ratio of approximately 0.1).

We conclude that YY1 contributes somewhat to sustaining this residual expression in mESCs, because a) substantial YY1 binding remains on Xi at these timepoints in mESCs and b) silencing increases with degradation of YY1 (the latter is more direct evidence). Notably, silencing does not progress to completion (allelic ratio of 0) in the absence of YY1, so we do not claim that YY1 is the only factor sustaining residual Xi gene expression in mESCs.

We interpret this comment to be a fundamentally similar concern to that raised by Reviewer #2 (2.), but in the context of undifferentiated mESCs rather than SmcHD1 KO. As stated above, we do not think it inherently contradictory for substantially increased Xi YY1 binding to sustain a quantitively small (but nonetheless meaningful) increase in residual gene expression from Xi.

Minor comments:

1. In the abstract lines 7-8, the authors state that the experiments were performed in mouse embryonic stem cell lines, but much of the data shown is acquired in NPC differentiations. Please adjust abstract.

We have adjusted this sentence in the abstract to include that many of the experiments in the paper involved differentiation of iXist-ChrX mESCs.

The last sentence of the abstract states that YY1 acts as a barrier to silencing but as stated in my major comment, that does seem to be the case in ESC differentiation towards NPCs, but not in ESCs themselves. Please tone down this sentence. Moreover, we do not fully understand where the 'is removed only at late stages' comes from? Is this because of the Smchd1 link? We find this link quite weak with the data presented. We would tone down that last abstract sentence.

We have toned down the final sentence of the abstract accordingly. We agree that “removed only at late stages” is unsubstantiated since YY1 binding on Xi decreases over the entire time course (albeit slowly). However, we maintain that a connection between YY1 and late stages of the XCI process is reasonable to infer from the various pieces of evidence we provide in the study (egs YY1 is persistently enriched in accessible REs, it is associated with slow-silencing genes, and it remains bound to Xi in undifferentiated mESCs).

Several comparisons to human XCI have been made in the article. We do agree that there are similarities between mouse and human XCI. However, there is insufficient data that substantiates that these genes are regulated in a similar manner in humans. We believe the comparisons should be removed altogether or attenuated.

We agree that there is nothing in our data that directly pertains to human XCI. Comparisons to human are only made twice in the paper: Initially in the introduction to make a broad statement that many mechanisms of Xist function are conserved between species, and finally as speculation in the last discussion paragraph. We think it is relevant to acknowledge the parallels between our study, which links YY1 binding with resistance to Xist-silencing in a mouse ESC model, and literature describing a similar association between YY1 and XCI escape in humans.

At bottom of page 4, the authors say that for any given gene, the allelic ration of accessibility at its promoter decreased more slowly than it silenced and then write Fig 1B. They probably mean S1C? Since 1B only shows 4 genes.

The phrase “any given” was used colloquially (ie imprecisely), so we have replaced it with “individual”.

Figure 1B shows the average allelic ratio of multiple clones for genes representing different silencing speeds. Each data point is the average of multiple clones for these representative genes, could the authors show the individual data points or the standard deviation?

Fig1B predominantly shows the averages of only two replicate time-courses of Xist induction with NPC differentiation using the same parental clonal cell line, iXist-ChrX-Dom, but performed on different dates and passages. We regenerated the panel without merging the replicate data points, but this has little effect on the plot (see the Rmarkdown html file of Figure 1 on Github).

Figure 1B. Loss of promoter accessibility lags behind loss of chromatin-associated RNA expression for these 4 genes. What about distal REs? Do the allelic ratios for the distal REs more closely follow chromatin-associated RNA expression? Could the authors show this in a supplemental figure?

We comment from FigS1C on the general trend that accessibility decrease from Xi occurs slower than gene silencing (measured by ChrRNA-seq). We then find in FigS1D that distal elements lose accessibility slightly faster than promoters. Although overall the allelic ratio decrease of distal (non-CTCF) RE accessibility is slightly closer to the trajectory to that of gene silencing, it remains substantially slower (see again the Rmarkdown .html file of Figure 1 on Github).

An equivalent plot to Fig1B showing distal REs would rely on our simplistic assignment of distal elements to their nearest genes. We believe this is reasonable generalisation for investigating chromosome-wide trends but unlikely to be sufficiently accurate at the level of specific genes.

Figure 1B: gene silencing trajectory is depicted left while the legend says right. Same for promoter accessibility.

The legend is now corrected.

Figure S1A shows only part of the X chromosome. The area downstream of Xist is missing. Is this because the iXist-ChrXDom cell line is missing allelic resolution as shown in figure S2A? Could the authors explain in the figure legend that part of the X-Chromosome is missing?

We have now included a reference to the recombination event in the iXist-ChrXDom cell line both when we present data from this background in the first paragraph of the Results section, and in the legend of FigS1A.

Figure 2C shows that 94 TSSs bear a YY1 peak, yet Fig 2F shows 62 are targets of YY1. Is this because the rest are not properly silenced or are escapees?

Fig2C shows the numbers of ChrX YY1 ATAC-seq peaks which overlap with “promoters” (ie regions +/- 500bp of a TSS). By contrast, Fig2F shows ChrX genes classified as direct YY1-targets for allelic silencing analysis. The discrepancy between these numbers is due to a number of reasons:

1. It is possible for multiple YY1 peaks to overlap the same promoter (eg one peak overlaps 500bp upstream, a separate peak overlaps 500bp downstream).
2. The count in Fig2C is not restrictive to one TSS per gene in cases where there are multiple transcript isoforms in the gene annotation, thus multiple YY1 peaks can overlap different promoters for the same gene.
3. A few genes do not pass our filters for allelic silencing analysis (eg they are too lowly expressed). Some YY1 peaks may overlap these genes. We hope the revised version of Fig2F, which includes numbers of direct YY1 target genes on autosomes and ChrX, makes the distinction between these two numbers clearer.

Moreover, YY1 has ~4-fold more peaks on the X chromosome on distal elements compared to promoters. Yet figure 2F exclusively shows the proportion of YY1 binding sites on TSSs. Would distal REs show similar proportions for the silencing categories? Could the authors show the differences in a Supplemental figure?

As discussed in the response to Reviewer #1 (point 8.), a large fraction of distal YY1 peaks on ChrX are at LINE1 elements, which are not amenable to allelic analysis. Excluding these peaks results in a smaller number of distal elements bound by YY1. The application of our filters for allelic analysis reduces the number of distal YY1-bound REs even more, and our assignment of distal REs to their nearest gene is imprecise. For these reasons, we do not think a comparison of genes classified by whether they are putative targets of distal YY1-bound enhancers is informative.

The authors switch between different model systems in the figures, which makes quite confusing which type of XCI is being discussed. We would like to see clearly stated above all panels which cell culture condition is being studied (mESCs or NPCs).

We have tried to improve this potential source of confusion by modifying “mESC” to “mESC no diff” in the relevant figure panels (see response to Reviewer #1 comment 7B), and adding “in mESCs without differentiation” to the title of Figure 4.

In Figure 3E and 3F the authors look at the binding retention of OCT4 during XCI in ESCs. However, it is not clear why the authors choose OCT4. Could the authors explain why specifically OCT4 was chosen for these analyses?

In our responses to the other reviewers, we discuss the limitations of only having one other TF to compare to YY1. The choice of OCT4 was primarily dictated by our experience and confidence in being able to generate high quality ChIP-seq data of this factor.

As it was essentially arbitrary for the purposes of this paper, we have added a comment to this effect in the text (“with that of a different arbitrary TF, OCT4”).

What is the expression level of YY1 in NPCs compared to mESCS? In Supplemental S2A, it seems that YY1 protein levels decrease over time during NPC differentiation. Is part of the increased eviction a result of lower protein levels of YY1? Probably not since you calculate ratios between Xi and Xa. Can you please comment on this?

We were similarly intrigued by this apparent decrease in YY1 protein levels in NPCs (there is no decrease on the RNA level) and initially considered if it could contribute to the relative.

In FigS2A specifically, the d18 NPC band is probably just a poor quality sample extraction. Our ChIP-seq data generated from the same sample is similar poor compared to the others (FigS2B). In other YY1-FKBP12F36V clones we derived and characterised by Western (not described further in this study, but will likely be published as raw source data for the cropped blots we show in FigS2A), the apparent difference in YY1 protein levels in NPCs is less pronounced. Although a minor decrease in YY1 protein in NPCs seems to be robust, we do not think it relevant in the context of our analysis of YY1 and XCI, as we almost always use Xa as internal comparison for any observations made about Xi.

On page 7 the authors state that degrading YY1 does not affect Xist spreading and/or localisation. Indeed, it has been previously shown by other groups that YY1 is required for Xist localisation during XCI. Could the authors elaborate further on the why their cells behave differently compared to the Jeon 2011 paper?

We are working with a mouse ESC model of inducible Xist from its endogenous locus on ChrX and using the dTAG system to degrade YY1 protein. By contrast, Jeon 2011 worked with an Xist transgene integrated at random in the genome of mouse embryonic fibroblasts (MEFs) and siRNA knockdown of YY1. The difference in our observations could be linked to any of these 4 differences (ie cellular context, Xist genomic location, Xist introns, knockdown strategy), but we cannot identify a specific explanation.

In figure 4G and figure S3D elevated levels of Xist are observed in the dTAG conditions. As the authors point out, this could then result in accelerated silencing of the X seen upon YY1 loss. Are these elevated Xist levels that result in enhanced silencing in figure 4 relevant for the kinetics of silencing? Moreover, YY1 could act as transcriptional regulator of those genes in the X and by removing YY1, one would expect decreased transcription, which would be read as accelerated silencing. The authors could see whether the genes that show accelerated silencing are regulated by YY1 in ESCs (+ dTAG, - Dox).

We agree that these points are important to consider when interpreting the results of the YY1-FKBP12F36V ChrRNA-seq we present in Figure 4. However, we believe they are covered in the text during our discussion of the data.

In relation to the final suggestion, the silencing of almost all X-linked genes is increased upon YY1 removal so separating a specific set of genes which show accelerated silencing would be difficult. Nevertheless, in Fig4F we report that the increases in Xi silencing are strongest for direct YY1 target genes. In fact, these genes also show a minor decrease in expression in the + dTAG - Dox condition (see response to Reviewer #1 point 12.). However, by-and-large the differences in Xa log2FCs between YY1-target and non-target genes are less statistically significant. Non-significant p-values are not shown on Fig4F, but can be found in our Rmarkdown analysis records.

Can the authors explain why they decided to put the Smchd1 part after the conclusion? Before the conclusion would have been better? The probable link between YY1 and SmcHD1 is definitely something important to investigate.

Supplemental FigS4 relating to SmcHD1 is more speculative and we lack direct mechanistic evidence linking YY1 and SmcHD1. It would require more experiments to substantiate this as a mechanism. We think these experiments could potentially be very interesting, but are beyond the scope of this study.

In the paper the authors cite Bowness et al., 2022. In it, Figure 5F studies silencing times with respect to silencing dependency on SmcHD1. What is the overlap between SmcHD1 target genes and YY1 target genes? This would provide more data about the correlation between YY1 and SmcHD1.

There is an association between YY1 target genes and our previous categories of genes based on SmcHD1 dependence (13/56 SmcHD1_dependent genes are YY1 targets compared to only 8/101 of SmchD1_not_dependent genes). However, this enrichment of YY1 targets in SmcHD1 dependent genes is not so striking to warrant inclusion into the (very short) discussion of SmcHD1 in this paper. This association is also expected from the fact that both YY1-target genes and SmcHD1-dependent genes associate with the set of slow-silencing genes.

Of note, our categories of SmcHD1 dependency were in fact defined in a previous study (Gdula et al., 2019) from a different cellular model (SmcHD1 KO MEFs).

The authors hypothesise that SmcHD1 might play a role in the eviction of YY1 in NPC differentiation. The current data shows impaired silencing of slow silencing genes and YY1-dependent genes in the SmcHD1 knock-out. However, it doesn't show SmcHD1 is required for YY1 eviction. Could the authors provide direct evidence for their hypothesis by performing NPC differentiation in wild type and SmcHD1 knock-out cells and investigate YY1 binding using ChIP-seq?

The data we show in FigS4 is ATAC-seq data. It shows that YY1 target REs are particularly more accessible from the Xi in SmcHD1 KO, which is not direct evidence but does align with a potential role for SmcHD1 in mediating removal of YY1 binding from Xi (see our response to Reviewer #2’s comment 2.). We agree that YY1 ChIP-seq over the same time course would be an interesting experiment, but arguably this would also only be indirect evidence (ie increased Xi YY1 enrichment may be due to a confounding consequence of SmcHD1 KO). We therefore believe the full suite of experiments needed to rigorously test the hypothesis are beyond the scope of this paper.

In figure S4A and S4B no significance is indicated among the different conditions across the different differentiation days. Could the authors add this?

At all timepoints, differences of Xi accessibility between YY1-binding vs non-YY1 REs are significant. P values are now added to FigS4 and the statistical test is described in the legend.

Finally, we would like the authors to elaborate in the conclusion about the order of events. As they correctly state at the top of page 5 (and we agree), delayed loss of promoter accessibility compared to gene silencing does not automatically mean that it is downstream of gene silencing. Can you elaborate on this? Also, in light of Fig S2C where loss of YY1 binding seems to happen after gene silencing.

We mention in the text and in the above response to Reviewer #2 (point 2.) that we do not wish to overinterpret this quantitative difference because the assays are technically different and accessibility is not linearly correlated with gene expression.

It is possible to speculate plausible biological explanations for this discrepancy in kinetics between accessibility loss, TF binding and gene silencing. For example, a change in the landscape of histone modifications at a promoter may have little effect on its accessibility to TFs but directly hinder RNA Polymerase II in initiation and/or elongation of transcription of the gene. However, we prefer to keep this speculation out of the main text of the paper.

Reviewer #3 (Significance (Required)):

This manuscript highlights a novel role for YY1 in XCI. The manuscript provides an analysis of the correlation and causation of YY1 in gene silencing during XCI. There is a clear correlation between YY1 and delayed silencing of genes on the Xi. To our knowledge, this is the first time such an analysis has been performed for YY1. It advances our conceptual and mechanistic understanding of gene silencing kinetics and what the factors involved in it are. We believe it is an important contribution to the XCI field and will be of great value to the XCI community.

Strength:

This study presents a comprehensive and in-depth characterization of X-linked gene silencing during XCI.

Two different types of inducible XCI are studied and compared (ESCs vs differentiation towards NPCs), which we are grateful for.

Systematic and stepwise analysis of the data is very strong.

Many data points have been collected which provide stronger conclusions.

Weakness:

Some sentences in the abstract should be toned down.

YY1 eviction on the inactive X doesn't seem crucial to establish X-linked gene silencing in mESCs.

The mechanistic approach at the end of the manuscript with relation to SmcHD1 could be studied further.

This paper will be suited for a specialised audience in XCI and transcription factor control of gene expression, i.e. basic research.

Field of expertise: XCI, epigenetics, Xist, gene silencing, X chromosome biology.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Bowness and colleagues describe the interesting finding that the transcription factor YY1 is associated with slow silencing genes in induced X-Chromosome Inactivation (XCI). The authors have conducted a comprehensive characterization of X-linked gene silencing and the loss of chromatin accessibility of regulatory elements in induced XCI in ESCs and during NPC differentiation. X-linked gene silencing was classified into four categories, ranging from fast-silenced genes to genes that escape silencing. Motif enrichment analysis of regulatory elements associated with slowly silenced genes identified YY1 as the transcription factor most significantly enriched. The separation of YY1-target and non-target genes confirmed that most genes bound by YY1 indeed exhibit slower silencing kinetics. A comparison of the binding kinetics of YY1 to another transcription factor, OCT4, during XCI revealed that YY1 is evicted more slowly compared to OCT4 on the inactive X, suggesting that slower eviction is a unique property of YY1. Conditional knock-outs of YY1 using protein degradation during induced XCI in mESCs demonstrated that the loss of YY1 at target genes enhances silencing. This supports the hypothesis that YY1 serves as a crucial barrier for slow-silenced genes during XCI. Finally, the authors propose a hypothesis regarding the mechanism of YY1 eviction, suggesting a potential connection to the role of SmcHD1 during XCI.

The authors provide an in-depth analysis of the role of YY1 in gene silencing kinetics during induced XCI and believe this manuscript should be published if our comments are addressed.

Major comment:

Based on the allelic ratio in figure 3C only minor loss of YY1 binding occurs in induced XCI in mESCs on the Xi, while silencing is established properly as shown in figure 4C (left panel, red boxplots). This suggests that YY1 eviction is not necessarily required for these genes to be effectively silenced. Could the authors explain this discrepancy in the data regarding their manuscript conclusions? It seems this is true for XCI happening during differentiation towards NPCs, but not if cells are stuck in the pluripotency stage?

Minor comments:

In the abstract lines 7-8, the authors state that the experiments were performed in mouse embryonic stem cell lines, but much of the data shown is acquired in NPC differentiations. Please adjust abstract.

The last sentence of the abstract states that YY1 acts as a barrier to silencing but as stated in my major comment, that does seem to be the case in ESC differentiation towards NPCs, but not in ESCs themselves. Please tone down this sentence. Moreover, we do not fully understand where the 'is removed only at late stages' comes from? Is this because of the Smchd1 link? We find this link quite weak with the data presented. We would tone down that last abstract sentence.

Several comparisons to human XCI have been made in the article. We do agree that there are similarities between mouse and human XCI. However, there is insufficient data that substantiates that these genes are regulated in a similar manner in humans. We believe the comparisons should be removed altogether or attenuated.

At bottom of page 4, the authors say that for any given gene, the allelic ration of accessibility at its promoter decreased more slowly than it silenced and then write Fig 1B. They probably mean S1C? Since 1B only shows 4 genes.

Figure 1B shows the average allelic ratio of multiple clones for genes representing different silencing speeds. Each data point is the average of multiple clones for these representative genes, could the authors show the individual data points or the standard deviation?

Figure 1B. Loss of promoter accessibility lags behind loss of chromatin-associated RNA expression for these 4 genes. What about distal REs? Do the allelic ratios for the distal REs more closely follow chromatin-associated RNA expression? Could the authors show this in a supplemental figure?

Figure 1B: gene silencing trajectory is depicted left while the legend says right. Same for promoter accessibility.

Figure S1A shows only part of the X chromosome. The area downstream of Xist is missing. Is this because the iXist-ChrXDom cell line is missing allelic resolution as shown in figure S2A? Could the authors explain in the figure legend that part of the X-Chromosome is missing?

Figure 2C shows that 94 TSSs bear a YY1 peak, yet Fig 2F shows 62 are targets of YY1. Is this because the rest are not properly silenced or are escapees?

Moreover, YY1 has ~4-fold more peaks on the X chromosome on distal elements compared to promoters. Yet figure 2F exclusively shows the proportion of YY1 binding sites on TSSs. Would distal REs show similar proportions for the silencing categories? Could the authors show the differences in a Supplemental figure?

The authors switch between different model systems in the figures, which makes quite confusing which type of XCI is being discussed. We would like to see clearly stated above all panels which cell culture condition is being studied (mESCs or NPCs).

In Figure 3E and 3F the authors look at the binding retention of OCT4 during XCI in ESCs. However, it is not clear why the authors choose OCT4. Could the authors explain why specifically OCT4 was chosen for these analyses?

What is the expression level of YY1 in NPCs compared to mESCS? In Supplemental S2A, it seems that YY1 protein levels decrease over time during NPC differentiation. Is part of the increased eviction a result of lower protein levels of YY1? Probably not since you calculate ratios between Xi and Xa. Can you please comment on this?

On page 7 the authors state that degrading YY1 does not affect Xist spreading and/or localisation. Indeed, it has been previously shown by other groups that YY1 is required for Xist localisation during XCI. Could the authors elaborate further on the why their cells behave differently compared to the Jeon 2011 paper?

In figure 4G and figure S3D elevated levels of Xist are observed in the dTAG conditions. As the authors point out, this could then result in accelerated silencing of the X seen upon YY1 loss. Are these elevated Xist levels that result in enhanced silencing in figure 4 relevant for the kinetics of silencing? Moreover, YY1 could act as transcriptional regulator of those genes in the X and by removing YY1, one would expect decreased transcription, which would be read as accelerated silencing. The authors could see whether the genes that show accelerated silencing are regulated by YY1 in ESCs (+ dTAG, - Dox).

Can the authors explain why they decided to put the Smchd1 part after the conclusion? Before the conclusion would have been better? The probable link between YY1 and SmcHD1 is definitely something important to investigate.

In the paper the authors cite Bowness et al., 2022. In it, Figure 5F studies silencing times with respect to silencing dependency on SmcHD1. What is the overlap between SmcHD1 target genes and YY1 target genes? This would provide more data about the correlation between YY1 and SmcHD1.

The authors hypothesise that SmcHD1 might play a role in the eviction of YY1 in NPC differentiation. The current data shows impaired silencing of slow silencing genes and YY1-dependent genes in the SmcHD1 knock-out. However, it doesn't show SmcHD1 is required for YY1 eviction. Could the authors provide direct evidence for their hypothesis by performing NPC differentiation in wild type and SmcHD1 knock-out cells and investigate YY1 binding using ChIP-seq?

In figure S4A and S4B no significance is indicated among the different conditions across the different differentiation days. Could the authors add this?

Finally, we would like the authors to elaborate in the conclusion about the order of events. As they correctly state at the top of page 5 (and we agree), delayed loss of promoter accessibility compared to gene silencing does not automatically mean that it is downstream of gene silencing. Can you elaborate on this? Also, in light of Fig S2C where loss of YY1 binding seems to happen after gene silencing.

Significance

This manuscript highlights a novel role for YY1 in XCI. The manuscript provides an analysis of the correlation and causation of YY1 in gene silencing during XCI. There is a clear correlation between YY1 and delayed silencing of genes on the Xi. To our knowledge, this is the first time such an analysis has been performed for YY1. It advances our conceptual and mechanistic understanding of gene silencing kinetics and what the factors involved in it are. We believe it is an important contribution to the XCI field and will be of great value to the XCI community.

Strength:

This study presents a comprehensive and in-depth characterization of X-linked gene silencing during XCI.

Two different types of inducible XCI are studied and compared (ESCs vs differentiation towards NPCs), which we are grateful for.

Systematic and stepwise analysis of the data is very strong.

Many data points have been collected which provide stronger conclusions.

Weakness:

Some sentences in the abstract should be toned down.

YY1 eviction on the inactive X doesn't seem crucial to establish X-linked gene silencing in mESCs.

The mechanistic approach at the end of the manuscript with relation to SmcHD1 could be studied further.

This paper will be suited for a specialised audience in XCI and transcription factor control of gene expression, i.e. basic research.

Field of expertise: XCI, epigenetics, Xist, gene silencing, X chromosome biology.

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Referee #2

Evidence, reproducibility and clarity

The authors studied the molecular basis of a variation in the rate of individual gene silencing on the X undergoing inactivation. They took advantage of ATAC-seq to observe the kinetics of chromatin accessibility along the inactive X upon induction of Xist expression in mESCs. They demonstrated a clear correspondence between the decrease in chromatin accessibility and the silencing of nearby genes. Furthermore, they found that persistently accessible regulatory elements and slow-silencing were associated with binding of YY1. YY1 tended to associate longer with genes that required more time to be silenced than those that became silenced fast on the inactive X during XCI. The acute loss of YY1 facilitated silencing of slow genes in a shorter period. They suggest that whether or not the transcription factors stay associated longer is another factor that impacts the variation in the rate of gene silencing on the Xi.

Significance

It has been suggested that the rate of gene silencing during XCI is varies depending on the distance of individual genes from the Xist locus or the entry site of Xist RNA on the X, as well as their initial expression levels before silencing. This study provides another perspective on this issue. The persistent association of transcription factors during XCI affects the rate of gene silencing. Although the issued addressed here might draw attention from only the limited fields of specialists, their finding advances our understanding of how the efficiency of silencing is controlled during the process of XCI. The experimental data essentially support their conclusion, and the manuscript was easy to follow. However, I still have some comments, which I would like the authors to consider before further consideration.

Major concerns

Based on the results shown in Figure 3E and F, the authors concluded that YY1 was more resistant than other TFs against the eviction from the X upon Xist induction. I am not still convinced with this. YY1 binds DNA via the zinc finger domain, while Oct4 binds DNA via the homeodomain. The difference in the binding module between them might affect their dissociation or the response to Xist RNA-mediated chromatin changes. In addition, given that YY1 has been reported to bind RNA, including Xist, as well, Oct4 might not be a good TF to compare.

I don't think that Kinetics of YY1 eviction upon Xist induction in SmcHD1 KO cells during NSC differentiation fit the phenotype of Smchd1mutant cells. Although their previous study by Bowness et al (2022) showed that Smchd1-KO cells fail to establish complete silencing of SmcHD1-dependnet genes, their silencing still reached rather appreciable levels according to Figure 6 of Bowness et al (2022). This is, in fact, consistent with the idea that XCI initially takes place in the mutant embryos, at least to an extent that does not compromise early postimplantation development. On the other hand, a significant portion of YY1 appears to remain associated with the target genes on both active and inactive X (Figure S4), which I think suggests that the presence of YY1 is compatible with silencing of SmdHD1-dependent genes. This is contradictory to the proposed role of YY1 that sustains the expression of X-linked genes in this context.

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Referee #1

Evidence, reproducibility and clarity

Summary: This manuscript uses differentiation of the highly informative inter-specific hybrid mouse ESC to follow features of genes that inactivate slowly. Resistance to silencing is reflected in reduced change in chromatin accessibility and the authors identify YY1 and CTCF as enriched amongst these 'slow' genes. This finding is provocative as these factors have been reported to enrich at both human and mouse escape genes. The authors go on to demonstrate that eviction of YY1 is slowly evicted from the X, and that removal of YY1 increases silencing.

Minor Comments:

Overall, the manuscript's conclusions are well supported; however, the brevity of the presentation in some places made it difficult to follow, and in other places seemed a missed opportunity to more fully examine or present their data.

1. Introduction is only 2 paragraphs and half of the last is their new findings. First part of results/discussion is then forced to be very introductory. In addition, some discussion of escapees, even if predominantly human, seems warranted in the introduction. There are multiple studies that have tried to identify features enriched at genes that escape inactivation that could be mentioned.
2. Variation in silencing rates. 'Comparable rankings' cites multiple studies (oddly previous sentence cites only two) - how concurrent are they? Developing this further (perhaps a supplementary table) would inform whether the genes assessed are ones that routinely behave similarly across different studies/lines; and also serve as a resource for future studies.
3. It would be helpful to give insight into informativity of cross - what proportion of ATAC-seq peaks were informative with allelic information (and similarly, what proportion of genes expressed had allelic information?
4. P5: "can be influenced by Xist RNA via a variety of mechanisms" seems like it this sweeping statement could use expansion, or at least a reference. Authors could also clarify that 'distal elements assigned by linear genomic proximity is their definition of nearest gene.
5. Figure S1 - there are 6-8 other regions that fail to become monoallelic - what are they?
6. Is there any correlation between silencing speed and expression (as previously reported)? If yes, then is there also a correlation with YY1 presence - and is this correlation greater than or less than seen on autosomes?
7. Figure 2: Have the authors considered using quartiles rather than an arbitrary division into depleted and persistent? B. Could simplify secondary labels to solely YY1 and CTCF. D & F do not print in black and white. Overall the mESC versus NPC can be confusing, perhaps mESC (no diff) would be helpful?
8. The numbers appear to suggest YY1 is generally enriched on X, but not at promoters?? Is this true? For Figure 2f, it might be helpful to show autosomal genes - are Fast depleted or Slow enriched for YY1 relative to autosomes? More generally, is YY1 binding on the X lost more slowly than YY1 binding on autosomes, or is the slow loss a feature of YY1. While I agree YY1 could have direct up or down-regulatory roles, Figure S3 could also be reflecting a secondary impact.
9. Figure 3, 4 and supplementary - the chromosome cartoon introduces the LOH in iXist, but this needs to be described in text. Describing the reciprocal as a biological replicate seems challenging given this LOH.
10. Could a panel of TFs be used rather than OCT4 which has its own unique properties to emphasize that YY1 is unique?
11. Figure 4 - by examining 'late' genes, a change in allelic ratio is observed, but what about escape genes (e.g. Kdm5c, Kdm6a)? Do they now become silent? It would be helpful to have all this data as a supplementary table so people could query their 'favorite' gene.
12. It seems surprising that loss of YY1 has no demonstrative impact on the Xa. Figure S3B suggests that over 1000 genes are significantly impacted - primarily down regulated. How many of those are X-linked? Perhaps they could be colored differently?
13. Since XIST+/undifferentiated cells retain YY1, is YY1 binding sensitive to DNAme? Indeed, are X chromosome bound sites in islands that become methylated? Figure S4 shows YY1-targetted X genes in SMCHD1 knockout; can CTCF targets also be shown? While identified in Figure 2, CTCF was not examined the way YY1 was, although it has also been identified in somatic studies of genes that escape X inactivation.
14. When the authors use cf. do they simply mean see also, or as wikipedia suggests: "the cited source supports a different claim (proposition) than the one just made, that it is worthwhile to compare the two claims and assess the difference". Perhaps it would be worth spelling out to clarify for the audience.

Significance

General assessment: An important question in human biology is how much the sex chromosome contributes to sex differences in disease frequency. Genes that escape X inactivation in humans seem to have considerable impact on gene expression genome-wide. While there are not as many genes in mouse that escape inactivation, the use of the mESC cell differentiation approach allows detailed assessment of the timing of silencing during inactivation. The authors utilize an inter-specific cross and it would be interesting to know the limitations of such a system (in terms of informative DHS/genes that are informative).

Advance: As the authors note, there are multiple studies of similar systems that have revealed differences in the speeds of silencing of genes. However, this is the first study to my knowledge that has then tried to assess timing with gene-specific factors. There are multiple studies in humans comparing escape and subject genes for TFs, but lacking the developmental timing that this study incorporates.

Audience: While generally applicable to a basic research audience interested in gene regulation, the applicability to human genes that escape inactivation may interest cancer researchers or clinical audiences interested in sex differences.

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Reply to the reviewers

General Statement We very much appreciate the reviewers' thorough comments and are sincerely grateful for their kind remarks on the novelty and interest of our manuscript. We are confident to have addressed all the points that they have raised including new data, as well as revised figures and text.

Point-by-point description of revisions All the revisions have been already carried out and included in the transferred manuscript.

Reviewer #1

Major comments:

> The number of the replicates/animals for the experiments described in Figures 1 and 2 should be reported either in the figure legends or in the methods (statistical analysis). We have added the required numbers to the corresponding revised figures, as requested.

> A relevant part of the discussion repeats what the authors have already said in the results. I would recommend to reorganize this section, emphasizing the importance of these results in the context of human brain tumors.

Following our own style, we have written a very short (46 lines in length!) Discussion. We dedicate a few lines to highlighting two points: (1) the suggestion, derived from our allograft experiments, that the initial stages of tumour development and long-term tumour growth may be molecularly distinct events, and (2), the unique effect of the combined loss of TrxT and dhd on mbt tumour transcriptomics -unique because none of the suppressors of mbt reported before are as effective in erasing both the MBTS and SDS mbt signatures. Neither of these points are raised in Results. In the remaining few lines we put our results in the context of human Cancer/Testis and elaborate on the fact that the TrxT and dhd pair qualify as head-to-head, CT-X genes, like those reported in human oncology. This is as far as we are willing to go at this stage at emphasizing the importance of our results in the context of human tumours.

Reviewer #2

> 1. Figures should include information regarding the sex of the larvae, particularly as there has been a previously reported sex-linked effect in the phenotypes analysed. (e.g. in Figure 2 and Figure S1, where Indication of the sex of the animals should be provided in the figure OK and not just in the figure legend). We fully agree. Sex must always be taken into account as a biological variable. All the experiments reported in the manuscript were carried out with sexed samples, and were annotated accordingly in the original text. In compliance with the reviewer's request we have added this information also to the revised figure.

*> 2. Data regarding fertility. Can this be shown in a table format? Are dhdKO females fully sterile? What are the fertility levels of Df(1)J5? * Please note that we are not discovering anything here but merely corroborating what has been published before: the lack of TrxT does not affect fertility in either sex; the lack of Dhd results in female sterility (Torres-Campana et al., 2022, Tirmarche et al., 2016, Svensson et al., 2003, Pellicena-Palle et al., 1997). Adding a table would not be justified. Moreover, it would be a rather simple table: all single-pair mating tests (n=10 for each genotype) with Trxt KO and Dhd KO males, and TrxT KO females were as fertile as control flies, while all single-pair mating tests (n=10) with Dhd KO females were sterile.

> 3. Are dhd and TrxT the only genes affected by Df(1)J5? Is there transcriptional data from Df(1)J5 animals to suggest that nearby genes are not affected by the deficiency? Of particular interest would be to assess if snf is affected or not as it is a known regulator of gene expression and splicing. Yes dhd and TrxT are the only genes affected by Df(1)J5. That is the case according to Flybase (citing Svensson et al., 2003, and Salz et al., 1994) and confirmed by our own RNAseq data. No other transcripts, including snf, are affected by Df(1)J5.

> 4. In Figure 1C, statistical test plus indication of significance is not presented. The requested statistical test and significance data have been added as required to the revised figure and figure legend.

> 5. Related to Figure 1D. Additional neural markers could be assessed in dhdKO and TrxTKO flies. Whilst the gross morphology of the brain does not seem to be affected, there is a possibility that cell specification is affected. Specific markers for the NE, MED and CB could be used to assess this in more detail, particularly as the DE-cad images shown for dhdKO and TrxTKO flies seem to differ slightly from the control. We believe that there may be a small misunderstanding here. We have made this point clear in the revised version by referring to substantial published data showing that expression of these two genes is restricted to the germline and that, female fertility aside, TrxT and dhd deficient flies' development and life span are perfectly normal. If anything, Figure 1D is redundant. However, we would rather keep it as a control that our CRISPR KO mutants behave as expected.

> 6. Related to Figure 2A, images from TrxTKO; l(3)mbtts1, dhdKO and l(3)mbtts1 should be added at the very least in a supplementary figure. Additionally, data for NE/BL ratio should be provided for dhdKO, TrxTKO and Df(1)J5 in the absence of l(3)mbtts1 tumours. Related to Figure S1, quantification of NE/BL ratio for female lobes should be added to the figure. All the requested images and data have been included in the revised version in new figures Figure S2B, Figure S2A, and Figure S1A.

> 7. Related to Figure 2B and Figure S1, three rows of images are presented for each genotype. It is unclear whether these correspond to brain lobes from different larvae or different confocal planes from the same animal. This should be clarified in the figure and/or figure legend. This point has been clarified as requested in the revised figure legend. Each group of three rows correspond to brain lobes from different larvae of the same genotype.

> 7 cont. Related to this, in addition to the anti-DE-cadherin data, it would be informative to include immunofluorescence data using antibodies such as anti-Dachshund (lamina), anti-Elav (medulla cortex) and anti-Prospero (central brain and boundary between central brain and medulla cortex) (as assessed in e.g. Zhou and Luo, J Neurosci 2013) in the mbt tumour situation to accurately describe regions disrupted by the tumours. There is no denying that taking advantage of the many cell-type specific markers that are readily available in Drosophila could be of interest. The same applies to cell cycle markers like PH3, FUCCI, and many others. However, we believe that interesting as they may be, none of this markers will give us the clue on the molecular basis of TrxT and Dhd tumour function that is, of course, the open burning question that we are trying to address now.

> 8. Authors should clarify how the NE was defined when mbt tumours are generated, as it is severely affected. From the images provided, it is unclear which region corresponds to NE or how the NE/BL ratio was measured. It would be helpful to outline these regions in the images or, as mentioned above, use antibodies to define them. The figure has been modified to include the requested outlines defining the NE that indeed is correspond to the channel showing DE-Cadh staining.

> 9. Figure 2C does not have indication of statistical significance for the comparisons stated in the text. Potential explanations for the different roles of Dhd and TrxT in long-term tumour development should be explored in the discussion. The requested statistical significance data for these comparisons were stated in the second last paragraph of that section. To make these data more prominent we have also added this information to revised Figure 2C.

>9 cont. Related to this, does the analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals reveal why they have similar effect on mbt tumour development but do not synergistically contribute to long-term growth? Unfortunately our analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals does not give us any clue that could help us understand why they have similar effect on mbt tumour development, but not in long-term growth (allografts). To further explore this point, we have added new Figure S3 that includes a Venn diagramme showing the overlap between the affected mMBTS genes in TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1, together with the lists of enriched GOs among overlapping and non-overlapping genes. GO differences are tantalising, indeed, However, they do not immediately suggest any direct explanation for the different roles of Dhd and TrxT in long-term tumour development.

> 10. Authors should clarify if there is any overlap between the affected M-tSDS and F-tSDS in the TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 conditions. Would the limited overlap suggest that TrxT and dhd act in parallel rather than synergistically? This might also explain the differential effects on long-term tumour development. Additionally, the stronger effect observed in Df(1)J5 animals may be due to TrxT and dhd functional redundancy. Currently, there is limited evidence to suggest that TrxT and dhd act synergistically to regulate mbt tumour growth based on the presented data. See below.

> 11. Authors should include a Venn diagram depicting affected genes (M-tSDS and F-tSDS) in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1 and Df(1)J5; l(3)mbtts1 genotypes as this could clarify the percentage of overlap of gene signatures in these different conditions. Related to this point, authors could provide results from GO analysis to investigate whether specific functional clusters are altered in the different conditions. We have taken the liberty of fusing points 10 and 11 that are conceptually similar. The requested Venn diagrams showing the overlap between the affected M-tSDS and F-tSDS genes in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, and Df(1)J5; l(3)mbtts1 conditions, and GO analysis are now shown in new Figure S5. Unfortunately, these new data do not suggest any obvious explanation for the differential effects of these two genes, nor do they allow us to derive any further conclusions regarding the nature of the pathways through which TrxT and dhd cooperate to sustain mbt tumour growth. However, our analyses demonstrate that efficient suppression of mbt phenotypic traits (in larval brains) and transcriptome requires the combined elimination of both germline thioredoxins, while the effect of individual removal of either of them is only partial. These data demonstrate the synergistic nature of TrxT and dhd function in mbt tumour growth.

> 12. In Figure 3E, authors should indicate more explicitly in the figure panel and/or figure legend which genes display significant differences in expression in the different samples. We apologise for not having made this point clear in the original version: All (21) genes shown in this Table are significantly downregulated in DfJ5;ts1 vs ts1. From these, nanos and Ocho are also significantly downregulated in TrxTKO;ts1 vs ts1, and Ocho, HP1D3csd, hlk, fj, Lcp9, CG43394, and CG14968 are significantly downregulated in dhdKO;ts1 vs ts1. These data have been included in the revised figure legend. Data on all other comparisons are included in Table S1.

> 13. In Figure S2C-F it is not clear if the graphs represent data from all tissues or data from male and female tissues separately, as shown in Figure 4. Apologies for the confusion. All samples were from male tissues as indicated in the original figure legend. To make it more clear, we have labelled all four panels in the revised figure.

> 14. Are TrxT and dhd also deregulated in other tumour types? Or is this specific for mbt tumours? This information could be provided to enhance the scope of the manuscript. Thank you for raising this point. TrxT and dhd are not dysregulated in the other tumour types that were analysed in Janic et al., 2010 (i.e pros, mira, brat, lgl and pins).

> 15. Authors conclude that TrxT and dhd cooperate in controlling gene expression between wild-type and tumour samples and that they act synergistically in the regulation of sex-linked gene expression in male tumour tissue. However, the link between the two observations (if indeed there is a link) has not been well explained. Is the effect on gene expression in tumours simply a result of the regulation of sex-linked transcription? Our data show that TrxT and dhd synergistically contribute to the emergence of both the MBTS (i.e tumour versus wild type) and SDS (i.e. male tumour versus female tumour). The only certainty at this time regarding the interconnection between both signatures is that they overlap, but only partially, which answers one the questions raised by the reviewer: the effect on gene expression in tumours is not simply a result of the regulation of sex-linked transcription. Beyond that, the link (if indeed there is a link) between these two signatures has not been investigated. The lack of insight on this issue is not surprising taking into account that, in contrast to classical tumour signatures (tumour versus healthy tissue), the concept of sex-linked tumour signatures is relatively new and only a handful of such signatures have been published. Moreover, the vast majority of classical tumour signatures have not been worked out in a sex-dependent manner.

Reviewer #3 Comments: > - In the first section of the results, as a first step to study the role of TrxT and dhd genes on mbt tumors the authors generate CRISPR knock outs of these genes and correctly validate them. However, afterwards, the experiment where the authors test the KO of these genes in a wild-type larva brain is not contextualized with the rest of the section. It might be best to first address the role of these genes in a tumor context and only then complement with the experiments in wild-type (in supplementary material). We do appreciate the reviewer's view, but respectfully disagree. In our opinion, the manuscript flows better by presenting the tools that we have generated in Figure 1, By corroborating published data showing that these two germline genes do not affect soma development (Torres-Campana et al., 2022, Tirmarche et al., 2016, Svensson et al., 2003, Pellicena-Palle et al., 1997) this first figure not only validates our CRISPR KO mutants, but also sets the stage to highlight their significant effect on a somatic tumour like mbt.

> - Fig 2 B - To back up the quantifications in Fig 2A the authors could include images of l(3)mbt ts1 tumors with TrxT KO and dhd KO also. The requested images are shown in new figure Figure S2B.

> Fig 2 B and C - Indeed, the results suggest that TrxT seems to be responsible for most tumor lethality upon l(3)mbt allografts, but not dhd. This is curious since l(3)mbt; dhd KO brain tumors have the same partial phenotype as l(3)mbt; TrxT KO (fig 1A). It would be interesting to further explore these phenotypes by staining l(3)mbt; TrxT KO and l(3)mbt; dhd KO brains with, for instance, PH3 to understand if the number of dividing cells of these tumors could be different. In addition, to back up this information, the authors could look at what happens to l(3)mbt tumors with TrxT KO and dhd KO at a later stage of development (or to larva or pupa lethality if that is the case) and compare it with l(3)mbt brains. We did explore the possibility of looking at later stages. Unfortunately, the onset of the lethality phase compounded by major tissue reshaping from larval to adult brain make these stages unsuitable to reach any meaningful conclusion. With regards to staining for PH3, we think that like FUCCI and a long list of other useful labels that could be explored, it is potentially interesting, but hardly likely to give us the clue on the molecular basis of TrxT and Dhd tumour function, that is of course the one important question that we are addressing now.

> - Fig 2 B - What happens to the medulla in a l(3)mbt brain tumor? Although the ratio of NE/BL is the same for wild-type and D(1)J5; l(3)mbt, it still seems that the medulla in D(1)J5; l(3)mbt brains is substantially bigger, although quantifications would be required. Do the authors know if the NE in D(1)J5; l(3)mbt brains is either proliferating less or differentiating more? There are no significant differences in medulla/BL nor in CB/BL ratios. The corresponding quantifications have been added to the revised version. As for the question on proliferation versus differentiation, the simple answer is that we do not know.

> Figure S1 - Although the effects of TrxT KO and dhd KO in male mbt tumors seem to be enhanced in relation to female tumors, the authors should include some form of tumor quantification for female tumors like in Fig 2 A. We have carried out the requested quantifications and added the results in a new panel in revised Figure S1A.

Moreover in the 2nd section of the results, relative to Fig 1S in "...Df(1)J5; l(3)mbtts1 female larvae although given the much less severe phenotype of female mbt tumours, the effect caused by Df(1)J5 is quantitatively minor." to say "quantitatively" minor, the authors should include not only quantifications, but a form of comparison between female tumors vs. male tumors. The requested quantification was published in Molnar et al., 2019. However, we agree on the convenience of doing it again with our new samples. The new data, that confirm published results, are now shown as a new panel in revised Figure S1C.

> - Fig 3D - The hierarchical clustering was done according to which parameters? A brief explanation could help a better interpretation of this results section. The requested information has been added to the Methods section. Hierarchical clustering was done using the function heatmap.2 in R to generates a plot in which samples (columns) are clustered (dendogram); genes (rows) are scaled by “rows"; distance = Euclidean; and hclust method = complete linkage. Expression levels are reported as Row Z-score.

> - Fig 3D - It could be beneficial for the authors to include an analysis of the downregulated genes shared between TrxT KO mbt tumors and dhd KO mbt tumors, as well as the genes that are not shared (besides MBTS genes). Could be something like a Venn diagram. Thanks for pointing this out. New Figure S3 shows the requested Venn diagram, as well as the list of enriched GOs for each group.There are no enriched GOs in the list of overlapping genes. TrxTKO; l(3)mbtts1-specific genes are enriched for GOs related to game generation, sexual reproduction, germ cell development and simlar GOs. dhdKO; l(3)mbtts1 -specific genes are enriched for GOs related to chitin, molting and cuticle development. Tantalising as they are, these observations do not immediately suggest any direct explanation for the different roles of Dhd and TrxT in long-term tumour development. We are happy to add these supplemental information, but we do not deem it worth of any further discussion at this point.

> - Results section 3 - "Expression of nanos is also significantly down-regulated upon TrxT loss, but remains unaffected by loss of dhd" - to corroborate the idea that TrxT and dhd work as a pair, but contribute to different functions within the tumor, it would be interesting for the authors to do an allograft experiment of dhd KO; l(3)mbt male tissue with nanos knock down in the brain, if genetically possible. The suggested experiment is published. The gene in question (nanos) is a suppressor of mbt tumour growth: In a nanos knock down background, l(3)mbt allografts do not grow (Janic 2010).

Minor comments: * > - In the first section of the results, the authors claim that "Consistent with the reported phenotypes of Df(1)J5...", but then the study is not mentioned.* The corresponding references (Salz et al., 1994; Svensson et al., 2003; Tirmarche et al., 2016) have been added.

> - Fig 1 B - It is a bit confusing to follow where TrxT and dhd are in the Genome browser view. I am guessing we should follow the TrxT-dhd locus from A, but the authors could make it clearer. Figure 1 has been changed to make this point more clear.

> - In the same section, in the next sentence, the homozygous and hemizygous is a bit confusing. "...homozygous TrxTKO females, dhdKO males, and TrxTKO males", should be corrected. We appreciate the suggestion, but would rather stick to classical terminology and refer to KO/KO females as homozygous and to KO/Y males as hemizygous.

>- In the same section (Fig 1C): "RNA-seq data also shows that TrxT is significantly upregulated in l(3)mbtts1 males compared to females (FC=7.06; FDR=1.10E-44) while dhd is not (FC=1.89; FDR=2.00E-14)." - But dhd is nevertheless upregulated, although less, in l3mbt males, right? The authors might need to rephrase. We refer to comparing males versus females, not wild type versus tumours. The text has been rephrased in the revised version to make this point clear.

> - Fig 2 A (quantifications), should be after the confocal images (Fig 2 B). We respectfully disagree on this minor point. We initially organised this figure in the order recommended by the reviewer, but we eventually found it easier to write the article using the order shown in the submitted figure. We would rather stick to this version.

> - Fig 2 B and Fig S1 - Please include an outline of at least neuroepithelia and, if possible, Central brain or medulla so that these regions can more clearly identified. Moreover, these results will be easier to interpret if you add a male symbol in this image and a female symbol in Figure S1, otherwise, it might seem like the same figure Outlines and symbols have been added to the revised figure, as required.

> - In results, section 2, "Consequently, in spite of the strong sex dimorphism of mbt tumours, the phenotype of Df(1)J5; l(3)mbtts1 larval brains is not sexually dimorph" - to back this up, quantifications of Df(1)J5; l(3)mbtts1 female vs male tumor size, as well as statistical analysis are needed, like previously said. The requested the new data is now shown in revised Figure S1C.

> - In results section 2 - "For allografts derived from, female larvae, we found that differences in lethality rate caused by TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, Df(1)J5; l(3)mbtts1, and l(3)mbtts1 tissues (7-23%) were not significant (Figure 2C)" - there is no statistical analysis to conclude that the lethality rate is not significant, from 7% to 23% still seems like a difference. Thanks for pointing this out. We did of course generate the requested statistical analysis data, but failed to include it in the manuscript. Chi-square statistical test gives a p value=0.2346. These data have been added to the revised version.

> - Last paragraph of section 2 of results - very long and confusing sentence. Please rephrase text. We have rephrased this sentence to make it shorter and clearer.

> - On section 3 of results: "The vas, piwi and CG15930 transcripts are not significantly down-regulated following either TrxT or dhd depletion alone." - in Fig 3E, not only these transcripts seem to suffer a slight downregulation, but there is also no statistical analysis supporting this. There seems to be a misunderstanding here. The requested statistical data for each gene were shown in Table S1

> - First paragraph of section 3 results - the first sentence is written in a confusing way. Moreover, more context is needed in the sentence afterwards: "we first focused on transcripts that are up-regulated in male mbt tumour samples compared to male wild-type larval brains (mMBTS)." but using which data? The RNA seq data? Agreed; this paragraph has been amended in the revised version.

> - Brief conclusion missing on the second paragraph of the last section of results. As far as the results presented in this paragraph are concerned, we can only mention the two potentially interesting observations, which were pointed out in the original version: (i) the suggestion that nanos upregulation could be critical for sustained mbt tumour growth upon allograft, and (ii) the fact that three genes (vas, piwi and CG15930), also known to be required for mbt tumour growth, are downregulated in Df(1)J5; l(3)mbtts1, but remain unaffected following either TrxT or dhd depletion alone. We are unable to derive any other conclusion from these observations.

> - In the end of 3rd paragraph of last section of results: "...M-tSDS and F-tSDS genes is partially reduced in l(3)mbtts1 brains lacking either TrxT or dhd, but it is completely suppressed upon the lack of both." - "completely" might not be a correct word to use in this case, as there is still some small differences As requested, we have changed "completely" for "strongly".

> - 4th paragraph of last section of results: Either mention the male results and then female (to be in order with the figure, as the female graphs come after the male graphs) or change the order in the figure. Also, this paragraph is not very clear, could benefit from a better explanation of the results and conclusions. Point taken. Figure 4 has been changed and female graphs come before male graphs. The paragraph is clearer now. The conclusion from this paragraph is included in the final paragraph of this section.

> - Fig 4 C,D,E,F: to make it more clear, please write the name of the genotypes in question in the figure. At the reviewer's request, the genotypes in question are now written in each panel. Please note that we did not do so before because all four panels correspond to the same genotype: Df(J5); l(3)mbtts1 vs l(3)mbtts1, as we mentioned in the original figure legend.

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Referee #3

Evidence, reproducibility and clarity

Summary:

• In this manuscript, the authors address the role of the thioredoxins Dhd and TrxT in the development and growth of mbt tumors, a sexually dimorphic brain tumor that derives from the expansion of the neuroephitelium. To this end, the authors have successfully generated dhd and TrxT knock-out mutants using CRISPR-Cas9 and show that both dhd and TrxT individual knock-out partially reduces the mbt tumor-associated brain phenotype. Moreover, using Df(1)J5, a deficiency that affects both TrxT and dhd, the recovery of the phenotype is enhanced. However, although concomitant expression of dhd and TrxT is required for proper tumor development, they show that only TrxT is necessary for the growth of allografts derived from male l(3)mbt tumors. This is interesting, not only because TrxT and dhd are never co-expressed in physiological conditions, but also because this data suggests that the pathways leading to l(3)mbt tumor development are different from the ones that contribute to tumor proliferation and aggressiveness. Moreover, the authors show that TrxT and dhd contribute to the emergence of the mbt tumour signature (MBTS) and sex-dimorphic signature (SDS) of tumours by analysing transcriptomic data of TrxT KO; l(3)mbt, dhd KO; l(3)mbt and Df(1)J5; l(3)mbt. In fact, through hierarchical clustering, the authors show that male Df(1)J5; l(3)mbt brain transcriptomic profile becomes closer to wild-type brains than l(3)mbt ts1 tumors.

• This study presents novelty to the cancer research field and both the model and methodology used were appropriate. Nonetheless, this study deals with mbt tumors which are sexually dimorphic, as well as male and female germline-specific genes that in a tumor can alter male and female sex-dimorphic signatures, making this study very easy to become confusing to non-experts in the field if not written in a very clear way. Therefore, the text, especially in the results and discussion section, could be revised in general to improve the comprehension and flow of the manuscript, given that some sentences and paragraphs are hard to follow. In particular, the results section could benefit with more contextualization and a more detailed explanation of experiments. Moreover, the study is lacking some quantifications and a few additional experiments. These issues can certainly be addressed by reviewing the text as well as reorganizing and including a few quantifications and experiments as described below. I am an expert in Drosophila brain development and tumorigenesis.

Comments:

• In the first section of the results, as a first step to study the role of TrxT and dhd genes on mbt tumors the authors generate CRISPR knock outs of these genes and correctly validate them. However, afterwards, the experiment where the authors test the KO of these genes in a wild-type larva brain is not contextualized with the rest of the section. It might be best to first address the role of these genes in a tumor context and only then complement with the experiments in wild-type (in supplementary material).

• Fig 2 B - To back up the quantifications in Fig 2A the authors could include images of l(3)mbt ts1 tumors with TrxT KO and dhd KO also.

Fig 2 B and C - Indeed, the results suggest that TrxT seems to be responsible for most tumor lethality upon l(3)mbt allografts, but not dhd. This is curious since l(3)mbt; dhd KO brain tumors have the same partial phenotype as l(3)mbt; TrxT KO (fig 1A). It would be interesting to further explore these phenotypes by staining l(3)mbt; TrxT KO and l(3)mbt; dhd KO brains with, for instance, PH3 to understand if the number of dividing cells of these tumors could be different. In addition, to back up this information, the authors could look at what happens to l(3)mbt tumors with TrxT KO and dhd KO at a later stage of development (or to larva or pupa lethality if that is the case) and compare it with l(3)mbt brains.

• Fig 2 B - What happens to the medulla in a l(3)mbt brain tumor? Although the ratio of NE/BL is the same for wild-type and D(1)J5; l(3)mbt, it still seems that the medulla in D(1)J5; l(3)mbt brains is substantially bigger, although quantifications would be required. Do the authors know if the NE in D(1)J5; l(3)mbt brains is either proliferating less or differentiating more?

• Figure S1 - Although the effects of TrxT KO and dhd KO in male mbt tumors seem to be enhanced in relation to female tumors, the authors should include some form of tumor quantification for female tumors like in Fig 2 A. Moreover in the 2nd section of the results, relative to Fig 1S in "...Df(1)J5; l(3)mbtts1 female larvae although given the much less severe phenotype of female mbt tumours, the effect caused by Df(1)J5 is quantitatively minor." to say "quantitatively" minor, the authors should include not only quantifications, but a form of comparison between female tumors vs. male tumors.

• Fig 3D - The hierarchical clustering was done according to which parameters? A brief explanation could help a better interpretation of this results section.

• Fig 3D - It could be beneficial for the authors to include an analysis of the downregulated genes shared between TrxT KO mbt tumors and dhd KO mbt tumors, as well as the genes that are not shared (besides MBTS genes). Could be something like a Venn diagram.

• Results section 3 - "Expression of nanos is also significantly down-regulated upon TrxT loss, but remains unaffected by loss of dhd" - to corroborate the idea that TrxT and dhd work as a pair, but contribute to different functions within the tumor, it would be interesting for the authors to do an allograft experiment of dhd KO; l(3)mbt male tissue with nanos knock down in the brain, if genetically possible.

Minor comments:

• In the first section of the results, the authors claim that "Consistent with the reported phenotypes of Df(1)J5...", but then the study is not mentioned.

• Fig 1 B - It is a bit confusing to follow where TrxT and dhd are in the Genome browser view. I am guessing we should follow the TrxT-dhd locus from A, but the authors could make it clearer.

• In the same section, in the next sentence, the homozygous and hemizygous is a bit confusing. "...homozygous TrxTKO females, dhdKO males, and TrxTKO males", should be corrected.

• In the same section (Fig 1C): "RNA-seq data also shows that TrxT is significantly upregulated in l(3)mbtts1 males compared to females (FC=7.06; FDR=1.10E-44) while dhd is not (FC=1.89; FDR=2.00E-14)." - But dhd is nevertheless upregulated, although less, in l3mbt males, right? The authors might need to rephrase.

• Fig 2 A (quantifications), should be after the confocal images (Fig 2 B).

• Fig 2 B and Fig S1 - Please include an outline of at least neuroepithelia and, if possible, Central brain or medulla so that these regions can more clearly identified. Moreover, these results will be easier to interpret if you add a male symbol in this image and a female symbol in Figure S1, otherwise, it might seem like the same figure if one does not properly read the legend.

• In results, section 2, "Consequently, in spite of the strong sex dimorphism of mbt tumours, the phenotype of Df(1)J5; l(3)mbtts1 larval brains is not sexually dimorph" - to back this up, quantifications of Df(1)J5; l(3)mbtts1 female vs male tumor size, as well as statistical analysis are needed, like previously said.

• In results section 2 - "For allografts derived from female larvae, we found that differences in lethality rate caused by TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, Df(1)J5; l(3)mbtts1, and l(3)mbtts1 tissues (7-23%) were not significant (Figure 2C)" - there is no statistical analysis to conclude that the lethality rate is not significant, from 7% to 23% still seems like a difference.

• Last paragraph of section 2 of results - very long and confusing sentence. Please rephrase text.

• On section 3 of results: "The vas, piwi and CG15930 transcripts are not significantly down-regulated following either TrxT or dhd depletion alone." - in Fig 3E, not only these transcripts seem to suffer a slight downregulation, but there is also no statistical analysis supporting this.

• First paragraph of section 3 results - the first sentence is written in a confusing way. Moreover, more context is needed in the sentence afterwards: "we first focused on transcripts that are up-regulated in male mbt tumour samples compared to male wild-type larval brains (mMBTS)." but using which data? The RNA seq data?

• Brief conclusion missing on the second paragraph of the last section of results.

• In the end of 3rd paragraph of last section of results: "...M-tSDS and F-tSDS genes is partially reduced in l(3)mbtts1 brains lacking either TrxT or dhd, but it is completely suppressed upon the lack of both." - "completely" might not be a correct word to use in this case, as there is still some small differences.

• 4th paragraph of last section of results: Either mention the male results and then female (to be in order with the figure, as the female graphs come after the male graphs) or change the order in the figure. Also, this paragraph is not very clear, could benefit from a better explanation of the results and conclusions.

• Fig 4 C,D,E,F: to make it more clear, please write the name of the genotypes in question in the figure.

Significance

This study presents an interesting new concept for Drosophila tumors, the cancer germline genes, which to my knowledge has been a poorly explored field, although it has a lot of potential. It is particularly interesting since it addresses the role of two germline specific thioredoxins, that are dispensable for somatic cells, but have a critical role in somatic mbt tumors, exploring new tumor vulnerabilities. This manuscript will benefit researchers in the field of cancer biology, in particular, to better understand cancer-testis (CT) genes and how they promote tumorigenesis, since the biological function for the most part remains unclear.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Molnar and colleagues is a follow-up from the authors' previously published work (Molnar et al 2019), where they demonstrated differential sex-linked gene expression in Drosophila l(3)mbt brain tumours and identified the thioredoxin proteins TrxT and Dhd in the mbt tumour signature (MBTS). In the current manuscript, the authors generated genetic mutants for both genes using CRISPR TrxTKO and dhdKO and a deficiency that spans both genes (Df(1)J5) to understand the role played by these thioredoxins in normal larval brain development and l(3)mbt tumour development. Both genes were found to be largely dispensable for normal larval brain development, however the authors uncovered a role in l(3)mbt tumour growth and development. Interestingly, although both TrxT and Dhd were required for l(3)mbt tumour development, they appeared to have distinct roles in long-term tumour growth, as assessed by allograft-induced lethality. Furthermore, the authors also investigated the link between the sexually dimorphic signatures of l(3)mbt tumours and the thioredoxins and suggest that both genes are required for the differential gene expression observed between the sexes.

Some of the conclusions are fairly well supported by the data presented. However, there are some aspects that are potentially not fully explored and that would provide more weight to the claims made by the authors. Some of these can be addressed by clarifications made in the text and/or figures and others would benefit from additional immunofluorescence staining experiments.

Specific comments are provided below.

1. Figures should include information regarding the sex of the larvae, particularly as there has been a previously reported sex-linked effect in the phenotypes analysed. (e.g. in Figure 2 and Figure S1, where Indication of the sex of the animals should be provided in the figure and not just in the figure legend).

2. Data regarding fertility. Can this be shown in a table format? Are dhdKO females fully sterile? What are the fertility levels of Df(1)J5?

3. Are dhd and TrxT the only genes affected by Df(1)J5? Is there transcriptional data from Df(1)J5 animals to suggest that nearby genes are not affected by the deficiency? Of particular interest would be to assess if snf is affected or not as it is a known regulator of gene expression and splicing.

4. In Figure 1C, statistical test plus indication of significance is not presented.

5. Related to Figure 1D. Additional neural markers could be assessed in dhdKO and TrxTKO flies. Whilst the gross morphology of the brain does not seem to be affected, there is a possibility that cell specification is affected. Specific markers for the NE, MED and CB could be used to assess this in more detail, particularly as the DE-cad images shown for dhdKO and TrxTKO flies seem to differ slightly from the control.

6. Related to Figure 2A, images from TrxTKO; l(3)mbtts1, dhdKO and l(3)mbtts1 should be added at the very least in a supplementary figure. Additionally, data for NE/BL ratio should be provided for dhdKO, TrxTKO and Df(1)J5 in the absence of l(3)mbtts1 tumours. Related to Figure S1, quantification of NE/BL ratio for female lobes should be added to the figure.

7. Related to Figure 2B and Figure S1, three rows of images are presented for each genotype. It is unclear whether these correspond to brain lobes from different larvae or different confocal planes from the same animal. This should be clarified in the figure and/or figure legend. Related to this, in addition to the anti-DE-cadherin data, it would be informative to include immunofluorescence data using antibodies such as anti-Dachshund (lamina), anti-Elav (medulla cortex) and anti-Prospero (central brain and boundary between central brain and medulla cortex) (as assessed in e.g. Zhou and Luo, J Neurosci 2013) in the mbt tumour situation to accurately describe regions disrupted by the tumours.

8. Authors should clarify how the NE was defined when mbt tumours are generated, as it is severely affected. From the images provided, it is unclear which region corresponds to NE or how the NE/BL ratio was measured. It would be helpful to outline these regions in the images or, as mentioned above, use antibodies to define them.

9. Figure 2C does not have indication of statistical significance for the comparisons stated in the text. Potential explanations for the different roles of Dhd and TrxT in long-term tumour development should be explored in the discussion. Related to this, does the analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals reveal why they have similar effect on mbt tumour development but do not synergistically contribute to long-term growth?

10. Authors should clarify if there is any overlap between the affected M-tSDS and F-tSDS in the TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 conditions. Would the limited overlap suggest that TrxT and dhd act in parallel rather than synergistically? This might also explain the differential effects on long-term tumour development. Additionally, the stronger effect observed in Df(1)J5 animals may be due to TrxT and dhd functional redundancy. Currently, there is limited evidence to suggest that TrxT and dhd act synergistically to regulate mbt tumour growth based on the presented data.

11. Authors should include a Venn diagram depicting affected genes (M-tSDS and F-tSDS) in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1 and Df(1)J5; l(3)mbtts1 genotypes as this could clarify the percentage of overlap of gene signatures in these different conditions. Related to this point, authors could provide results from GO analysis to investigate whether specific functional clusters are altered in the different conditions.

12. In Figure 3E, authors should indicate more explicitly in the figure panel and/or figure legend which genes display significant differences in expression in the different samples.

13. In Figure S2C-F it is not clear if the graphs represent data from all tissues or data from male and female tissues separately, as shown in Figure 4.

14. Are TrxT and dhd also deregulated in other tumour types? Or is this specific for mbt tumours? This information could be provided to enhance the scope of the manuscript.

15. Authors conclude that TrxT and dhd cooperate in controlling gene expression between wild-type and tumour samples and that they act synergistically in the regulation of sex-linked gene expression in male tumour tissue. However, the link between the two observations (if indeed there is a link) has not been well explained. Is the effect on gene expression in tumours simply a result of the regulation of sex-linked transcription?

Significance

The current manuscript provides additional information regarding the regulation of mbt tumours and establishes TrxT and Dhd as potential cancer-germline genes in Drosophila. This will be of interest to researchers studying basic mechanisms of tumourigenesis and could potentially lead to identification of genes that could serve as biomarkers of disease. However, for this, a more general role of TrxT and Dhd needs to be established, as well as their potential conserved role as cancer-germline genes needs to be established.

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Referee #1

Evidence, reproducibility and clarity

Two cancer-germline (CG) genes encoding the Drosophila thioredoxins Deadhead (Dhd) and Thioredoxin-T (TrxT) are located head-to-head in the X chromosome. Cristina Molnar and coworkers investigate the effects of Dhd and TrxT in brain tumours of either sex caused by mutations in l(3)malignant brain tumour (l(3)mbt). Using CRISPR/Cas9-mediated knock-out alleles and RNA-seq, they demonstrate that, although both TrxT and Dhd are not required for normal brain development, they have a significant but partial effect on l(3)mbt brain tumour development, that is stronger in male than in female larval brains. However, allograft experiments show that only TrxT plays a significant role in long-term, sustained tumour growth. TrxT and dhd play a synergistic contribution role in development of mbt tumours and in the emergence of l(3)mbt tumour-linked transcriptomic signatures.

Major comments:

Most of the work in this paper is well conducted and the key conclusions are convincing. I think that the number of the replicates/animals for the experiments described in Figures 1 and 2 should be reported either in the figure legends or in the methods (statistical analysis). A relevant part of the discussion repeats what the authors have already said in the results. I would recommend to reorganize this section, emphasizing the importance of these results in the context of human brain tumors.

Significance

This work provides the first instance of an X-linked, head-to-head cancer-germline gene pair in Drosophila showing that these genes are dispensable for somatic cell development but have a crucial role to prevent malignant growth. Importantly, in humans, cancer germline genes and cancer testis (CT) genes have been involved in a wide range of cancers and about half of CT genes are located on the X chromosome. Thus, findings in this paper would be of interest to a broad audience that includes all the scientists studying the molecular mechanisms leading to cancer development.

The following keywords describe my expertise: Drosophila genetics, cell division, cancer genetics. I have less expertise to evaluate transcriptomics.

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Reply to the reviewers

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

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Referee #2

Evidence, reproducibility and clarity

Biddie et al. address the important question of what genomic annotations are relevant to the fine-mapping of trait-associated variation. They assessed data identifying DNase I hypersensitive sites, footprints, H3K27ac and other ChIP-seq peaks, ATAC-seq peaks, and eRNA locations using a benchmark set of allelically imbalanced DNase I hypersensitive sites and ChIP-seq peaks, and MPRA data. They find that a combination of DNase footprints and eRNA locations gives high enrichment for functional variants (albeit with low sensitivity) and demonstrate their FINDER on 53 traits from the GWAS catalog.

I have some questions to address before publication, all of which relate to clarifying the description in the manuscript.

1. I found this line in the abstract unclear: "This signature provides high precision, trading-off low recall".
2. Figure 1C is missing a y-axis label and a colour legend.
3. The authors note a high genomic coverage "by ATAC-seq (75.2%), [and] H3K27ac (61.5%)", which they attribute in part to "too low a threshold used in peak calling". However, both the benchmark datasets and the genomic predictors are utilized without consideration of the effect of thresholding. To what extent are DNase footprints and eRNA specifically informative, vs. representing datasets processed with highly selective cutoffs?
4. The benchmark datasets are described as molQTL, bWTL, and caQTL. "QTL" implies a regression of a trait (e.g. accessibility) on a genotype. This is not accurate here: the Vierstra and Abramov datasets investigate allelic imbalance (a related but orthogonal approach), while van Arensbergen is an MPRA.
5. QTLbase is cited alongside the Vierstra paper. I had some trouble searching in QTLbase but did not find the Vierstra dataset. It should be clarified whether QTLbase was used to download the Vierstra results, or to supplement it with other studies.
6. Fig. 4 discusses the effect of variant centrality in a DHS for prioritization, but it isn't included in the FINDER schematic in Fig. 7. How come it wasn't employed in FINDER?
7. The Discussion notes "Firstly, the identification of DNase footprints may be related to residency time of TFs on DNA, where rapidly exchanging factors impart poor footprints (Sung et al., 2014). Variants associated with altering binding of dynamic factors may therefore be missed. To overcome this, detection of footprints could be improved by enzymatic digestion bias correction". I don't see how enzymatic digestion bias is related to sensitivity to detect rapidly exchanging TFs.
8. It looks like the eRNA data were obtained from GRO-seq or PRO-seq data. It would be helpful to note key details like this directly rather than leaving it to the reader to try to figure out what is in the PINTS database.
9. The github link https://github.com/sbiddie/FINDER gives a 404 not found error. Is FINDER an actual tool implementation, or more generally describing the approach?

Minor comments:

1. Some of the figure text is quite small or blurry (e.g. Fig. 1A/B, Fig. S2).
2. Typo in Figure 1A legend: "Heatpmap".
3. The author of the last entry in the References is "Zhen Z" but should be "Zheng Z".

Significance

This work is highly relevant and well-done and provides practical information to guide future fine-mapping studies. The authors partially address the tradeoff between enrichment and recall, which is frequently swept under the rug. Their approach ought to be of high interest to the broad genetics and gene regulation communities.

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Referee #1

Evidence, reproducibility and clarity

Summary: Disease and trait associated genetic variation is primarily localizes to non-coding regulatory DNA. A wide-variety methods and assays are routinely used to delineate putative regulatory elements. In this manuscript Bidde et al. sought to evaluate which of these assays is useful for identifying and prioritize trait-associated regulatory variation. To these ends the authors perform enrichment analysis on a genetic variation from different sources encompassing both molecular phenotypes (QTLs) and trait-associated variation via GWA-studies. The authors show that genetic variants localizing to DNase I footprints and within elements associated with RNA production (enhancer RNA) are maximally enriched for both molQTLs and trait-associated variation vs. other markers of regulatory DNA. Overall, I find that this manuscript is technically sound, and is consistent with prior studies (namely the enrichment of GWAS variants within DNase I footprints -- Vierstra et al. 2020). I suggest only a few additional analyses and edits to the presentation.

Major comments:

1. The authors should expand the QTL studies and the GWAS variants via LD and recompute the enrichments. For example, I would take all variants in high LD (r2 > 0.8 or 0.9) with either a QTL or GWA-variant. This will likely increase total variants overlapping an annotation, but reduce overall enrichment (odds-score), and possibly provide some information about which chromatin marks are more associated with "causal" variants.
2. Can the authors comment on why eRNAs seem to be such a strong marker of functional variation? Are these just "strongest" (most accessible) distal elements? I would assume that these peaks have high overlap with chromatin accessibility peaks.
3. Would the ATAC-seq enrichment increase if the authors stratified regions by signal rather than aggregating all peaks? The vast majority of chromatin accessibility peaks are very weak and could be false-positives. Lets imagine that in each dataset 1% of peaks are FPs and that the FP peaks are mostly randomly distributed accross the genome. As such, aggregating hundreds to thousands of samples would have many FP peaks and greatly affect the enrichment analysis. Conversely, DNase I footprints are found in high signal peaks that are less likely to be false-positives. One approach to deal with this is to select ATAC-seq peaks matched to the peak signal in DHS peaks with footprints.

Minor comments:

1. Figure 1c -- no legend is provided specifying what the bar colors represent.
2. Pg. 10 -- "To overcome this, detection of footprints could be improved by enzymatic digestion bias correction (Calviello et al., 2019)." The DNase I footprinting dataset used in this paper performs extensive bias correction using a 6mer statistical model. Nevertheless, I completely agree the sentiment of the authors that low and variable sensitivity of footprinting is certainly driving a high false-negative rate with regards to comprehensively identifying function variants.
3. Figure 3 is a little too complicated for its purpose, which is to show the enrichment of bQTLS, caQTLs and raQTLs.

Significance

This manuscript provides a rigorous analysis characterize how various markers of chromatin help aid in the interpretation of non-coding genetic variation. The findings are not entirely novel, however, the analyses and approaches described are nevertheless useful for variant prioritization. This manuscript is broadly applicable and useful to anyone interested studying non-coding genetic variation.

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Reply to the reviewers

Reviewer #1

The paper by Yammine et al addresses a major problem in peculiarities of genotype to phenotype manifestation in collagen II and chondrodysplasia. It is a lucid and comprehensive study detailing what they see as the fundamental mechanism of Gly1170 Ser mutated Col2a1 gene.

At the heart of the matter is the debunking of the results from a mouse model generated by liang et al (Plos one 2014) paper in which the authors suggested that the phenotype seen only homozygous mice (heterozygous mice appear normal), was related to ER stress -UPR-apoptosis cascade resulting in the chondrodysplasia. Yammine et al paper uses a different model, a robust human iPSC-based tissue, with a CRISPRed variant show that despite the ability of the variant chondrocytes to deposit a Gly1170Ser-substituted collagen II in both the hetero- and homozygous models, is not accompanied by any substantive UPR. The authors of this current paper also argue that their model system is most closely resemble the human context, where heterozygous individual show pathology.

We appreciate the Reviewer highlighting the significance of this manuscript addressing a major issue in the field.

I have sieved all the data related to this topic and have gone back to examine the data and what struck me was the repeated use of the phrase "slow to fold" in the current paper and wondered whether the element of "TIME" is as important in the chondrogenesis of either models and it is this element that generate the difference between the two results? While iPSC-based tissue takes up to 44 days, a female mouse would have had two litters in this time and made many more growth plates. Could it be by "slowing" the chondrogenesis pathway, which is part of the procedure of differentiation of iPS cells into chondrocytes, the ER is not as "stressed" as in mouse development? I would like the authors to reflect and comment and put forward their view given UPR signaling pathways play a crucial role in chondrocytes in phases of high protein synthesis, e.g., during bone development by endochondral ossification (Journal of Bone Metabolism, vol. 24, no. 2, pp. 75-82, 2017).

The Reviewer here emphasizes a likely benefit of the human model that we had not previously considered, as differentiation and growth in our model are indeed far more similar to humans than the rapid timeline in mice. We also note that the evidence that collagen is slow to fold comes from the gold standard assay in the field for collagen folding rate, a point discussed in greater detail in response to Reviewer 2’s query (see below).

The literature evidence does indicate that transient UPR signaling is relevant for chondrogenesis. We selected UPR timepoints that do not interface with the differentiation process, but rather the tissue deposition process while chondrocytes are still actively depositing and maintaining the extracellular matrix, to be able to distinguish a physiological transient UPR during differentiation from a potential chronic and possibly pathologic one. We now clarify this point in the manuscript (see text below).

“These timepoints were selected to reflect an early and a late stage of cartilage maturation, but with both timepoints harvested post-chondrogenesis so as not to interfere with the physiologic transient UPR activation that can be important in that process.”

This is not withstanding the good argument given by the authors in defending their robust results, namely that the there is no evidence that the hydrophilic triple-helical domain of pro-collagen binds BiP, the main detector of accumulated misfolded proteins. What then do they make out of the immunostaining and qPCR with ER stress related genes in Liang et al paper?? I know that the data is not theirs but a comment on the indisputable data gives the reader a better understanding.

It is critical to note that the evidence for ER stress that induces the UPR is, at best, exceptionally weak for heterozygotes in the Liang et al paper, and arguably also weak for homozygotes. Liang et al observed, via quantitative PCR, that the mRNA levels of just Chop (which is also a marker of the integrated stress response and not a good readout for UPR activity) and ATF6 (whose RNA-level upregulation is not a standard marker of the UPR) were significantly upregulated in the disease-relevant heterozygous mice – given that other (more valid) UPR markers were not altered, this is not so different from our observation of a lack of UPR in the disease-relevant heterozygotes.

A somewhat more comprehensive set of UPR markers, including Chop, Xbp1(Total and Spliced), Grp78 (BiP), ATF4, and ATF6, was significantly upregulated only in homozygous mice compared to wild-type. PERK is one of many kinases upstream of ATF4 and Chop that can be activated by a variety of processes (the pathway is part of the integrated stress response, for example). Moreover, transcriptional upregulation of ATF4 (which is actually induced translationally, not transcriptionally) and ATF6 (which is actually induced proteolytically, not transcriptionally) are not normally used to read out UPR activation, so it is not so clear to us that a robust UPR was induced even in homozygotes. Moreover, there was not a substantial increase in Xbp1-S (S = spliced) relative to Xbp1-T (T= total) in the study of homozygous mice, which is the most appropriate measure of UPR activation – rather than change in Xbp1-T and Xbp1-S. The use of mostly non-standard genes to assess UPR induction, the weak upregulation of BiP (2.5-fold), and the unchanged ratio of Xbp1-S to Xbp1-T raise some questions regarding UPR induction even in the homozygotes. Regardless of these homozygote data, as noted above, the evidence for a UPR in heterozygotes is very weak, despite ER stress being the focus of the Liang et al paper.

With respect to immunostaining, Liang et al observed that tissue from homozygous mice (but not heterozygotes) contained significantly more apoptotic cells. Apoptosis could be a result of chronic, unresolved UPR signaling, but it could also result from any number of other pathways and is certainly not direct evidence for UPR-inducing ER stress. Additionally, for the homozygote apoptosis assay, Liang et al do not note how many mice were analyzed for each genotype, a value they did report for their other assays. While examining multiple sections for each genotype is valuable (they state ≥10), the assessment of biological replicates (additional mice) seems critical to confidently reach a conclusion.

Although I understand the choice of cell lines for overexpression, the transfection of the HT-1080 cells using wild-type and Gly1170Ser COL2A1encoding plasmids are not a match to the in vivo model (variation of efficiency, etc.) the appearance of BiP even at a lower fold increase does not negate ER stress, as the authors acknowledge but more important is what other paracrine signals which triggers the UPR signally pathway which is not linked to BiP? or an iPS system may lack? Is there anything else not only ATF6α (activating transcription factor 6 alpha), but IRE1α (inositol-requiring enzyme 1 alpha), and PERK (protein kinase RNA-like endoplasmic reticulum kinase).

Our finding that the UPR is not activated is based on comprehensive RNA-sequencing performed in the physiologically more relevant iPSC-derived chondrocyte, as opposed to the tumor cell line HT-1080. Our interactomic finding that BiP interacts to the same extent with wild-type and Gly1170Ser procollagen-II (in HT-1080 cells) strongly supports our proposal that the reason the UPR is not activated is that BiP fails to recognize unfolded triple-helical domains.

We note that, although HT-1080 cells are not a perfect match, they are the most accessible option for interactome-based studies. Because there is no MS-grade antibody for collagen-II IP, we need to IP a transfected, tagged collagen. We cannot do this in chondronoids, or in isolated chondrocytes that transfect poorly and rapidly dedifferentiate. Critically, Prockop and co-workers extensively validated HT-1080 cells as a platform for fibrillar collagen biochemical studies in Matrix 1993, 13, 399. Our own lab further characterized their capacity to properly handle fibrillar collagen variants in great molecular detail in ACS Chem Biol 2016, 11__, __1408.

Since our chondronoid system contains only chondrocyte cells, as is the case in cartilage, the cells can receive paracrine signals from other chondrocytes, but not other cell types. In joints within a whole animal, it is true that paracrine crosstalk occurs between different cell types of different tissues, including inflammatory cells for example. The chondronoid is very useful for elucidating the defects that occur at the chondrocyte-level, without confounding secondary effects. At the chondrocyte-level, Gly1170Ser-substituted procollagen-II does not activate the UPR.

The Reviewer’s comment regarding the absence of paracrine signals in an iPSC-based system is well-taken, and we added discussion as follows:

“These observations indicate that the chondrocytes were not raising such stress responses, at least when examined in the absence of paracrine signals from other cell types in the joint.”

The authors have given us plenty of alternatives that are relevant, and they prepared us for yet another paper on articular cartilage using iPS tissue model which I am looking forward to.

We are also excited about the upcoming potential of this model system!

Significance

I think this paper is publishable and it is important in understanding the mechanism by which mutation in collagen type II affect chondrogenesis and therefore bone formation. This paper will appeal to musculoskeletal scientist especially those who are interested in bone and its pathology. It would be important for the authors to respond to the critique of "TIME" and speed of protein synthesis which create a duress in the ER pathway.

We greatly appreciate the Reviewer’s comment again on the significance of this work, and their scholarly input which has substantially improved the paper. We hope they will agree that the manuscript is now ready for publication.

Reviewer #2

Evidence, reproducibility and clarity

*System: The investigators have used a human iPSC chondrocyte model system to investigate the biochemistry of the Chondrodysplasia caused by the p.Gly1170Ser mutation in the type II collagen gene (COL2A1). They studied presumably homogeneous chondronoids formed by 3 cell lines they previously reported in which the chondrocytes were either homozygous wild type for the gene, homozygous for the Cas Crispr induced mutation or heterozygous for the two alleles (their refs 42-45). In addition, they utilized cultured HT1080 human fibrosarcoma cells transfected with wild type and mutant Col2A1 to study differences in the interactomes of the two proteins.

*

*Analytic Parameters: They investigated the extracellular matrix formed by the three cells using collagen and proteoglycan staining and TEM and the transcriptional responses in chondronoids expressing the wild type and mutant genes.

*

*Observations: matrix formation was defective in the two mutation bearing cell populations, reflecting defective fibril formation proportional to the abnormal gene dose. They found increased accumulations of post-translational modifications (hydroxylation, and O-glycosylation) on the mutant collagen extracted from the chondronoids and EM evidence of collagen retention in the ER. They studied the comparative transcriptional profiles in the three phenotypes and failed to find a profound UPR response late in culture and only a mild upregulation of UPR genes in the young cultures. They could not find evidence for activation of the ISR except in the homozygous mutant cells.

*

*Using transfected HT-1080 cells (previously shown by these investigators not to express endogenous pro-collagen II but able to synthesize transfected pro-collagen genes) they were able to study the comparative wt and mutant pro-collagen interactomes.

*

Conclusions: They conclude that the p.gly1170ser mutation in Col2A1 results in abnormal folding which results in trapping of the protein in the ER and some interaction with cellular elements of the proteostatic response. They concluded that the cellular proteostasis machinery can recognize slow-folding Gly1170Ser through increased interactions with certain ER network components but not in the same fashion that has been described for liver cells producing mutated versions of high volume secreted proteins.

We appreciate this careful summary of our work.

*Major comments:

*

Their first conclusion, stated in the abstract, "Biochemical characterization reveals that Gly1170Ser procollagen-II is notably slow to fold and secrete." that the mutant polypeptide chain is slower folding than the wild type chain is based on the premise that the longer the chains are in the ER the greater the degree of lysine hydroxylation and O-glycosylation. Although this may be true, they do not provide a reference and I could not find a definitive description of the phenomenon. Their reference 48 only discusses the occurrence of intracellular post-translational modification of the lysines and continuing modification extracellularly but does not relate these phenomena to the rate at which the peptides traverse the cell. I think the reader would benefit from seeing experiments in which the rate of folding and secretion of the wild type and mutant chains are measured and the degree of post-translational modification are compared. Cabral WA et al showed differences in collagen folding and secretion rates in cyclophilin wt, knockouts and heterozygotes osteoblasts and fibroblasts by western blots. (2014) Abnormal Type I Collagen Post-translational Modification and Crosslinking in a Cyclophilin B KO Mouse Model of Recessive Osteogenesis Imperfecta. PLoS Genet 10(6): e1004465. doi:10.1371 / journal.pgen. 1004465). Performing such experiments in their chondronoids would confirm the authors' interpretation that the increased post-translational modification portrayed in their figure 4 reflects slowed folding and secretion related to the mutation.

We apologize for failing to provide essential background references and information to assess our assay for slow folding/secretion of procollagen. In fact, slow migration on SDS-PAGE is not only a widely used assay for comparing the rate of folding of procollagens, it has also remained the gold standard in the field for the past forty years. The studies cited below are some of the seminal papers in the field linking collagen’s rate of folding with its extent of posttranslational modifications and its electrophoretic mobility. We have now updated our citations accordingly.

1. Bateman, J.F.; Mascara, T.; Chan, D.; Cole, W.G. “Abnormal type I collagen metabolism by cultured fibroblasts in lethal perinatal osteogenesis imperfecta” Biochem J 1984, 217, 103.
2. Bonadio, J.; Holbrook, K.A.; Gelinas, R.E.; Jacob, J.; Byers, P.H. “Altered triple helical structure of type I procollagen in lethal perinatal osteogenesis imperfecta” J Biol Chem 1985, 260, 1734.
3. Bateman, J.F.; Chan, D.; Mascara, T.; Rogers, J.G.; Cole, W.G. “Collagen defects in lethal perinatal osteogenesis imperfecta” Biochem J 1986, 240, 699.
4. Godfrey, M.; Hollister, D.W. “Type II achondrogenesis-hypochondrogenesis: Identification of abnormal type II collagen” Am J Hum Genet 1988, 43, 904. The basis for this collagen-specific assay of folding rate is that the ER-localized procollagen proline and lysine hydroxylases require monomeric collagen strands as substrates, and cannot accommodate a folded triple helix in their active sites. Thus, accumulation of post-translational modifications on collagen depends on the procollagen triple-helical domain’s residence time as an unfolded monomeric region of the assembling triple-helical trimer within the ER. Some fraction of the hydroxylated lysines are later glycosylated, which slows migration on SDS-PAGE gels. We have now clarified our slow folding conclusion with more precise references and discussion in the manuscript.

Pulse-chase experiments like those suggested by the Reviewer would indeed be beneficial if they were possible in this system, but they simply are not. Although it might be possible to soak in a radiolabeled amino acid over a short time period, the assay still relies on separating the cell fraction from the secreted fraction. This is possible in monolayer cultures, but in a chondronoid composed of complex cartilage and cells we have no way to do it. One could propose that we extract the chondrocytes and then do the pulse-chase in a monolayer culture, but this unfortunately is also not possible as chondrocytes do not behave well outside the tissue setting and rapidly differentiate into other cell types. Fortunately, the procollagen overmodification assay is a widely used and well-accepted measure of slow folding, and thus addresses the issue.

I think Figure 4 needs more explanation for the reader. While, as expected, the homozygous mutant band is much slower than the homozygous wild type band, in the heterozygotes the band is intermediate rather than showing a discrete mixture of wild type and mutant proteins, reflecting different degrees of post-translational modification. Is this a function of mixed triple helices with heterogeneous degrees of post-translational modification? It deserves more comment, since the argument relating the degree of post-translational modification to the rate of folding is dependent on this observation. It would also be helpful to show the whole gel with collagen II markers.

We modified Figure 4 __to show the whole gel (in the SI, see __Fig. S3) and molecular weight markers. It also shows the wild-type collagen-II band. Most of the procollagen produced by the heterozygote is heterotrimeric for the disease-causing substitution (>87% of trimers will contain at least one mutant chain and thus experience delayed folding) and, therefore, the diffuse banding structure is to be expected. Further, we would speculate that in these challenged ER, even the folding of wild-type only trimers is impaired. The Reviewer’s comment suggests there may be some basis for that speculation. We added a note to this effect.

“The presence of a single broad, slow-migrating band as opposed to distinctive overmodified mutant versus normally modified wild-type strands is due to fact that the vast majority of trimers formed in heterozygotes (>85%) contain at least one Gly1170Ser strand that delays triple-helix folding.”

Another approach to the question of intracellular accumulation due to a slow rate of folding of the mutant collagen would be to perform pulse chase labeling of the three types of chondronoids with radiolabeled amino acids and sugars and processing the media and lysates with analysis using antibodies specific for the two collagen chain types. Given the authors extensive experience in studying collagen biosynthesis (e.g. Chan et al J. Biochem. Biophys. Methods 36 (1997) 11-29), such a supporting study would firmly establish whether the rate of folding/secretion differs between the wt and the homozygous and heterozygous chondroidinomas. Until the slow folding can be directly demonstrated in a quantitative fashion rather than by monitoring the secondary phenomenon of post-translational modification the hypothesis remains unproven.

Discussed above in response to the Reviewer’s earlier suggestion of pulse-chase and question regarding the post-translational modification assay, unfortunately the pulse-chase experiment is infeasible. Fortunately, the modification-based assay is already the gold standard in the collagen field.

Another issue that does not appear to be addressed is the consequence of having misfolded collagen chains in the dilated ER. Liang et al, using mice transgenic for one or two copies of the mutant human gene showed apoptosis in the homozygotes but not in the hets a finding similar to that of Kimura et al using transgenics carrying a different human COL2A1 mutation. Okada et al, using chondrocytes converted from human fibroblasts with clinical collagenopathy (heterozygous), although not the same mutation as in the present study, showed dilated ER and some level of apoptosis in the cultured cells. Hintze et al, examining chondrocytes expressing different mutants associated with different forms of spondyloepiphyseal dysplasia, suggested that the degree of stability of the mutations might determine whether apoptosis occurred, i.e. the thermolabile p.R989C was associated with apoptosis while cells expressing the more thermostable mutants p.275C, P.719C and p.G853E did not reveal any evidence for ongoing apoptosis R989. Is it possible that the smaller size of the homozygous chondronoids reflect fewer cells rather than less matrix (or both) as result of apoptosis? Examination of the chondronoids with reagents for caspase 3 or Tunel staining. One could also measure by Col/DNA ratio in wt, hets and homos. It might also have been useful for these experiments been more quantitative, i.e. by cell sorting rather than by eye. Would ImageJ software been helpful?

We greatly appreciate this suggestion. We now added results of TUNEL assays performed on sections of the chondronoids (see Fig. 8), including quantification of the results. Notably, we do not observe a significant difference in apoptosis between genotypes at the timepoint considered. This result is also supported by our transcriptional data, where we do not observe upregulation of apoptosis-related pathways, via the UPR or otherwise.

It is also unclear as to the conformation of chains trapped in the ER. There are many examples in which the natural tendency of misfolded proteins is to aggregate. This is certainly true in the neurodegenerative diseases. While at the magnification used here in the TEM's the ER inclusions appear homogeneous and amorphous, perhaps at higher magnification/resolution a more discrete structure might be seen.

From collagen-II immunohistochemistry confocal images, the intracellular collagen appears sometimes as aggregated puncta, and in other cases more diffuse and amorphous. Given this heterogeneity, we were not able to readily obtain clear additional structural characterization of the intracellular procollagen-II fraction.

*While the choice of time points for the transcriptional analysis, i.e. early and late seems well thought out, the lack of a significant response may be due to the timing and it might have been useful to do earlier or later time points or intermediate time points in case the response was transient, particularly since other laboratories have reported UPR activation and abnormalities in the context of the silencing of Xbp1, the spliced form of which is a major driver of at least one arm of the UPR. *

While our RNA-sequencing results at the specific timepoints we chose cannot rule out a transient activation of the UPR, they do indicate that chronic, unresolved UPR signaling is not the underlying cause of pathology, which is the main point we are making.

The notion that pro-collagen is largely hydrophilic without the potential for exposure of hydrophobic regions that might engage BiP, thus is not sensitive to BiP sensing, is interesting. Is it possible that the tendency of the mutant polypeptides to form the triple helix which in itself acts as kind of a self chaperoning structure? Looking at the kinetics of assembly inside the cell, see suggestions above, might provide further insight into the process beyond that obtained by looking at the modified state of the lysines.

We believe this notion is very strongly supported by the interactomic experiment showing that BiP fails to preferentially engage the poorly folding triple-helical variant. There are, however, many other chaperones and folding enzymes that assist collagen folding, including prolyl isomerases and Hsp47. Hence, it is not clear to us that substantial self-chaperoning occurs. Still, the self-chaperoning idea is intriguing, and we will note that prior work does indicate that triple-helical domains of individual procollagen polypeptides are strongly pre-organized for triple-helix formation (for a review, see Annu Rev Biochem 2009, 78, 929). That said, we hesitate to speculate here on the self-chaperoning idea without additional evidence.__

__Minor comments:

As I mentioned above, while the transcriptional interactome experiments are computationally sophisticated the cell biology and biochemistry would benefit from more and better quantitation.

We have included quantitation of the extent of intracellular procollagen accumulation and the extent of apoptotic cells, which we hope helps to address this point.

The paper is written in a style in which results and discussion are intermingled. Personally I prefer that the introductions are short, the results clearly and briefly presented and the discussion deals with the interpretation and conclusions. I thought that whole paragraphs could have been omitted. e.g. in the introduction *Omit paragraph "The fibrillar.........achondrogenesis type II" Omit paragraph "Conventional and... for example." Omit "Excitingly........in vitro and in vivo (36)." Results: First paragraph repeats last paragraph of introduction and not necessary in one place or the other, condense. *

We appreciate this feedback and have accordingly edited the manuscript for clarity and brevity, which includes deleting or significantly shortening all the paragraphs indicated by the Reviewer. These improvements are indicated in the track-changes version of the manuscript we resubmitted.

Figure 2 by eye MGP (Matrix gla protein inhibits vascular calcification of type II collagen) seems highly over-expressed in the homozygous mutants; MGP is supposedly an inhibitor of calcification, does its over-expression here reflect something about the adequacy of the matrix

Overexpression of MGP could indeed reflect a defect in the matrix of the homozygous variants. It is also likely a reflection of the delayed hypertrophy and maturation observed in the homozygous variants, as matrix calcification is a step in the endochondral ossification process. We did not follow-up on this particular observation, as it is exclusively observed in the less clinically relevant homozygous variant. We added a note to the manuscript to capture the Reviewer’s point about MGP, as below:

“The upregulation in the homozygous system of Matrix Gla Protein (MGP) (Fig. 2A), which inhibits vascular calcification of the matrix in vivo, further supports the delay in hypertrophy, and could lead to differences in the biomechanical properties of the matrix.”

Figure 5 is good but can it be confirmed by quantitative biochemistry?

We have included quantitation of the extent of intracellular procollagen accumulation and the extent of apoptotic cells.

__ __Did you stain with antibodies to other ER resident chaperones other than calreticulin?

Yes, we also stained the ER with PDI. However, the chondronoids require extensive optimization for immunostaining and we could obtain much better images using the ER marker for calreticulin, hence our choice of images to present in the manuscript.__

__Do cells with large amounts of intracellular G1170S die?

As indicated by the newly included TUNEL data, interestingly, even cells expressing exclusively the Gly1170Ser variant of procollagen-II do not seem to apoptose at a significantly higher rate than wild-type, at least at the timepoint considered. As mentioned above, we added these data as Fig. 8, and added discussion of these results and methodology in the relevant sections of the manuscript.__

__Does higher magnification EM reveal any structure of the material within the dilated ER?

We have so far not been able to use EM to obtain higher-resolution insight into intracellular procollagen structures, but we will work on this idea in future studies.__

__Are there any inflammatory cells in the Chondronoids? To respond to aberrant proteins?

There should not be any such cells present in the chondronoids, and we indeed do not observe any inflammatory response. As noted in the response to Reviewer 1, we added discussion regarding the absence of paracrine signals in this type of model system, which we do believe has major advantages for biochemical studies like those performed here.__

__Paragraph

* "Bypassing the UPR.......often do not" Is discussion not results*

Corrected, thanks.

Significance

The experimental system described here is clearly the wave of the present. Generating human ipSC's of different lineages is now being exploited to study a variety of disorders, to achieve better understanding of pathogenesis at the molecular level to serve as appropriate models for drug development, particularly in the context of high throughput screening. In addition, as in this case, relatively rare autosomal dominant disorders with phenotypes that resemble more common sporadic disease, may allow the development of treatments that are relevant for the sporadic disorder. While it is likely that the osteoarthritis that develops in the carriers of the COL2A1 mutations is a function of the host response to the aberrant mechanics resulting from the defective extra-cellular matrix caused by the mutation, having a pure system in which the primary defect can be corrected and the predisposing matrix deficit reversed, could allow normal reparative processes to mitigate the functional joint disability. While the transgenic mice are useful as a disease model, they represent not only the expression of the primary defect but the host pathophysiologic response to that defect, i.e. in this case how the mouse responds to the defective matrix state and whether those responses add additional pathogenic factors to the disease course. Having a tool in which to relatively assess the pure chondrocyte effect should allow more granular analysis of the primary process.

We appreciate the Reviewer’s careful and enthusiastic assessment of the significance of our work.__

__

Their findings reinforce the notion that involvement of the UPR as well as the other arms of the proteostatic response in chondrocytes expressing a variety of mutant collagens suggests a degree of heterogeneity, perhaps depending on the mutation involved. While I do not believe that their current data prove or rigorously test their proposed hypothesis, i.e. that "perhaps due to the pathologic substitution occurring within a triple-helical domain that lacks hydrophobic character, this ER protein accumulation is not recognized by cellular stress responses, such as the unfolded protein response", it is worth considering.

We provide that hypothesis as a reasonable explanation for the absence of a UPR, and it is strongly supported by our interactomic studies. Furthermore, neither we nor others have found evidence for BiP binding the triple helical domain of procollagen in any other studies. Still, that hypothesis is not the core point of the paper and we do appreciate the Reviewer’s perspective.

Given the fact that this is a relatively small field with a variety of observations concerning the role of proteostasis and the UPR in particular which seem to vary depending on the system, i.e. transgenic mice, transfected fibroblasts, the chondroidomas, these observations particularly with additional biochemistry to confirm their notions regarding folding rates etc, represent a useful technical addition to the field and should be interesting for people working on collagen biology, arthritis and protein folding.

I am not a collagen biologist hence my knowledge of some of the nuances of collagen biology may not be extensive. My own areas of interest include the assembly of multi-peptide proteins (such as immunoglobulins) for secretion; the mechanisms that allow them to exit the cell and the aggregation of misfolded proteins as exemplified by the amyloidoses and other forms of clinically relevant protein aggregation. Hence, I am very familiar with tissue culture, transgenic animals as disease models, studies of protein aggregation, and as a former rheumatologist, osteoarthritis.

We greatly appreciate the Reviewer providing such valuable and scholarly input from the perspective of a scientist with deep expertise in the secretory pathway and other diseases of protein misfolding, as well as from rheumatology. Specifically from the perspective of expertise in collagen biology/biochemistry, we hope that our detailed explanations of assays that are possible versus not possible with collagen in this system, the additional context for why our assessment of the modification of procollagen is correlated with folding/secretion rate, and the further analyses added to the paper, now make a convincing case that the improved manuscript is of high significance and is ready for publication.

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Referee #2

Evidence, reproducibility and clarity

System: The investigators have used a human iPSC chondrocyte model system to investigate the biochemistry of the Chondrodysplasia caused by the p.Gly1170Ser mutation in the type II collagen gene (COL2A1). They studied presumably homogeneous chondronoids formed by 3 cell lines they previously reported in which the chondrocytes were either homozygous wild type for the gene, homozygous for the Cas Crispr induced mutation or heterozygous for the two alleles (their refs 42-45). In addition, they utilized cultured HT1080 human fibrosarcoma cells transfected with wild type and mutant Col2A1 to study differences in the interactomes of the two proteins.

Analytic Parameters: They investigated the extracellular matrix formed by the three cells using collagen and proteoglycan staining and TEM and the transcriptional responses in chondronoids expressing the wild type and mutant genes.

Observations: matrix formation was defective in the two mutation bearing cell populations, reflecting defective fibril formation proportional to the abnormal gene dose. They found increased accumulations of post-translational modifications (hydroxylation, and O-glycosylation) on the mutant collagen extracted from the chondronoids and EM evidence of collagen retention in the ER. They studied the comparative transcriptional profiles in the three phenotypes and failed to find a profound UPR response late in culture and only a mild upregulation of UPR genes in the young cultures. They could not find evidence for activation of the ISR except in the homozygous mutant cells. Using transfected HT-1080 cells (previously shown by these investigators not to express endogenous pro-collagen II but able to synthesize transfected pro-collagen genes) they were able to study the comparative wt and mutant pro-collagen interactomes.

Conclusions: They conclude that the p.gly1170ser mutation in Col2A1 results in abnormal folding which results in trapping of the protein in the ER and some interaction with cellular elements of the proteostatic response. They concluded that the cellular proteostasis machinery can recognize slow-folding Gly1170Ser through increased interactions with certain ER network components but not in the same fashion that has been described for liver cells producing mutated versions of high volume secreted proteins.

Major comments:

Their first conclusion, stated in the abstract, "Biochemical characterization reveals that Gly1170Ser procollagen-II is notably slow to fold and secrete." that the mutant polypeptide chain is slower folding than the wild type chain is based on the premise that the longer the chains are in the ER the greater the degree of lysine hydroxylation and O-glycosylation. Although this may be true, they do not provide a reference and I could not find a definitive description of the phenomenon. Their reference 48 only discusses the occurrence of intracellular post-translational modification of the lysines and continuing modification extracellularly but does not relate these phenomena to the rate at which the peptides traverse the cell. I think the reader would benefit from seeing experiments in which the rate of folding and secretion of the wild type and mutant chains are measured and the degree of post-translational modification are compared. Cabral WA et al showed differences in collagen folding and secretion rates in cyclophilin wt, knockouts and heterozygotes osteoblasts and fibroblasts by western blots. (2014) Abnormal Type I Collagen Post-translational Modification and Crosslinking in a Cyclophilin B KO Mouse Model of Recessive Osteogenesis Imperfecta. PLoS Genet 10(6): e1004465. doi:10.1371 / journal.pgen. 1004465). Performing such experiments in their chondronoids would confirm the authors' interpretation that the increased post-translational modification portrayed in their figure 4 reflects slowed folding and secretion related to the mutation.

I think Figure 4 needs more explanation for the reader. While, as expected, the homozygous mutant band is much slower than the homozygous wild type band, in the heterozygotes the band is intermediate rather than showing a discrete mixture of wild type and mutant proteins, reflecting different degrees of post-translational modification. Is this a function of mixed triple helices with heterogeneous degrees of post-translational modification? It deserves more comment, since the argument relating the degree of post-translational modification to the rate of folding is dependent on this observation. It would also be helpful to show the whole gel with collagen II markers.

Another approach to the question of intracellular accumulation due to a slow rate of folding of the mutant collagen would be to perform pulse chase labeling of the three types of chondronoids with radiolabeled amino acids and sugars and processing the media and lysates with analysis using antibodies specific for the two collagen chain types. Given the authors extensive experience in studying collagen biosynthesis (e.g. Chan et al J. Biochem. Biophys. Methods 36 (1997) 11-29), such a supporting study would firmly establish whether the rate of folding/secretion differs between the wt and the homozygous and heterozygous chondroidinomas. Until the slow folding can be directly demonstrated in a quantitative fashion rather than by monitoring the secondary phenomenon of post-translational modification the hypothesis remains unproven.

Another issue that does not appear to be addressed is the consequence of having misfolded collagen chains in the dilated ER. Liang et al, using mice transgenic for one or two copies of the mutant human gene showed apoptosis in the homozygotes but not in the hets a finding similar to that of Kimura et al using transgenics carrying a different human COL2A1 mutation. Okada et al, using chondrocytes converted from human fibroblasts with clinical collagenopathy (heterozygous), although not the same mutation as in the present study, showed dilated ER and some level of apoptosis in the cultured cells. Hintze et al, examining chondrocytes expressing different mutants associated with different forms of spondyloepiphyseal dysplasia, suggested that the degree of stability of the mutations might determine whether apoptosis occurred, i.e. the thermolabile p.R989C was associated with apoptosis while cells expressing the more thermostable mutants p.275C, P.719C and p.G853E did not reveal any evidence for ongoing apoptosis R989. Is it possible that the smaller size of the homozygous chondronoids reflect fewer cells rather than less matrix (or both) as result of apoptosis? Examination of the chondronoids with reagents for caspase 3 or Tunel staining. One could also measure by Col/DNA ratio in wt, hets and homos. It might also have been useful for these experiments been more quantitative, i.e. by cell sorting rather than by eye. Would ImageJ software been helpful? It is also unclear as to the conformation of chains trapped in the ER. There are many examples in which the natural tendency of misfolded proteins is to aggregate. This is certainly true in the neurodegenerative diseases. While at the magnification used here in the TEM's the ER inclusions appear homogeneous and amorphous, perhaps at higher magnification/resolution a more discrete structure might be seen.

While the choice of time points for the transcriptional analysis, i.e. early and late seems well thought out, the lack of a significant response may be due to the timing and it might have been useful to do earlier or later time points or intermediate time points in case the response was transient, particularly since other laboratories have reported UPR activation and abnormalities in the context of the silencing of Xbp1, the spliced form of which is a major driver of at least one arm of the UPR. The notion that pro-collagen is largely hydrophilic without the potential for exposure of hydrophobic regions that might engage BiP, thus is not sensitive to BiP sensing, is interesting. Is it possible that the tendency of the mutant polypeptides to form the triple helix which in itself acts as kind of a self chaperoning structure? Looking at the kinetics of assembly inside the cell, see suggestions above, might provide further insight into the process beyond that obtained by looking at the modified state of the lysines.

Minor comments:

As I mentioned above, while the transcriptional interactome experiments are computationally sophisticated the cell biology and biochemistry would benefit from more and better quantitation.

The paper is written in a style in which results and discussion are intermingled. Personally I prefer that the introductions are short, the results clearly and briefly presented and the discussion deals with the interpretation and conclusions. I thought that whole paragraphs could have been omitted. e.g. in the introduction

Omit paragraph "The fibrillar.........achondrogenesis type II" Omit paragraph "Conventional and... for example." Omit "Excitingly........in vitro and in vivo (36)."

Results:

First paragraph repeats last paragraph of introduction and not necessary in one place or the other, condense. Figure 2 by eye MGP (Matrix gla protein inhibits vascular calcification of type II collagen) seems highly over-expressed in the homozygous mutants; MGP is supposedly an inhibitor of calcification, does its over-expression here reflect something about the adequacy of the matrix

Figure 5 is good but can it be confirmed by quantitative biochemistry?

Did you stain with antibodies to other ER resident chaperones other than calreticulin?

Do cells with large amounts of intracellular G1170S die?

Does higher magnification EM reveal any structure of the material within the dilated ER?

Are there any inflammatory cells in the Chondronoids? To respond to aberrant proteins?

Paragraph "Bypassing the UPR.......often do not" Is discussion not results

Referees cross-commenting

Are other reviewers concerned about the precise definition of slowed folding rather than utilizing the degree of post-translational modification as a surrogate?

Significance

The experimental system described here is clearly the wave of the present. Generating human ipSC's of different lineages is now being exploited to study a variety of disorders, to achieve better understanding of pathogenesis at the molecular level to serve as appropriate models for drug development, particularly in the context of high throughput screening. In addition, as in this case, relatively rare autosomal dominant disorders with phenotypes that resemble more common sporadic disease, may allow the development of treatments that are relevant for the sporadic disorder. While it is likely that the osteoarthritis that develops in the carriers of the COL2A1 mutations is a function of the host response to the aberrant mechanics resulting from the defective extra-cellular matrix caused by the mutation, having a pure system in which the primary defect can be corrected and the predisposing matrix deficit reversed, could allow normal reparative processes to mitigate the functional joint disability. While the transgenic mice are useful as a disease model, they represent not only the expression of the primary defect but the host pathophysiologic response to that defect, i.e. in this case how the mouse responds to the defective matrix state and whether those responses add additional pathogenic factors to the disease course. Having a tool in which to relatively assess the pure chondrocyte effect should allow more granular analysis of the primary process.

Their findings reinforce the notion that involvement of the UPR as well as the other arms of the proteostatic response in chondrocytes expressing a variety of mutant collagens suggests a degree of heterogeneity, perhaps depending on the mutation involved. While I do not believe that their current data prove or rigorously test their proposed hypothesis, i.e. that "perhaps due to the pathologic substitution occurring within a triple-helical domain that lacks hydrophobic character, this ER protein accumulation is not recognized by cellular stress responses, such as the unfolded protein response", it is worth considering.

Given the fact that this is a relatively small field with a variety of observations concerning the role of proteostasis and the UPR in particular which seem to vary depending on the system, i.e. transgenic mice, transfected fibroblasts, the chondroidomas, these observations particularly with additional biochemistry to confirm their notions regarding folding rates etc, represent a useful technical addition to the field and should be interesting for people working on collagen biology, arthritis and protein folding.

I am not a collagen biologist hence my knowledge of some of the nuances of collagen biology may not be extensive. My own areas of interest include the assembly of multi-peptide proteins (such as immunoglobulins) for secretion; the mechanisms that allow them to exit the cell and the aggregation of misfolded proteins as exemplified by the amyloidoses and other forms of clinically relevant protein aggregation. Hence, I am very familiar with tissue culture, transgenic animals as disease models, studies of protein aggregation, and as a former rheumatologist, osteoarthritis.

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Referee #1

Evidence, reproducibility and clarity

The paper by Yammine et al addresses a major problem in peculiarities of genotype to phenotype manifestation in collagen II and chondrodysplasia. It is a lucid and comprehensive study detailing what they see as the fundamental mechanism of Gly1170 Ser mutated Col2a1 gene.

At the heart of the matter is the debunking of the results from a mouse model generated by liang et al (Plos one 2014) paper in which the authors suggested that the phenotype seen only homozygous mice (heterozygous mice appear normal), was related to ER stress -UPR-apoptosis cascade resulting in the chondrodysplasia. Yammine et al paper uses a different model, a robust human iPSC-based tissue, with a CRISPRed variant show that despite the ability of the variant chondrocytes to deposit a Gly1170Ser-substituted collagen II in both the hetero- and homozygous models, is not accompanied by any substantive UPR. The authors of this current paper also argue that their model system is most closely resemble the human context, where heterozygous individual show pathology.

I have sieved all the data related to this topic and have gone back to examine the data and what struck me was the repeated use of the phrase "slow to fold" in the current paper and wondered whether the element of "TIME" is as important in the chondrogenesis of either models and it is this element that generate the difference between the two results?

While iPSC-based tissue takes up to 44 days, a female mouse would have had two litters in this time and made many more growth plates. Could it be by "slowing" the chondrogenesis pathway, which is part of the procedure of differentiation of iPS cells into chondrocytes, the ER is not as "stressed" as in mouse development? I would like the authors to reflect and comment and put forward their view given UPR signaling pathways play a crucial role in chondrocytes in phases of high protein synthesis, e.g., during bone development by endochondral ossification (Journal of Bone Metabolism, vol. 24, no. 2, pp. 75-82, 2017).

This is not withstanding the good argument given by the authors in defending their robust results, namely that the there is no evidence that the hydrophilic triple-helical domain of pro-collagen binds BiP, the main detector of accumulated misfolded proteins. What then do they make out of the immunostaining and qPCR with ER stress related genes in Liang et al paper?? I know that the data is not theirs but a comment on the indisputable data gives the reader a better understanding.

Although I understand the choice of cell lines for overexpression, the transfection of the HT-1080 cells using wild-type and Gly1170Ser COL2A1encoding plasmids are not a match to the in vivo model (variation of efficiency, etc.) the appearance of BiP even at a lower fold increase does not negate ER stress, as the authors acknowledge but more important is what other paracrine signals which triggers the UPR signally pathway which is not linked to BiP ? or an iPS system may lack? Is there anything else not only ATF6α (activating transcription factor 6 alpha), but IRE1α (inositol-requiring enzyme 1 alpha), and PERK (protein kinase RNA-like endoplasmic reticulum kinase). The authors have given us plenty of alternatives that are relevant, and they prepared us for yet another paper on articular cartilage using iPS tissue model which I am looking forward to.

Significance

I think this paper is publishable and it is important in understanding the mechanism by which mutation in collagen type II affect chondrogenesis and therefore bone formation.

This paper will appeal to musculoskeletal scientist especially those who are interested in bone and its pathology.

It would be important for the authors to respond to the critique of "TIME" and speed of protein synthesis which create a duress in the ER pathway.

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Reply to the reviewers

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

1. In this manuscript, Imoto et al. analyze the specific role of the Dynamin1 splice variant Dyn1xA in so-called ultrafast endocytosis, an important mechanism of synaptic vesicle recycling at synapses. In a previous publication (Imoto et al. Neuron 2022), some of the authors had shown that Dyn1xA, and not the other splice variant Dyn1xB, is essential for ultrafast endocytosis. Moreover, Dyn1xA forms clusters around the active zone for exocytosis and interacts with Syndapin 1 in a phosphorylation dependent manner. However, it was unclear which molecular interactions underlie the specific role of Dyn1xA. Here, the authors provide convincing evidence with pull down assays and CSP that Dyn1xA PRR interacts with EndophilinA1/2 with two binding sites. The first binding site lies in the part common to xA and xB, was previously characterized. The second site was previously uncharacterized, is specific for Dyn1xA, and is regulated by phosphorylation (phosphobox 2). The location of these splice variants and mutated forms at presynaptic sites correlate with the prediction made by the biochemical assays. Finally, the authors perform rescue experiments ('flash and freeze' and VGLUT1-pHluorin imaging experiments) to show that Dyn1xA-EndophilinA1/2 binding is important for ultrafast endocytosis. I find the results interesting, providing an important step in the understanding of the interplay between dynamin and the endocytic proteins interacting with it (endophilin, syndapin, amphiphysin) in the context of synaptic vesicle recycling. The manuscript is clearly written and for the most part the data supports the authors' conclusions (see specific comments below). However, there are some issues which need to be clarified before this manuscript is fully suitable for publication.

We thank the reviewer for noting the importance of our study. Indeed, our previous study has raised the question as to why only the Dyn1xA splice variant mediates ultrafast endocytosis, and our current manuscript now resolves this issue.

Introduction: the dynx1B Calcineurin binding motif is written PxIxIT consensus but actual sequence is PRITISDP. Is this a typo?

The sequence is correct. One thing we failed to mention is that the last amino acid in this motif can be either threonine or serine for calcineurin binding, as we demonstrated previously [Jing, et al., 2011 JBC; PMC3162388]. We have amended the text as follows.

1. calcineurin-binding motif (PxIxI[T/S]) 19.

Figure 1: the difference between the constructs used in panels C and D is not clear. In D, is it a truncation without residues 796 and 845? If so, it should be labelled clearly in the Western blots. In Panel E, Dyn1xA 746-798 should be labeled Dyn1x 746-798 because it is common to both splice variants.

We thank the reviewer for pointing this out. Both C and D used the full-length PRRs of Dyn1xA-746 to 864 and xB-746 to 851. To make the labeling clear, we changed Dyn1xA PRR to “Dyn1xA PRR (746-864)” and Dyn1xB PRR to “Dyn1xB PRR 746-851” in Figure 1. In the main text, we made the following changes.

1. 4: “To identify the potential isoform-selective binding partners, the full-length PRRs of Dyn1xA746-864 and xB746-851 (hereafter, Dyn1xA-PRR and Dyn1xB-PRR, respectively).”

Figure 1: For amphiphysin binding the authors write that "No difference in binding to Amphiphysin 1 was observed among these peptides (Figure1D-F)." They should write that Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain, confirming the specificity of binding to the 833-838 motif.

We edited the sentence as suggested.

1. “Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain (Figure 1G), confirming the specificity of binding to the 833-838 motif as reported in previous studies 29,30. (Figure 1D-F).”

Figure S2. The panels are way too small to see the shifts and the labelling. Please provide bigger panels

As suggested, we have now provided bigger panels in Figure S2, and amended the text and Figure legend accordingly.

We also removed Figure S2B as it was not referred to in the text in any way. (It was the reverse experiment – HSQCs of 15N-labelled SH3 titrated with unlabelled dynamin).l

Figure 2 panel B. There is a typo in the connecting line between the sequence and the CSP peaks. It is 846 instead of 864 (after 839).

Corrected.

Figure 3 panel E. In the text, the authors write that "Western blotting of the bound proteins from the R838A pull-down experiment showed that R838A almost abolished both Endophilin and Amphiphysin binding in xA806-864 (Figure 3D), and reduced Endophilin binding to xA-PRR (Figure 3E)." I think they should write "only slightly reduced Endophilin binding..." it is more faithful to the result and consistent with the conclusion that Endophilin A1 has two binding sites on Dyn1xA PRR.

We have now provided quantitative data for R838A and R846A (Fig. 3F and G). Endophilin binding is significantly reduced with R846A.

It is unclear why the R846A mutant affects binding of Dyn1xA 806-864 but not Dyn1xA-PRR-.

The reviewer asks why the R846A mutant affects binding of Dyn1xA 806-864, but not so much of Dyn1xA-PRR. The explanation is simply that there are two endophilin binding sites in Dyn1xA-PRR. The first is not present in the xA806-864 peptide, while both are present in Dyn1xA-PRR (the full length tail). When doing pull-down experiments, the binding tends to saturate – even when the second site is blocked by R846A. The first site is still able to bind, and the binding appears as normal. The same applies to the R838A mutant.

Moreover, it affects binding to endophilin as well as amphiphysin, and therefore it is not specific. It is thus not correct to write that "R846 is the only residue found to specifically regulate the Dyn1 interaction with Endophilin as a part of an SDE". In the Discussion (page 11), the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding. For this important point, the data on quantification of Endophilin binding should be presented.

The reviewer’s concern is about our claims of specificity of Endophilin A binding in Dyn1xA R846 mutation experiments. The reviewer is correct, and we have now defined specific parameters for those claims. Specifically, we have added new quantitative data from the Western blots in Fig 3E (full-length Dyn1aX-PRR) as Fig 3F-G. We used full-length Dyn1aX-PRR rather than the xA806-864 peptide because the subsequent transfection experiments use full length Dyn1xA. In the new figures 3F and 3G, we quantified Endophilin A, Amphiphysin and Syndapin1 amounts from the multiple Western blots such as Figure 3E (now n=14, 6 experiments, each in with 2-4 replicates for Dyn1xA PRR). R846A mutated in Dyn1xA-PRR significantly reduces the binding to Endophilin A, but it does not significantly affect the binding to Amphiphysin 1and Syndapin1 (Fig 3G). Therefore, this particular Dyn1xA-PRR mutation specifically affects Endophilin A binding, in the context of the full-length tail Dyn1aX-PRR. To make these results clear, we modified the text as below.

P7. “R838A and R846A caused smaller reductions in Endophilin binding compared to wild-type Dyn1xA-PRR, (Figure 3E, 3F, R838A, median 68.5 ; Figure 3G, R846A, median 59.3 % : R838A reduced the Dyn1/Amphiphysin interaction (Figure 3E, 3F, median 14.2 % binding compared to wild-type Dyn1xA-PRR). By contrast, R846A did not affect Amphiphysin and Syndapin binding to Dyn1xA-PRR (Figure 3E, 3G). Therefore, R846, being part of an SDE, is the only residue we found to specifically regulate the Dyn1 interaction with Endophilin in the context of the full length tail (DynxA-PRR)”.

Additionally, the reviewer notes that “the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding.” In the light of the above data and new quantitative analysis (Fig 3F-G), we have clarified the conclusion. However, to be clear that this statement is only correct in the context of the full-length DynxA-PRR, we amended texts as follows:

P7. “By contrast, R846A did not affect Amphiphysin and Syndapin binding to Dyn1xA-PRR (Figure 3E, 3G). Therefore, R846, being part of an SDE, is the only residue we found to specifically regulate the Dyn1 interaction with Endophilin in the context of the full length tail (DynxA-PRR)”.

New legends for Figure 3F and G have now been added as follows.

“(F) The binding of Endophilin A, and Amphiphysin 1 and Syndapin1 to Dyn1xA-PRR (wild type) or R838A mutant quantified from Western blots in (E). n=14 (6 experiments with 2-4 replicates in each). Median and 95% confidential intervals are shown. Kruskal-Wallis with Dunn’s multiple comparisons test (**p (G) The binding of Endophilin A, and Amphiphysin 1 and Syndapin1 to Dyn1xA-PRR (wild type) or R846A mutant quantified from Western blots in (E). n=14 (6 experiments with 2-4 replicates in each). Median and 95% confidential intervals are shown. Kruskal-Wallis with Dunn’s multiple comparisons test was applied (*p

Figure 3F-G (which are now 3H and 3I in the revised text): what do the star symbols represent in the graphs? I guess the abscissa represents retention time. Please write it clearly instead of a second ordinate for molecular mass, which does not make much sense if this reflects the estimate for the 3 conditions.

The “stars” are crosses (x) and represent individual data points. The figure legends have been updated for clarity. The reviewer is correct that the X-axis is retention time (min). The second Y-axis is needed to define the points in the curve marked with crosses (x’s). The legends for Figure 3H and I are now changed as follows.

“(H) SEC-MALS profiles for Dyn1xA alone (in green), Endophilin A SH3 alone (in red) and the complex of the two (in black) are plotted. The x-axis shows retention time. The left axis is the corresponding UV absorbance (280 nm) signals in solid lines, and the right axis shows the molar mass of each peak in crosses. The molecular weight of the complex was determined and tabulated in comparison with the predicted molecular weight. x represent individual data points.

(I) SEC-MALS profiles for a high concentration of Dyn1xA-PRR/Endophilin A SH3 complex (0.5 mg) (in dark blue) and a low concentration of Dyn1xA-PRR/endophilin A SH3 complex (0.167 mg) (in blue). The x-axis shows retention time. The left axis is the corresponding UV absorbance (280 nm) signals in solid lines, and the right axis shows the molar mass of each peak in crosses. The molecular weight of the complex was determined and tabulated in the table. x represent individual data points.”

Figure 4: The statement that "By contrast [to Dyn1xA], Endophilin A1 or A2 formed multiple clusters (1-5 clusters)" is not at all clear on the presented pictures. The authors should provide views of portions of axons with several varicosities, for the reader to appreciate the cases where there are more EndoA clusters than Dyn1 clusters.

In the revised Figure S4, we added additional STED images for a region of axons with more EndoA1/2 clusters than Dyn1xA clusters. The locations of Dyn1xA and EndoA1/2 clusters are annotated in each image based on the local maximum of intensity, which is determined using our custom Matlab analysis scripts (Imoto, et al., Neuron 2022; for the description of the methods, please refer to the Point #14 below). We also added Figure S3 to describe our analysis pipelines. In the Dyn1xA channel, outer contour indicates 50% of local maxima (boundary of Dyn1xA cluster) while inner contour indicates 70% of local maxima of the clusters. In the EndoA1/2 channel, local maxima of the clusters are indicated as points. To reflect these changes, we modified text as below.

P 9. “By contrast, Endophilin A1 or A2 formed multiple clusters (1-5 clusters) (Figure S4)”

The legends for Figure S4 are now as follows.

“Figure S4. Additional STED images for Figure 4.

(A) The top image shows an axon containing multiple boutons. Signals show overexpression of GFP-tagged Dyn1xA (Dyn1xA) and mCherry-tagged Endophilin A1 (EndoA1). The bottom images show magnifications of four boutons in the top image. Red hot look-up table (LUT) images on the right side of Dyn1xA and EndoA1 images are enhanced contrast images. Outer and inner contours represent 50% and 70% of local maxima of the Dyn1xA, respectively. Black circles represent local maxima of Endophilin A1. In these boutons, multiple EndophilinA1 puncta are present.

(B) The top image shows an axon congaing multiple boutons. Signals show overexpression of mCherry-tagged Dyn1xA (Dyn1xA) and GFP-tagged Endophilin A1 (EndoA1). The bottom images show magnifications of four boutons in the top image. Red hot LUT images on the right side of Dyn1xA and EndoA2 images are enhanced contrast images. Outer and inner contours represent 50% and 70% of local maxima of the Dyn1xA, respectively. Black circles represent local maxima of Endophilin A2. In these boutons, multiple EndophilinA2 puncta are present.

(C) STED micrographs of the same synapses as in Figure 4E with an active zone marker Bassoon (magenta) visualized by antibody staining. GFP-tagged Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A (green) are additionally stained with GFP-antibodies. Local maxima of Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A signals and minimum distance to the active zone boundary are indicated by dark blue lines.”

Moreover, overexpression of EndophilinA1/2-mCherry is not sufficient to assess its localization. Please consider either immunofluorescence or genome editing (e.g. Orange or TKIT techniques).

We agree with the reviewer that overexpression obscures the endogenous localization of proteins. To address this point in our previous publication, we titrated the amount of plasmids for Dyn1xA-GFP and transfected neurons just for 20 hours – this protocol allowed us to uncover the endogenous localization of Dyn1xA despite the fact that it was overexpressed in wild-type neurons (Imoto, et al., 2022). We also confirmed this localization by ORANGE-based CRISPR knock-in of GFP-tag in the endogenous locus of Dyn1 just after the exon 23 and confirm the true endogenous localization of Dyn1xA (Imoto, et al., 2022). Similar approaches were taken by the Chapman lab to localize Synaptotagmin-1 and Synaptobrevin 2 in axons (Watson et al, 2023, eLife, PMID: 36729040). We did not emphasize this in the first submission, but we took the same approach for the EndoA1/2 localization. This does not mean that they also unmask the endogenous localization, and the reviewer is correct that additional evidence would strengthen the data here. Thus, as suggested, we have looked at the endogenous EndophilinA1 localization by antibody staining. As the reviewer is likely aware, EndophilinA1 also localizes to other places including dendrites and postsynaptic terminals, making it difficult to analyze the data. However, we observe colocalization of Dyn1xA with endogenous EndoA1. Thus, we believe that our major conclusion here drawn based on EndoA1/2-mCherry overexpression is valid (Reviewer’s Figure 1). Since the Endophilin signals in neighboring processes obscures its localization in synapses-of-interest, repeating this localization experiments with ORANGE-based knock-in would be ideal. However, with the lead author starting his own group and many validations needed to confirm the knock-in results, this experiment would require us at least 4-6 months, and thus, it is beyond the scope of our current study. We will follow up on this localization in the near future, but given that endophilin is required for ultrafast endocytosis (Watanabe, et al., Neuron 2018, PMID: 29953872) and these proteins need to be in condensates at the endocytic sites for accelerating the kinetics of endocytosis (Imoto, et al., Neuron 2022, PMID: 35809574), we are confident that endogenous

EndoA1/2 are localized with Dyn1xA.

The analysis of the confocal microscopy data is not explained. How is the number of clusters determined? How far apart are they? Confocal microscopy may not have the resolution to distinguish clusters within a synapse.

We apologize for the insufficient description of the method. We had provided a more thorough description of the methods in our previous publication (Imoto, et al., Neuron 2022, PMID: 35809574). To make this more automated, we improved our custom Matlab scripts. Please note that all the analysis for the cluster location is performed on STED images, not on normal confocal images. To determine the cluster, first, presynaptic regions (based on Bassoon signals or Dyn1xA signals within boutons) in each STED image are cropped with 900 by 900 nm (regions-of-interest) ROIs. Then, our Matlab scripts calculate the local maxima of fluorescence intensity within the ROIs. To determine the distance between the active zone and the Dyn1xA or EndoA1/2 clusters, the Matlab scripts perform the same local maxima calculations in both channels and make contours at 50% intensity of the local maxima. The minimum distance reflects the shortest distance between the active zone and Dyn1xA/EndoA1/2 contours. To make these points clearer, we modified the main text and the Methods section. In addition, we have added workflow of these analysis as Figure S3.

P9. Main. “Signals of these proteins are acquired by STED microscopy and analyzed by custom MATLAB scripts, similarly to our previous work23.”

P20. Methods. “All the cluster distance measurements are performed on STED images. For the measurements, a custom MATLAB code package23 was modified using GPT-4 (OpenAI) to perform semi-automated image segmentation and analysis of the endocytic protein distribution relative to the active zone marked by Bassoon or relative to Dyn1xA cluster in STED images. First, the STED images were blurred with a Gaussian filter with radius of 1.2 pixels to reduce the Poisson noise and then deconvoluted twice using the built-in deconvblind function: the initial point spread function (PSF) input is measured from the unspecific antibodies in the STED images. The second PSF (enhanced PSF) input is chosen as the returned PSF from the initial run of blind deconvolution62. The enhanced PSF was used to deconvolute the STED images to be analyzed. Each time, 10 iterations were performed. All presynaptic boutons in each deconvoluted image were selected within 3030-pixel (0.81 mm2) ROIs based on the varicosity shape and bassoon or Dyn1xA signals. The boundary of active zone or Dyn1xA puncta was identified as the contour that represents half of the intensity of each local maxima in the Bassoon channel. The Dyn1xA clusters and Endophilin A clusters were picked by calculating pixels of local maxima. The distances between the Dyn1xA cluster and active zone boundary or Endophilin A clusters were automatically calculated correspondingly. For the distance measurement, MATLAB distance2curve function (John D'Errico 2024, MATLAB Central File Exchange) first calculated the distance between the local maxima pixel and all the points on the contour of the active zone or Dyn1xA cluster boundary. Next, the shortest distance was selected as the minimum distance. Signals over crossing the ROIs and the Bassoon signals outside of the transfected neurons were excluded from the analysis. The MATLAB scripts are available by request.”

In the legend of Figure S3,

“Protein localization in presynapses is determined by semi-automated MATLAB scripts (see Methods).

(A) Series of deconvoluted STED images are segmented to obtain 50-100 presynapse ROIs in each condition.

(B) Two representations of the MATLAB analysis interface are shown. The first channel (ch1, green) is processed to identify the pixels of local maxima within this channel. The second channel (ch2, magenta) is normally an active zone protein, Bassoon. Active zone boundary is determined by the contour generated at 50% intensity of the local maxima of ch2. The contours outside of the transfected neurons are manually selected on the interface and excluded from the analysis. Minimum distances from each pixel of the local maxima in ch1 to the contour in ch2 are calculated and shown in the composite image. The plot “Distance distribution” shows all the minimum distance identified in this presynapses ROI (unit of the y axis is nanometer). The plot “Accumulated distance distribution” shows the accumulated distance distribution from the initial to the current presynapses ROI. The plot “Histogram of total intensity” shows the intensity counts around individual local maxima pixels in ch1.”

For the STED microscopy, a representation of the processed image (after deconvolution) and the localization of the peaks would be important to assess the measurement of distances. If Dyn1xA S851/857D is more diffuse, are there still peaks to measure for every synapse?

We thank the reviewer for bringing up this important question. In Figure S4C, we have added the position of the local maxima of wild-type and mutant Dyn1xA shown in the main Figure 4E. As the reviewer pointed out, when a protein is more diffuse, it is difficult to find the peak intensity by STED. However, since these proteins are still found at a higher density within a very confined space of a presynapse and synapses are packed with organelles like synaptic vesicles and macromolecules, signals from even diffuse proteins can be detected as clusters, and local maxima can be detected in these images.

To illustrate this point better, we added Reviewer’s Figure 2 below. In this experiment, we transfected neurons with a typical amount of plasmids (2.0 µg/well) or ~10x lower amount (0.25 µg/well). When the density of cytosolic proteins is high (Reviewer’s Figure 2A), the depletion laser has to be strong enough to induce sufficient stimulated emission and resolve protein localization. Insufficient power would produce low resolution images, leading to inappropriate detection of the local maxima (Reviewer’s Figure 1A). Thus, we set our excitation and depletion laser powers to resolve the protein localization to ~40-80 nm at presynapses. Furthermore, to avoid mislocalization of proteins due to the overexpression, we use 0.25-0.5 ug/well (in 12-well plate) of plasmid DNA for transfection, which is around 10 times lower than the amount used in the typical lipofectamine neuronal transfection protocol (Imoto, et al., Neuron 2022). We also change the medium around 20 hours after the transfection instead of the typical 48 hours (Imoto, et al., Neuron 2022). With these modifications and settings, we can obtain the location of the local maxima of the diffuse signals (Reviewer’s Figure 1B and Figure 4E and Figure S4). We modified the Method section to make these points clearer.

P 17, “Briefly, plasmids were mixed well with 2 µl Lipofectamine in 100 µl Neurobasal media and incubated for 20 min. For Dyn1xA and Endophilin A expressions, 0.5 µg of constructs were used to reduce the overexpression artifacts23. The plasmid mixture was added to each well with 1 ml of fresh Neurobasal media supplemented with 2 mM GlutaMax and 2% B27. After 4 hours, the medium was replaced with the pre-warmed conditioned media. To prevent too much expression of proteins, neurons were transfected for less than 20 hours and fixed for imaging.”

P 20, “Quality of the STED images are examined by comparing the confocal and STED images and measuring the size of signals at synapses and PSF (non-specific signals from antibodies).”

Legends for Figure S4C,

“(C) STED micrographs of the synapses shown in Figure 4F with an active zone marker Bassoon (magenta). GFP-tagged Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A are visualized by antibody staining of GFP (green). Local maxima of Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A signals and minimum distance to the active zone boundary are overlaid.”

Figures 5 and 6: No specific comment. The data and its analysis are very nice and elegant. The comment on the lack of rescue of Dyn1xA on endosome maturation may be a bit overstated, because many "controls" (shRNA control Figure S5 or Dyn3 KO in Imoto et al. 2022) have a significant number of endosomes 10 s after stimulation.

We thank the reviewer for noting the strength of our data and pointing out this issue on endosomal resolution. In particular, the reviewer is concerned about our interpretation of the ferritin positive endosomes present at 10 s in time-resolved electron microscopy experiments. Indeed, the number of ferritin positive endosomes in Dyn1 KO, Dyn1xA OEx neurons (0.1/profile) is similar to the control conditions: scramble shRNA control (0.1/profile, Figure S5) and Dyn3KO neurons (0.2/profile) in our previous study (Imoto et al. 2022). Although we do not consider Dyn3 KO as a control, given the presence of abnormal endosomal structures, we agree with the reviewer that scramble shRNA control in Figure S5 does indicate that some ferritin-positive endosomes even at 10 s after stimulation. We would like to note that this result is in stark contrast to our previous studies where we observed the number of ferritin positive endosomes returning to the basal level in both wild-type neurons and many scramble shRNA controls (Watanabe et al. 2014, 2018, Imoto et al 2022). Thus, the majority of the data we have indicate that the number of ferritin positive endosomes returns to basal level by 10 s, suggesting that endosomes are typically resolved into synaptic vesicles by this time. However, given that we do not know the nature of the inconsistency here and we cannot exclude the possibility of overexpression artifact of Dyn1xA as an alternative, we changed the following lines.

P. 10, “Interestingly, the number of ferritin-positive endosomes did not return to the baseline (Figure 5E, F) as in previous studies3,35,36, suggesting that Dyn1xA may not fully rescue the knockout phenotypes or that overexpression of Dyn1xA causes abnormal endosomal morphology.”

By the way, why did the authors use Dyn1 KO in this study, and not Dyn1,3 DKO as in Imoto et al. 2022?

This is simply because Dyn3KO displayed an endosomal defect in our previous study (Imoto et al 2022), and we wanted to focus on endocytic phenotypes of Dyn1 KO and mutant rescues in this study.

In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent. However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle. Even though they provide evidence in vitro (Figure 3) that in these conditions of high concentration one dyn1xA-PRR binds one SH3 domain, in cells multiple binding sites on the PRR to these proteins may involve avidity effects, as discussed for example in Rosendale et al. 2019 doi 10.1038/s41467-019-12434-9. For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.

The reviewer suggests “In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent.” However, we do not claim these interactions are functionally independent, except in the context of in vitro experiments where they are sequence-independent.

They also suggest “However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle”. However we do not agree with this in the context of our Discussion, because the evidence of multimers and clustering is convincing but is entirely in vitro data.

Thirdly they comment that “For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.” We fully agree with the statement and felt we had addressed this in the manuscript. To explain, it’s important to point out our relatively new concept here and previously reported by us (Lin Luo et al 2016, PMID: 26893375) of the existence and importance of SDE and LDE for SH3 domains (Endophilin here, syndapin in our previous report). These elements act at a distance from the so-called core PxxP motifs and they provide much higher affinity and specificity than the core region alone. We had further mentioned this in the p11 discussion “Although this is a previously characterized binding site for Amphiphysin and is also present in Dyn1xB-PRR, the extended C-terminal tail of Dyn1xA contains short and long distance elements (SDE and LDE) essential for Endophilin binding, making it higher affinity for Endophilin.” Because the NMR identified F862 as a chemical shift for dynamin, we performed a pulldown with this mutant in the xA746-798 construct (which only contains the higher affinity site) and found that indeed “.F862A reduced Endophilin binding 29% (pOverall, the reviewer correctly points out that “multiple binding sites on the PRR to these proteins may involve avidity effects*” could play a role in vivo. We agree that avidity is an additional possibility, not examined in our study. Therefore, as suggested, we added the following sentence to the discussion on the SDE and LDE impacts.

P. 11. “Our pull-down results showed that R846A abolished endophilin binding to xA806-864 (which contains only the second and higher affinity binding site and the associated SDE (A839) and LDE (F862)) and reduced about 40% of endophilin binding to the Dyn1xA-PRR (which contains both binding sites) without affecting its interaction with Amphiphysin, providing important partner specificity, although we cannot exclude the possibility that avidity effects may additionally come in play in vivo 42

Reviewer #1 (Significance (Required)):

This study provides a significant advance on the mechanisms of dynamin recruitment to endocytic zones in presynaptic terminals. The work adds a significant step by experienced labs (Robinson, Watanabe) who have provided important insight in the mechanisms by many publications in the last years.

We thank the reviewer for the careful read of our manuscript and positive outlook of our work.

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

1. This is a compelling study that reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. The authors demonstrate that the Dynamin splice version 1xA (Dynamin 1xA) uniquely binds Endophilin A, in contrast to Dynamin splice version 1xB (Dynamin 1xB) that does not bind Endophilin A and it is not required for ultrafast endocytosis. In addition, the Endophilin A binding occurs in a dephosphorylation-regulated manner. The study is carefully carried out and it is based on high quality data obtained by means of advanced biochemical methodologies, state-of-art flash-freezing electron microscopy analysis, superresolution microscopy and dynamic imaging of exo-and endocytosis in neuronal cultures. The results convincingly support the conclusions.

We thank the reviewer for supporting the conclusions of our study.

1. Although additional experiments are not essential to support the claims of the paper there is room, however, for improvement within the pHluorin experiments. These experiments, that are clearly informative and consistent with the rest of experimental data, do not apply the useful approach to separate endo- from exocytosis. The use of bafilomycin or folimycin to block the vesicular proton pump allows the unmasking the endocytosis that is occurring during the stimulus, that should correspond to ultrafast endocytosis. It would be very elegant to demonstrate that such a component, as expected according to the electron microscopy data, requires the binding of Endophilin A to Dynamin 1xA. If the authors have the pHluorin experiments running, the suggested experiments are very much doable because the reagents and the methodology is already in place and the new data could be generated in around six weeks.

We thank the reviewer for the suggestion. The reviewer is concerned that vGlut1 pHluorin experiment in Figure 6 may not correspond to ultrafast endocytosis. We agree that bafilomycin/folimycin treatment will reveal the amount of endocytosis that takes place while neurons are stimulated. However, we are not certain that endocytosis during this phase would fully correspond to ultrafast endocytosis because reacidification of endocytosed vesicles typically takes 3-4 s (Atluri and Ryan, 2006, PMID: 16495458; although see https://elifesciences.org/articles/36097) and thus, the nature of endocytosis cannot be fully determined by this assay. To claim that endocytosis measured by pHluorin assay during stimulation all correspond to ultrafast endocytosis, we would need to perform very careful work to track single pHluorin molecules at the ultrastructural level and corelate their internalization to pHluorin signals. Perhaps, a rapid acid quench technique used by the Haucke group would also be appropriate to estimate the amount of ultrafast endocytosis (Soykan et al. 2017 PMID: 28231467), but we are not set up to perform such experiments here. Also, our lead author, Yuuta Imoto, is leaving the lab to start up his own group, and it will take us months rather than weeks to get the requested experiments done. Since the point of this experiment was to test whether the interaction of Dyn1xA and EndoA is essential for protein retrieval regardless of the actual mechanisms and the reviewer acknowledges that this point is sufficiently supported by the experiments, we will set this experiment as the priority for the next paper.

Instead of the bafilomycin or rapid acid quenching experiments, we have now added data from vglut1-pHluorin experiment with a single action potential. With a single action potential, all synaptic vesicle recycling is mediated by ultrafast endocytosis in these neurons (Watanabe et al, 2013 PMID: 24305055; Watanabe et al. 2014, PMID: 25296249). Our electron microscopy experiments in Figure 5 is also performed with a single action potential. As with 10 action potentials, 20 Hz experiments, re-acidification of vglut1-pHluorin is blocked when Dyn1 and EndophilinA1 interaction is disrupted (Figure 6 F-I). We added a description of this result as below.

P 11. “Similar defects were observed when the experiments were repeated with a single action potential – synaptic vesicle recycling is mediated by ultrafast endocytosis with this stimulation paradigm25 (S851/857 recovery is 73.3% above the baseline; R846A, recovery is 30.0% above the baseline) (Figure S9 A-D). Together, these results suggest that the 20 amino acid extension of Dyn1xA is important for recycling of synaptic vesicle proteins mediated by specific phosphorylation and Endophilin binding sites within the extension.”

The methods are carefully explained. Some of the experiments are only replicated in two cultures and the authors should justify the reasons to convince the audience that the approaches used have enough low variability for not increasing the n number. The pHluorin experiments, however, are performed only in a single culture; they should replicate these experiments in at least 3 different cultures (three different mice).

The reviewer is correct. The variability is very low in our ultrastructural studies and STED imaging, and thus, in all our previous publications, two independent cultures are used. We do agree that in the ideal case, we would like to have three independent cultures, but given the nature of ultrastructural studies (control, mutants, and multiple time points), triplicating the data would add another year to our work. We are currently developing AI-based segmentation analysis, and once this pipeline is established, we will be able to increase N. However, please note that for these experiments, we examine around 200 synapses from each condition in electron microscopy studies (Table S2)– these numbers are far more than the gold standard in the field. Likewise, 50-100 synapses are examined for STED experiments (Table S2). To examine variability of our analysis results, we compared a significance between the dataset using cumulative curves and Kolmogorov–Smirnov test (Figure S11). As shown in the summarized data and p value in each condition, there are no significant difference between the datasets.

For pHluorin analysis, the reviewer is correct. We repeated the experiments twice to increase the N after the initial submission. The data are consistent, and the conclusions are not changed by the additional experiments (Figure 6 and Figure S9). We also changed the Statistical analysis section in Methods as below.

P. 19. “All electron microscopy data are pooled from multiple experiments after examined on a per-experiment basis (with all freezing on the same day); none of the pooled data show significant deviation from each replicate (Table S2).”

p 19, “All fluorescence microscopy data were first examined on a per-experiment basis. For Figure 4, the data were pooled; none of the pooled data show significant deviation from each replicate (Figure S11 and Table S2). Sample sizes were 2 independent cultures, at least 50-100 synapses from 4 different neurons in each condition..”

Legends for Figure S11

Figure S11. Data variability in Figure 4.

Cumulative curves are made from each dataset of (A) distance of Endophilin A1 puncta from the edge of Dyn1xA puncta, (B) distance of Endophilin A2 puncta from the edge of Dyn1xA puncta, distance distribution of Dyn1xA from active zone edge in (C) neurons expressing wild-type Dyn1xA-GFP, (D) Dyn1xA-S851/857-GFP and (E) Dyn1xA-R846-GFP. n > 4 coverslips from 2 independent cultures. Kolmogorov–Smirnov (KS) test, p values are indicated in each plot.

Minor comments: 4. Prior studies referenced appropriately and the text and figures are clear and accurate.

We thank the reviewer for the careful read of our manuscript.

The authors should discuss about the mediators (enzymes) responsible for dephosphorylation of phosphor-box 2 that is key for the Dynamin 1xa-Endophilin A interaction.

We thank the reviewer for the suggestion. We added a discussion on a potential mediator, Dyrk1, as below.

P. 12. ”What are the kinases that regulate Dyn1? The phosphorylation of phosphobox-1 is mediated by Glycogen synthase kinase-3 beta (GSK3ß) and Cyclin-dependent kinase 5 (CDK5)17, while phosphobox-2 is likely phosphorylated by Trisomy 21-linked dual-specificity tyrosine phosphorylation-regulated kinase 1A (Mnb/Dyrk1)44,45 since Ser851 in phosphobox-2 is shown to be phosphorylated by Mnb/Dyrk1 in vitro32. Furthermore, overexpression of Mnb/Dyrk1 in cultured hippocampal neurons causes slowing down the retrieval of a synaptic vesicle protein vGlut146. Consistently, our data showed that phosphomimetic mutations in phosphobox-2 results disruption of Dyn1xA localization, perturbation of ultrafast endocytosis, and slower kinetics of vGlut1 retrieval. However, how these kinases interplay to regulate the interaction of Dyn1xA, Syndapin1 and Endophilin A1 for ultrafast endocytosis is unknown.”

It would be very helpful to include a final cartoon depicting the key protein-protein interactions regulated by dephosphorylation (activity) and the sequence of molecular events that leads to ultrafast endocytosis

As suggested, we made a model figure, (new Figure 7) showing how Dyn1xA and its interaction with EndoA and Syndapin1 increases the kinetics of endocytosis at synapses. Regarding the sequence of molecular events, we think that there are already dephosphorylated fraction of Dyn1xA molecules sitting on the endocytic zone at the resting state and they mediate ultrafast endocytosis. However, it is equally possible that activity-dependent dephosphorylation of Dyn1xA also may play a role (Jing et al. 2011, PMID: 21730063). However, we have no evidence about the sequence of activity dependent modulation of Dyn1xA and its binding partners during ultrafast endocytosis yet. This is much beyond what we have reported in this work and therefore, excluded from the model figure. We added the following to the end of the discussion:

p13, “Nonetheless, these results suggest that Dyn1xA long C-terminal extension allows multivalent interaction with endocytic proteins and that the high affinity interaction with Endophilin A1 permits phospho-regulation of their interaction and defines its function at synapses (Figure S7)”.

Figure legend Figure 7,

“Figure 7. Schematics depicting how specific isoforms Dyn1xA and Endophilin A mediate ultrafast endocytosis.

A splice variant of dynamin 1, Dyn1xA, but not other isoforms/variants can mediate ultrafast endocytosis. (A) Dyn1xA has 20 amino acid extension which introduces a new high affinity Endophilin A1 binding site. Three amino acids, R846 at the splice site boundary, S851 and S857, act as long-distance element which can enhance affinity of proline rich motifs (PRM) to SH3 motif from outside of the PRM core sequence PxxP. (B) At a resting state, Dyn1xA accumulates at endocytic zone with SH3 containing BAR protein Syndapin 123 and Endophilin A1/2. When phosphobox-1 (Syndapin1 binding) and phosphobox-2 (Endophilin A1/2 binding, around S851/S857) within Dyn1xA PRD are phosphorylated, these proteins are diffuse within the cytoplasm. A dephosphorylated fraction of Dyn1xA molecules can interact with these BAR domain proteins. Loss of interactions including Dyn1xA-R846A or -S851/857D mutations, disrupts endocytic zone pre-accumulations. Consequently, ultrafast endocytosis fails.”

Reviewer #2 (Significance (Required)):

This is a remarkable and important advance in the field of endocytosis. The study reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. Scientist interested in synaptic function and the general audience of cell biologist interested in membrane trafficking will very much value this study. The mechanism reported will potentially be included in textbooks in the near future.

My field of expertise includes molecular mechanisms of presynaptic function and membrane trafficking.

I have not enough experience to evaluate the quality of the NMR experiments, however, I do not have any problem at all with, in my opinion, elegant results reported.

We thank the reviewer for the positive outlook of our manuscript.

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

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

This is a compelling study that reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. The authors demonstrate that the Dynamin splice version 1xA (Dynamin 1xA) uniquely binds Endophilin A, in contrast to Dynamin splice version 1xB (Dynamin 1xB) that does not bind Endophilin A and it is not required for ultrafast endocytosis. In addition, the Endophilin A binding occurs in a dephosphorylation-regulated manner. The study is carefully carried out and it is based on high quality data obtained by means of advanced biochemical methodologies, state-of-art flash-freezing electron microscopy analysis, superresolution microscopy and dynamic imaging of exo-and endocytosis in neuronal cultures. The results convincingly support the conclusions.

Although additional experiments are not essential to support the claims of the paper there is room, however, for improvement within the pHluorin experiments. These experiments, that are clearly informative and consistent with the rest of experimental data, do not apply the useful approach to separate endo- from exocytosis. The use of bafilomycin or folimycin to block the vesicular proton pump allows the unmasking the endocytosis that is occurring during the stimulus, that should correspond to ultrafast endocytosis. It would be very elegant to demonstrate that such a component, as expected according to the electron microscopy data, requires the binding of Endophilin A to Dynamin 1xA. If the authors have the pHluorin experiments running, the suggested experiments are very much doable because the reagents and the methodology is already in place and the new data could be generated in around six weeks.

The methods are carefully explained. Some of the experiments are only replicated in two cultures and the authors should justify the reasons to convince the audience that the approaches used have enough low variability for not increasing the n number. The pHluorin experiments, however, are performed only in a single culture; they should replicate these experiments in at least 3 different cultures (three different mice).

Minor comments:

Prior studies referenced appropriately and the the text and figures are clear and accurate.

1. The authors should discuss about the mediators (enzymes) responsible for dephosphorylation of phosphor-box 2 that is key for the Dynamin 1xa-Endophilin A interaction.
2. It would be very helpful to include a final cartoon depicting the key protein-protein interactions regulated by dephosphorylation (activity) and the sequence of molecular events that leads to ultrafast endocytosis

Significance

This is a remarkable and important advance in the field of endocytosis. The study reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. Scientist interested in synaptic function and the general audience of cell biologist interested in membrane trafficking will very much value this study. The mechanism reported will potentially be included in textbooks in the near future.

My field of expertise includes molecular mechanisms of presynaptic function and membrane trafficking.

I have not enough experience to evaluate the quality of the NMR experiments, however, I do not have any problem at all with, in my opinion, elegant results reported.

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

In this manuscript, Imoto et al. analyze the specific role of the Dynamin1 splice variant Dyn1xA in so-called ultrafast endocytosis, an important mechanism of synaptic vesicle recycling at synapses. In a previous publication (Imoto et al. Neuron 2022), some of the authors had shown that Dyn1xA, and not the other splice variant Dyn1xB, is essential for ultrafast endocytosis. Moreover, Dyn1xA forms clusters around the active zone for exocytosis and interacts with Syndapin 1 in a phosphorylation dependent manner. However, it was unclear which molecular interactions underlie the specific role of Dyn1xA. Here, the authors provide convincing evidence with pull down assays and CSP that Dyn1xA PRR interacts with EndophilinA1/2 with two binding sites. The first binding site lies in the part common to xA and xB, was previously characterized. The second site was previously uncharacterized, is specific for Dyn1xA, and is regulated by phosphorylation (phosphobox 2). The location of these splice variants and mutated forms at presynaptic sites correlate with the prediction made by the biochemical assays. Finally, the authors perform rescue experiments ('flash and freeze' and VGLUT1-pHluorin imaging experiments) to show that Dyn1xA-EndophilinA1/2 binding is important for ultrafast endocytosis. I find the results interesting, providing an important step in the understanding of the interplay between dynamin and the endocytic proteins interacting with it (endophilin, syndapin, amphiphysin) in the context of synaptic vesicle recycling. The manuscript is clearly written and for the most part the data supports the authors' conclusions (see specific comments below). However, there are some issues which need to be clarified before this manuscript is fully suitable for publication.*

Introduction: the dynx1B Calcineurin binding motif is written PxIxIT consensus but actual sequence is PRITISDP. Is this a typo? Figure 1: the difference between the constructs used in panels C and D is not clear. In D, is it a truncation without residues 796 and 845? If so, it should be labelled clearly in the Western blots. In Panel E, Dyn1xA 746-798 should be labeled Dyn1x 746-798 because it is common to both splice variants. For amphiphysin binding the authors write that "No difference in binding to Amphiphysin 1 was observed among these peptides (Figure1D-F)." They should write that Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain, confirming the specificity of binding to the 833-838 motif. Figure S2. The panels are way too small to see the shifts and the labelling. Please provide bigger panels Figure 2 panel B. There is a typo in the connecting line between the sequence and the CSP peaks. It is 846 instead of 864 (after 839). Figure 3 panel E. In the text, the authors write that "Western blotting of the bound proteins from the R838A pull-down experiment showed that R838A almost abolished both Endophilin and Amphiphysin binding in xA806-864 (Figure 3D), and reduced Endophilin binding to xA-PRR (Figure 3E)." I think they should write "only slightly reduced Endophilin binding..." it is more faithful to the result and consistent with the conclusion that Endophilin A1 has two binding sites on Dyn1xA PRR. It is unclear why the R846A mutant affects binding of Dyn1xA 806-864 but not Dyn1xA-PRR. Moreover, it affects binding to endophilin as well as amphiphysin, and therefore it is not specific. It is thus not correct to write that "R846 is the only residue found to specifically regulate the Dyn1 interaction with Endophilin as a part of an SDE". In the Discussion (page 11), the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding. For this important point, the data on quantification of Endophilin binding should be presented. Figure 3F-G: what do the star symbols represent in the graphs? I guess the abscissa represents retention time. Please write it clearly instead of a second ordinate for molecular mass, which does not make much sense if this reflects the estimate for the 3 conditions. Figure 4: The statement that "By contrast [to Dyn1xA], Endophilin A1 or A2 formed multiple clusters (1-5 clusters)" is not at all clear on the presented pictures. The authors should provide views of portions of axons with several varicosities, for the reader to appreciate the cases where there are more EndoA clusters than Dyn1 clusters. Moreover, overexpression of EndophilinA1/2-mCherry is not sufficient to assess its localization. Please consider either immunofluorescence of genome editing (e.g. Orange or TKIT techniques). The analysis of the confocal microscopy data is not explained. How is the number of clusters determined? How far apart are they? Confocal microscopy may not have the resolution to distinguish clusters within a synapse. For the STED microscopy, a representation of the processed image (after deconvolution) and the localization of the peaks would be important to assess the measurement of distances. If Dyn1xA S851/857D is more diffuse, are there still peaks to measure for every synapse? Figures 5 and 6: No specific comment. The data and its analysis is very nice and elegant. The comment on the lack of rescue of Dyn1xA on endosome maturation may be a bit overstated, because many "controls" (shRNA control Figure S5 or Dyn3 KO in Imoto et al. 2022) have a significant number of endosomes 10 s after stimulation. By the way, why did the authors use Dyn1 KO in this study, and not Dyn1.3 DKO as in Imoto et al. 2022? In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent. However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle. Even though they provide evidence in vitro (Figure 3) that in these conditions of high concentration one dyn1xA-PRR binds one SH3 domain, in cells multiple binding sites on the PRR to these proteins may involve avidity effects, as discussed for example in Rosendale et al. 2019 doi 10.1038/s41467-019-12434-9. For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.

Significance

This study provides a significant advance on the mechanisms of dynamin recruitment to endocytic zones in presynaptic terminals. The work adds a significant step by experienced labs (Robinson, Watanabe) who have provided important insight in the mechanisms by many publications in the last years.

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Reply to the reviewers

Please find below a point-by-point reply to the reviewers, with our comments in plain text, and reviewer comments in italics. Direct quotations of MS revisions in the below point-by-point reply are in quotation marks.

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

**The manuscript "Circadian regulation of protein turnover and proteome renewal" investigates the role of protein degradation in the circadian control of proteostasis. The researchers suggest that the relatively static levels of protein levels in a cell are incongruent with the known oscillation in protein synthesis. They therefore hypothesize that there should be a compensatory mechanism to counteract rhythmic protein synthesis, rhythmic protein degradation. To investigate this, they employ bulk pulse chase labeling to study the process of degradation. They identify a synchronization between the creation and turnover of proteins in a cell, implying the clock helps to maintain homeostasis through a novel mechanism. They note that these phases align with energy availability, granting a plausible reasoning behind the biological implementation of this regulation. In summary, this is a sound manuscript that adds to the research field. The experiments in this manuscript are well thought out, organized, and explained. In general, the authors do not go further in their conclusions than I think is warranted given the data that they have, though I think that there are some key items that should be addressed before the publication of this manuscript. *

Thank you for reading and appreciating our work

Major notes: 1) In figure 1, a clearer idea of what the ** means would be appreciated. What was the standard of significance for this measure?

Thank you, this was already reported in the methods section but is now reported in the figure legend also.

* 2) In Figure 1b, it is important to note clearly in the text that the this is not a direct measure of protein degradation, but a subtractive proxy. Though I don't think that necessarily makes the authors conclusions incorrect, the same result could also be obtained if an extra 15% of the proteins were moved into the insoluble fraction. This is the same for Figure 1E and F. *

Considering only the pulse shown in the left-hand graph of 1B, the reviewer is correct that this could arise by rhythmic partitioning of nascently synthesised proteins between digitonin-soluble and insoluble fractions. This could not readily explain the variation in the % of nascently synthesised digitonin-soluble protein that is degraded however (right hand graph), hence the need for pulse-chase rather than pulse alone. As such, we do not exclude circadian-regulated solubility of nascently synthesised protein or that there is a rhythm of protein synthesis in the soluble fraction, both are likely true. Rather Figure 1B indicates the relative proportion of nascently-synthesised protein in the soluble fraction that is degraded within 1h of synthesis is not constant over time. This is consistent with current understanding of the regulated increase in activity of protein quality control mechanisms (including proteasome-mediated degradation) that are required to maintain protein homeostasis upon an increase in bulk translation (Gandin and Topisirovic, Translation, 2014).

In contrast, the lysates probed in Fig 1F were extracted in denaturing urea/thiourea buffer and so cannot be explained by variation in protein solubility.

Considering 1E, to explain this result entirely through solubility changes would require that puromycinylated polypeptides to become more soluble, at discrete phases of the circadian cycle, but only when the proteasome is inhibited. Whilst we cannot formerly exclude this possibility, we are not aware of evidence to support it, whereas there is prior evidence supporting circadian regulation of protein synthesis and proteasome activity.

To communicate all of this more clearly we have made the following revisions to the text:

Page 6: ".The experiment was performed over a 24h time series followed by soluble protein extraction using digitonin, which preferentially permeabilises the plasma membrane over organelle membrane."

Page 6: " Importantly, the proportion of degraded protein varied over time, being highest at around the same time as increased protein synthesis (Fig 1B), indicating time-of-day variation in digitonin-soluble protein turnover which cannot be solely attributed to previously reported circadian regulation of protein solubility (Stangherlin et al, 2021b). Rather, it suggests that global rates of protein degradation may be co-ordinated with protein synthesis rates, and may vary over the circadian cycle."

Fig 1a legend: "...with digitonin buffer"

Fig 1e legend: "...in digitonin buffer"

Fig1f legend: "... and extracted with urea/thiourea buffer"

* 3) In figure 1c, is the noted oscillation in protease activity due to the oscillation of these proteins? What are the predicted mechanisms behind this? I don't think that this is necessarily within the scope of this paper but should be addressed in the discussion. Also, the peak degradation rate from Figure 1B is 4 hours before the peak enzyme activities. How can this observation be reconciled? *

Besides this study, our two previous proteomic investigations of the fibroblast circadian proteome detected no biologically significant or consistent rhythm in proteasome subunit abundance (Wong et al., EMBO J, 2021; Hoyle et al., Science Translational Medicine, 2017). Moreover, proteasomes are long-lived stable complexes whose activity is determined by a combination of substrate-level, allosteric and post-translational regulatory mechanisms that includes their reversible sequestration into storage granules (Albert et al., PNAS, 2020; Fu et al., PNAS, 2021; Yasuda et al., Nature, 2020). It is therefore very likely that the observed rhythm in trypsin- and chymotrypsin-like activity occurs post-translationally. Proteasome subunit composition is also known to change, which might be another reason for differences between the protease activities (Marshall and Vierstra, Front Mol Biosci, 2019; Zheng et al., J Neurochem, 2012).

Due to the nature of the experiment, the degradation rate inferred from Figure 1B does not reflect proteasome activity, exclusively. Rather it reflects the combined sum of processes that remove nascently produced proteins from the cell's digitonin-soluble fraction, which includes proteasomal degradation, but also autophagy, protein secretion and sequestration into other compartments. Therefore, the peak degradation in Fig 1B would not necessarily be expected to coincide with the peak of proteasome activity in Fig 1C. Figure 1A/B is intended as an exemplar for the investigation's rationale and was the first to be performed chronologically.

To communicate this succinctly, we have revised the relevant text as follows:

Page 7: "Previous proteomics studies under similar conditions have revealed minimal circadian variation in proteasome subunit abundance (Wong et al, 2022), suggesting that proteasome activity rhythmicity, and therefore rhythms in UPS-mediated protein degradation, are regulated post-translationally (Marshall & Vierstra, 2019; Hansen et al, 2021)"

* 4) For the pSILAC analysis, the incorporation scheme has a six-hour window between the comparison of the light and heavy peptides. This makes it somewhat difficult to assess whether you are looking a clock effect from T1 or T1+6. This does not negate the findings, but it does question when the synthesis is occurring and what is being compared, which I think should be more clearly discussed in the manuscript. This is discussed later in the manuscript but should be mentioned in this section. *

Thank you for this suggestion. To communicate this more clearly, we have rearranged the labels at the top of schematic graphs in figures 2b and 3b in order to clearly distinguish the pulse-labelling window from the time of sample collection. The following text has been added to the methods section:

Page 9: "To enable sufficient heavy labelling for detection, a 6h time window was employed, thus measuring synthesis and abundance within each quarter of the circadian cycle "

* 5) There are no error bars on figure 2C. What the pSILAC just done in a singlet? If so, the rhythms estimation is likely a large overestimate and should be noted. *

This first pSILAC experiment was performed in singlet with respect to external time for the RAIN analysis, but is duplicate for the two-way ANOVA that is also reported, by treating each cycle as a separate replicate. In fact, the 6.2% of proteins that were significantly rhythmically abundant by RAIN actually agree well with two previous experiments we performed using mouse fibroblasts under identical conditions: the first with 3h resolution over 3 cycles in singlet (7% rhythmic), the second with 4 biological independent replicates over one cycle (8% rhythmic) (Wong et al., EMBO J, 2021). The curve fits shown in 2C are the standard damped sine wave fits, with p-values from RAIN reported in the figure legend.­­

Most importantly however, and as noted in the text, the absolute % of rhythmically abundant proteins is rather irrelevant and indeed the absolute numbers of 'rhythmic' proteins can vary wildly, dependent on the analysis method and stringency. The only important point to be gleaned from the estimates shown in Figure 2e is that by either statistical test, most rhythmically abundant proteins are not rhythmically synthesised, and vice versa; however, the % of proteins that are both rhythmically synthesised and rhythmically abundant is 6 to 11--fold higher than would be expected by chance (taking proteins rhythmic by RAIN and ANOVA, respectively; in both cases the overlap between the two sets is highly significant) . This serves as a positive control, i.e., a minority of proteins show correlated rhythms of synthesis and abundance that are consistent with the canonical activity of 'clock-controlled genes' which cannot be explained by overestimation of rhythmicity.

Odds Ratio comparison synthesis vs total

Synthesis rhythmic by RAIN - listA size=148, e.g. A8Y5H7, B2RUR8, E9Q4N7

Total rhythmic by RAIN - listB size=149, e.g. A1A5B6, A2A6T1, A2AI08

Intersection size=34, e.g. A8Y5H7, O08795, O54910

Union size=263, e.g. A8Y5H7, B2RUR8, E9Q4N7

Genome size=2528

Contingency Table:

notA inA

notB 2265 114

inB 115 34

Overlapping p-value=5.4e-13

Odds ratio=5.9

Overlap tested using Fisher's exact test (alternative=greater)

Jaccard Index=0.1

Synthesis rhythmic by ANOVA - listA size=66, e.g. A8Y5H7, O35639, O55143

Total rhythmic by ANOVA - listB size=83, e.g. A8Y5H7, B2RQC6, E9Q6J5

Intersection size=16, e.g. A8Y5H7, P22561-2, Q3TB82

Union size=133, e.g. A8Y5H7, O35639, O55143

Genome size=2528

Contingency Table:

notA inA

notB 2395 50

inB 67 16

Overlapping p-value=9.7e-11

Odds ratio=11.4

Overlap tested using Fisher's exact test (alternative=greater)

Jaccard Index=0.1

Nevertheless, we agree with the reviewer's general point and have revised the text as follows:

Page 9: "... and may be susceptible to overestimation of rhythmicity."

Page 9: "Consistent with similar previous studies, Page 9: "The proportion of such proteins was more than expected by chance (pMethods, Page 21: "...(n=1 per timepoint)"

* 6) Why were the genes selected in 2C? these are not discussed anywhere else in the manuscript.*

These are simply illustrative examples so that the reader can better understand what we mean, i.e., two proteins in different phases and one that did not change, all within a similar range of abundance. The selected proteins were not discussed because we do not expect the reader to attach any specific meaning to them. We have revised the figure to include in 2C examples of each rhythmicity category shown in 2E. To make this clear, we now state the following:

Figure 2 legend: "No specific meaning is inferred from the protein identities”.

• 7) The authors note that for Figure 2 "These observations are consistent with widespread rhythmic regulation of protein degradation." However, only 5-10% of the proteome is oscillating at any level and less with a discrepancy between synthesis and abundance, so "widespread" is an exaggeration and this statement should be limited to the degradation in the rhythmic proteome. *

We take the reviewer's point, but the term rhythmic proteome is also inaccurate since half the proteins with rhythmic degradation did not show an abundance rhythm in both mass spec experiments. We therefore revised this sentence as follows:

Page 10: "These observations are consistent with widespread temporal organisation of protein degradation within the circadian-regulated proteome."

* 8) The authors note that their more developed strategy in figure 3 would allow for the detection of less abundant proteins. However, they do not discuss that they in fact found less proteins overall, or if they were able to detect proteins of lower abundance. This is of some concern in determining if this is indeed the better method that they predict. How can the authors reconcile this issue? How can they rationalize this explains their increase in oscillating elements? *

Thank you for raising this point, we did not explain ourselves sufficiently clearly. As stated in the revised text, once we had analysed the first iteration of pSILAC (Fig 2), we realised that detection of heavy-labelled proteins was "inevitably limited and biased the proteome coverage towards abundant proteins with higher synthesis rates". In other words, in order to be considered in our analysis both unlabelled and heavy-labelled peptides needed to be detected in every sample at every time point. In fact, if we do not consider heavy-labelling, the overall coverage in the Fig 3 experiment (6577 proteins) was better than the Figure 2 experiment (6264 proteins), as expected, due to technical improvements in the methods used (by the time of the experiment in Fig. 3, we were able to perform the analysis using mass spectrometry techniques with better fractionation and detection, namely FAIMS and MS3). When the analysis criteria are applied however, this falls to 2302 and 2528 proteins, respectively. Because of the way that mass spectrometry works, many proteins needed to be excluded from analysis because the heavy label wasn't detected in one or more samples. In these cases, we cannot infer that no heavy-labelled protein was present in that sample or even that it was present at lower levels than other samples - it simply wasn't detected and therefore we cannot make any quantitative comparisons. Non-detection of any given heavy peptide may occur for several reasons, the most likely being that it co-elutes from the chromatography column at the same time as other much more abundant (light) peptides and simply escapes detection. This is an unavoidable limitation of the technique, we hope the reviewer can understand our need to restrict the analysis to those proteins whose nascent synthesis, and total abundance in the MMC fraction, can be confidently quantified.

As the experiments in Fig 2 and Fig 3 were performed independently, with separate TMT sets and different instrumentation, we are also unable to compare absolute abundances of the proteins between the two.

To communicate this more clearly we have amended Figures 2e and 3e to state the total coverage in the legends, as well as clearly stating the coverage of heavy-labelled proteins in the figure itself. We have also added the following explanation to the text:

Page 11:

“Despite enriching for only one cellular compartment, the overall coverage in this experiment was similar to the previous one (6577 and 6264 proteins, respectively), due to the altered and more targeted approach; with heavy peptides detected for 2302 proteins."

*9) In the comparison of complex turnover rates, the authors need to provide a metric that backs their statement that "the majority of component subunits not only showed similar average heavy to total protein ratios but also a similar change in synthesis over the daily cycle" for figure 3F. *

Our apologies for this oversight, this is now presented in new Fig S3D.

* 10) In reference to the AHA incorporation, why is the hypothesis not that, like the puramycin, you would not see oscillation unless you add BTZ? Shouldn't the active degradation regulate the incorporation of AHA such that there is no visible rhythm unless you suppress degradation? *

AHA is a methionine analogue that is sparsely incorporated into polypeptide chains with minimal effect on protein function/structure (Dietrich et al., PNAS, 2006). Unlike puromycin, therefore, AHA does not lead to chain termination or protein misfolding/degradation (Dermit et al., Mol Biosyst, 2017) and so pulsed application at different phases of the circadian cycle is sufficient to reveal protein synthesis rhythms. The novelty in Fig 3H is the combination of AHA labelling with native PAGE that allows us to validate rhythmic production of high molecular weight protein complexes. This would not be possible with puromycin because prematurely-terminated polypeptide chains are not able to assemble into native complexes unless chain termination happens to occur at the extreme C-terminus and the C-terminus does not partake in any intermolecular interactions within the assembled complex.

* 11) The authors claim that there is enrichment of the actin cytoskeleton, but where this data can be found should be explained. The only thing that is shown is a few selected graphs of proteins in this pathway. *

We previously reported circadian regulation of the actin cytoskeleton in Hoyle et al. (Sci Trans Med, 2017). The extremely high relative amplitude of Beta-actin (the structural component of microfilaments) in the MMC fraction is, in and of itself, entirely sufficient to demonstrate a circadian rhythm in the relative ratio of globular to filamentous actin that was originally identified by Ueli Schibler's lab (Gerber et al., Cell, 2013) and then shown to have a cell-autonomous basis in fibroblasts in Hoyle et al (2017). We have included further examples of an actin-binding protein (Corinin1b) and a motor protein (Myosin 6) to further illustrate this, but do not feel further discussion is warranted because it was comprehensively addressed in our previous work. The enrichment for actin was determined by GO analysis, which is now shown in the Fig 4A and referred to in the text.

The important point in Fig 4C is the difference in phase with the examples shown in Fig 4B and summarised in Figure 4A, i.e., there are a small number of proteins whose presence in the MMC fraction is highest in advance of the majority of rhythmically abundant proteins, but this earlier group doesn't show any significant synthesis rhythm. Actin is one of the most abundant cellular proteins, and by mass it accounts for 67% of the circadian variation of rhythmically abundant proteins that peak in this fraction at the same phase. All these data and analyses are available for scrutiny in Supplementary Table 2.

To communicate this more clearly we have expanded on this point as follows:

Page 13: " These proteins were enriched by 9-fold for actin and associated regulators of the actin cytoskeleton (q* 12) The authors note an oscillation in the total levels of p-eif2, commenting that these do not arise from the rhythms in total eif2a but temperature and feeding rhythms. However, unless I misunderstood, this work was done in fibroblast cell culture, so in this case, where would these temperature and feeding rhythms come from? *

We were insufficiently clear. Daily rhythms of p-eIF2 have been observed under physiological conditions in mouse, in vivo. We do not observe similar rhythms in cultured fibroblasts under constant conditions unless the cells are challenged by stress. By inference therefore, it seems likely that daily rhythms of p-eIF2 in vivo arise from the interaction between cell-autonomous mechanisms and daily systemic cues such as, insulin/IGF-1 signalling and body temperature that are in turn driven by daily rhythms in CNS control, daily feed/fast rhythms and daily rest/activity rhythms, respectively. We have amended the text as follows:

Page 15: "...and so suggest that daily p-eIF2α rhythms in mouse tissues likely arise through the interaction between cell-autonomous mechanisms and daily cycles of systemic cues, e.g., insulin/IGF-1 signalling and body temperature rhythms driven by daily feed/fast and rest/activity cycles, respectively."

* 13) In Figure 5d, the treatment impeding degradation is causing cell death while the inhibition of translation does not. However, wouldn't too much, or not enough, translation, without compensatory regulation from degradation cause a problem in the same way that degradation does? *

It is well-established that acute treatment with high concentrations of proteasomal inhibitors rapidly leads to proteotoxic stress that will trigger apoptosis unless resolved (Dantuma and Lindsten, Cardiovasc Res, 2010). Treatment with CHX is certainly stressful to cells, but in a different way, and cells die through mechanisms generally regarded to be necrotic and certainly do not involve the canonical proteotoxic stress responses that are activated by MG132 and similar drugs. Our findings show that, by whatever mechanisms cells die with CHX treatment, it does not change over the circadian cycle whereas death via proteotoxic stress does, consistent with our prediction. We hope the reviewer agrees it is beyond the scope of our study to explain why CHX-mediated cell death does not show a circadian rhythm in mouse fibroblasts.

*Reviewer #1 (Significance (Required)):

*The information that stems from this work is relevant and of interest to circadian clock field as how the regulation of the output of the circadian clock is implemented is still a major question in the field. This manuscript suggests a novel and plausible method for how, at least in part, this regulation occurs. However, the manuscript uses methods that do not measure degradation directly, which is a minor limitation. In addition, the mechanisms by which this regulation is imparted are not addressed in any meaningful way, even in the discussion.

We are sorry that we did not adequately discuss the extensive previous work that has already addressed regulatory mechanisms. We would like to stress that this manuscript concerns protein turnover and proteome renewal, of which degradation is obviously an important part but not the sole focus.

To communicate this more clearly, we have amended the title to:

"Circadian regulation of macromolecular complex turnover and proteome renewal"

... which we previously explicitly predicted in the discussion of previous papers (Feeney et al., Nature, 2016; O'Neill et al., Nat Comms, 2020; Wong et al., EMBO J, 2022) and our recent review (Stangherlin et al., Curr Opin Syst Biol, 2021).

With respect to measurement of degradation - Physiologically, cellular rates of proteasomal degradation are so intimately coupled with protein synthesis that, over circadian timescales, the former cannot meaningfully be studied in isolation. It is possible that the reviewer is alluding to historical methods that measure change over time in the presence of translational or proteasomal inhibitors, but these have long been known to introduce artifacts - because translational inhibition rapidly leads to reduced proteasome activity, whereas proteasomal inhibition rapidly reduces protein synthesis rates through the integrated stress response. We would be interested to hear of any more direct method for measuring protein degradation proteome-wide than the pulsed SILAC method we developed, as we are not aware of any. Even proteasomal proximity labelling coupled with MG132 treatment, recently developed by the Ori lab, does not directly measure degradation (bioarxiv https://www.biorxiv.org/content/10.1101/2022.08.09.503299v1). By definition, degradation can only be measured through the disappearance of something that was previously present, usually by comparing its rate of production with the change in steady state concentration (if any), which we have done using multiple methods.

With respect to regulation of degradation - We speculated on the mechanisms regulating rhythms in protein turnover in our several previous papers (Feeney et al., Nature, 2016; O'Neill et al., Nat Comms, 2020; Wong et al., EMBO J, 2021; Stangherlin et al, Nat Comms, 2021), whereas outside the circadian field these mechanisms have been addressed extensively. This was also discussed in detail in our recent review on the topic (see Stangherlin et al., COISB, 2021). In this review, we lay out the evidence for a model whereby most aspects of circadian cellular physiology might be explained by daily rhythms in the activity of mammalian target-of-rapamycin complexes (mTORC). This model makes multiple predictions and informs the central hypothesis which is tested in the current manuscript: that circadian rhythms in complex turnover and proteome renewal should be prevalent over abundance rhythms. An enormous body of work over the last two decades has already clearly established mTORC1 as the master regulator of bulk protein synthesis and degradation, and a substantial number of independent observations have demonstrated circadian regulation of mTORC1 activity in vivo and in cultured cells. The mechanisms that drive cell-autonomous mTORC1 signalling are only partially understood (e.g. Feeney et al., Nature, 2016; Wu et al., Cell Metab, 2019), and we continue to explore this experimentally but they certainly lie well beyond the scope of this investigation.

Therefore, to address the reviewer's concern about inadequate discussion of mechanism, we have expanded on mTORC in the introduction and discussion, as follows:

Page 3: "Daily rhythms of PERIOD and mTORC activity facilitate daily rhythms of gene expression and protein synthesis. In particular, mTORC1 is a master regulator of bulk 5'-cap-dependent protein synthesis, degradation and ribosome biogenesis (Valvezan & Manning, 2019) whose activity is circadian-regulated in tissues and in cultured cells (Ramanathan et al, 2018; Feeney et al, 2016a; Stangherlin et al, 2021b; Mauvoisin et al, 2014; Jouffe et al, 2013; Sinturel et al, 2017; Cao, 2018). It is plausible that daily rhythms of mTORC activity underlie many aspects of daily physiology (Crosby et al, 2019; Stangherlin et al, 2021a; Beale et al, 2023b)."

Page 17: "The mechanistic underpinnings for cell-autonomous circadian regulation of the translation and degradation machineries remain to be fully explored, but are likely to be driven by daily rhythms in the activity of mTORC: a key regulator of protein synthesis and degradation as well as macromolecular crowding and sequestration (Stangherlin et al, 2021b, 2021a; Cao, 2018; Adegoke et al, 2019; Ben-Sahra & Manning, 2017; Delarue et al, 2018). In particular, global protein synthesis rates are greatest when mTORC1 activity is highest, in tissues and cultured cells, whereas pharmacological treatments that inhibit mTORC1 activity reduce daily variation in crowding and protein synthesis rates (Feeney et al, 2016a; Lipton et al, 2015; Stangherlin et al, 2021b). Given our focus on proteomic flux and translation-associated protein quality control, autophagy was not directly within the scope of this study but is also mTORC-regulated and subject to daily regulation (Ma et al, 2011; Ryzhikov et al, 2019). In vivo, daily regulation of mTORC activity arises primarily through growth factor signalling associated with daily feed/fast cycles (Crosby et al, 2019; Byles et al, 2021). The mechanisms facilitating cell-autonomous circadian mTORC activity rhythms are incompletely understood but may include Mg.ATP availability (Feeney et al, 2016a) and its direct regulation by PERIOD2 (Wu et al, 2019). This will be an important area for future work."

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

Summary: This is a very interesting and well written paper that addresses key questions in the circadian organization of proteostasis. The paper investigates origins of cellular circadian rhythms, invoking a premise early that there is a poor correlation between rhythmic gene expression - regulated by the canonical TTFL - and rhythms of the proteome, which are rather meager. Specifically, they ask how a relatively stable proteome is possible if cells engage in rhythms of cellular protein synthesis? Their hypothesis is that protein degradation must rhythmically compensate for rhythms of synthesis and much of the manuscript is focused on defining the relationship between rhythmic global synthesis and rhythmic degradation. They employ a series of detailed proteomic investigations and biochemical assessments of protein synthesis coupled with various circadian reporters to assess proteosome function. The proteomic experiments reveal a limited number of proteins with oscillations in either synthesis or abundance or both and no discernible pathway organization however, a followup and more refined study that utilized fractionated samples and boosted heavy SILAC identified strikingly, that many proteins in relatively heavy fractions are rhythmic and that these fall into possible complexes including ribosome and chaperonins. Finally, they perform in vivo experiments testing whether the timing of proteotoxic stimuli regulates the degree of the integrated stress response measured as pEif2a. Overall, I think that this is a fascinating paper that addresses and important question but falls short on mechanistically unifying them and completely contextualizing the findings in light of the canonical modes of circadian timekeeping leaving us with an important, but mostly descriptive set of findings. In addition, there are a number of important questions about data interpretation, some issues with data quality that should be addressed outlined below. With revision and further explication, this study will be an excellent addition to the growing field of circadian organization of the cellular proteome. *

Thank you for reading and appreciating our work

*Major and minor Comments. Figure 1. Fig 1a. The difference in Pulse and Chase at ZT24 does not appear to reflect the quantified data in 1b. This should be reconciled to make the figure convincing. *

When working with radioactive cell lysates it is not possible to equalise the level of protein loaded on each gel beforehand as would happen with a western blot, for example. For this reason, the radioactive signal was normalised to the protein level subsequently measured by coomassie staining, as is standard practise for this type of assay, with all 4 replicates being shown in supplementary Fig.1A. An overnight phosphor screen image is presented in the main Fig.1A for illustrative purposes, but we take the point that this might not be immediately obvious. In revised Fig 1A we therefore now also show the relevant coomassie as well as labelling to make clear that the radioactive signal was normalised to protein levels.

* How was the timing of the chase collection determined? *

For these proof-of-principle experiments, we empirically determined the minimum duration of pulse and chase necessary to detect a quantifiable signal.

*Fig 1d-e. What is the evidence that puro labeling results in 'rapid' turnover. *

Apologies, this has been established for some time. Some additional papers are now cited in this section of the text (Liu et al, PNAS, 2012; Lacsina et al., PLoS One, 2011; Szeto et al., Autophagy, 2006)

*Fig 1e seems to be missing the data from the treated and untreated conditions? How are the lines produced (e.g. linear versus rhythmic? Are these drawn lines or actual regressions?). *

Fig 1e depicts the result of the experiment schematically explained in 1d. The only conditions were +Puro or +Puro+BTZ. There was no completely untreated condition, as puromycin incorporation is the basis of the assay (Lacsina et al., PLoS One, 2012; Szeto et al., Autophagy, 2006) and puromycin does not occur naturally in cells. We realise the figure could potentially be confusing without the associated raw data (anti-puromycin blots) - these are shown in supplementary Fig. 2A.

To explain the method more clearly, the following has been added to the results section where this experiment is described:

" As determined by anti-puromycin western blots, over two days under constant conditions, puromycin incorporation in the presence of BTZ showed significant circadian variation. In contrast, cells that were treated with puromycin alone showed no such variation, and nor did total cellular protein levels (Fig 1E, Fig S2A).”

The fit lines are produced by statistical comparison of fits, i.e., our hypothesis (damped cosine fit) vs null hypothesis (no or constant change over time, linear fit, y = mx+c), using sum-of-squares F test. The statistically preferred fit is plotted and p-value displayed on the graph, i.e., the regression line of the preferred fit and parameters are plotted. These details are reported in the figure legends.

* Why was 30 minutes chosen as labeling time? It seems hard to understand here how protein degradation kinetics can be measured by puromycin labeling if the authors' claim that puromycin labeling potentially changes degradation rates as a function - primary or secondary - of the labeling itself. It seems they are measuring the potential to degrade proteins. *

Puromycin labelling is a 20 year-old widely-used technique that can be employed in a range of applications. It was first used in a circadian context by Lipton et al (Cell, 2015) whose work we quickly followed (Feeney et al, Nature, 2016). Briefly, puromycin mimics tyrosyl-tRNA to block translation by labelling and releasing elongating polypeptide chains from translating ribosomes. When used at low concentrations (1 ug/mL in this case) puromycin is sparsely and sporadically incorporated into a small minority of elongating polypeptide chains. Those prematurely terminated chains have puromycin at the C-terminus, which can be detected by western blotting. We chose 30 minutes after optimisation experiments, as it was the shortest incubation time where a robust signal could be observed in these cells with this concentration of puromycin. The puromycinylated peptides are preferentially degraded by the ubiquitin-proteasome system because they are efficiently recognised as misfolded/aberrant proteins by chaperones within tens of minutes of being translated. Unless used at much higher concentrations, or over much longer timescales, there is no reason to believe that puromycin affects the degradation machinery itself, but the degradation of puromycinylated peptides depends on the proteasome. Therefore, puromycin+a proteasome inhibitor provides a reliable proxy for translation rate in the preceding 30 minutes, whereas puromycin alone tells us the steady state concentration under normal conditions, i.e., where proteasomes remain active. By subtracting the latter from the former we can infer the level of degradation of puromycinylated peptides that must have occurred in the previous 30 minutes. It is not a perfect technique, but its results agree with other findings in this manuscript: that protein turnover varies more than steady state protein abundance. With respect to the potential to degrade proteins, this is measured in Fig 1C.

* How do they determine that they are measuring degradation of functionally relevant proteins as opposed to a host of premature truncations? *

We do not. This is measured by stable isotope labelling in Figures 2-4. Figure 1 provides the rationale for what follows in subsequent figures, i.e., proof-principle experiments suggesting that turnover is not constant over the circadian cycle. No single experiment in Figure 1 is expected to convince the reader that of circadian turnover. Rather, several independent methods suggest that bulk protein synthesis and degradation (turnover) are not constant over time, and deviate from the null hypothesis with variation that appears to change over the 24h circadian cycle.

* Fig 1e bottom - again is this a true regression line? *

It is not a regression line, otherwise a p-value of fit would be shown. Fig1e bottom shows the bioluminescence measured at each timepoint from parallel control cultures (average of triplicates, error bars shown as dotted lines). Due to very high temporal resolution (every 30 min) and robustness of the cell line, it appears as a virtually perfect damped (co)sine wave. We apologise that this was not explained more clearly in the figure legend, now amended as follows:

"Parallel PER2::LUC bioluminescence recording from replicate cell cultures (mean +/- SEM, every 30 min) is shown below, acting as phase marker."

*Perhaps two time points should be examined here - similar to the pulse chase performed with 35S labeling? *

We are sorry we were not fully clear with our method here. The puromycin (+/- BTZ) labelling was performed over two days every 4h (so 12 timepoints in total), which can be inferred from the data points in the top two graphs in Fig. 1E, and x-axis - but is now also clearly stated in the figure legend. The bottom right graph was a continuous bioluminescence recording, integrated every 30 min from the set of parallel culture dishes. The bioluminescence data serves as a circadian phase marker, so that we can infer at which biological times synthesis and inferred turnover was higher vs lower.

We’ve adjusted the text to explain our method more clearly:

“Acute (30 min) puromycin treatment of cells in culture, with or without proteasomal inhibition (by bortezomib, BTZ), allowed us to measure both total nascent polypeptide production (+BTZ) and the amount of nascent polypeptides remaining when the UPS remained active (-BTZ). This allowed inference of the level of UPS-mediated degradation of puromycylated peptides within each time window, as a proxy for nascent protein turnover (Fig. 1D).”

* Fig 1f. It appears that Puro labeling results in a rhythm between ZT1 and ZT13 but no statistic is provided and appears that the 'ns' is the results of variance in the data as opposed to difference in means? - would this not contradict the cellular result? What accounts for the rhythm reversal in the presence/absence of BTZ. *

To be clear, we measured the level of puromycin incorporation in mouse liver in vivo following a similar method employed by Lipton et al, Cell, 2015 (Figure 2). The prediction was that, exactly as in cells (Fig 1E), treatment with a proteasome inhibitor would lead to a much greater increase in puromycinylated peptides at ZT13 than ZT1, because this is when protein synthesis is known to be higher and thus (we predict) protein degradation should also be higher. The experiment was not designed or powered to detect a time effect, it was designed to detect an interaction between time-of-puromycin treatment and BTZ, with the specific prediction being that BTZ would have a greater effect during the active phase. This is what we observed.

* While the authors have previously demonstrated an increase in rhythmicity of the proteome in Cry1/Cry2 double knockout cells, it would have been welcome here to test a global loss of circadian transcription in the degradation assay. One might expect that these rhythms would also be even higher. What I am really asking is: what is the mechanism for rhythmic degradation and is it dependent on the canonical clock? *

To address the reviewer's curiosity, we used the proteasome-Glo assay (also used in Fig 1C) to assess whether there was an interaction between genotype (WT vs CKO) and time at opposite phases of the circadian cycle over 2 days. We found a significant interaction by two-way ANOVA, indicating that components of the 'canonical clock' regulate the temporal organisation of proteasomal activity (see revised Figure S1). Circadian regulation of mammalian cellular functions, such as protein turnover, is a complex and dynamic process, whereas gene deletion affects the steady state and may be epistatic to phenotype rather than revealing gene function. We are therefore reluctant to speculate what this result means in the present manuscript, which is focused entirely on testing the hypothesis that global protein turnover and complex biogenesis have cell-intrinsic circadian rhythms in non-stressed, wild type cells.

To communicate this, the text has been revised as follows:

"Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-lik proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B-E). "

* **Fig 2. How was the 'fixed window' timeframe determined? *

A trial experiment was performed with labelling windows of various length, and 6h was determined to be the shortest window where enough heavy label incorporation was detected to be able to assess circadian changes. This was the case with our first methodology, which was subsequently improved (Figure 3), and therefore labelling window reduced to 1.5h.

* *Fig 3h. While admittedly difficult, the native PAGE is not of great quality and kind of unconvincing. Also not really sure why the AHA labeling is used here an nowhere else in the paper.

AHA is a methionine analogue that is sparsely incorporated into polypeptide chains with minimal effect on protein function/structure (Dietrich et al., PNAS, 2006). Unlike puromycin, therefore, AHA does not lead to chain termination or protein misfolding/degradation (Dermit et al., Mol Biosyst, 2017). In Figure 1, the aim was to validate previous reports of rhythmic protein synthesis assess whether there was any evidence for rhythmic turnover. To this end, we employed two independent methods (35S-labelling and puromycin-incorporation). We did not want to rely on AHA for measuring turnover: although it has been validated and used for this purpose in some studies (McShane et al., Cell, 2016), AHA is not fully equivalent to methionine, and cellular aminoacyl-tRNA synthetases have much higher affinity to methionine than they do to AHA (Ma and Yates, Expert Rev Proteomics, 2018). It is thus impossible to perform AHA labelling without methionine-free medium, and in turn methionine starvation and media changes are known to have an effect on cell signalling and cell metabolism, which would be particularly pronounced in circadian context (over days rather than over hours).

By contrast, in Fig 3H, we use AHA with native PAGE to specifically validate one inference from the mass spectrometry analyses: circadian production of high molecular weight protein complexes. This would not be possible with puromycin because prematurely terminated polypeptide chains are not able to assemble into native complexes unless chain termination happens to occur at the extreme C-terminus and the C-terminus does not partake in any intermolecular interactions within the assembled complex.

The raw data (full gels, all replicates) are presented in Figure S2e, which of course was used for quantification. We have now picked a different example for the main figure, which hopefully allows for clearer representation.

The text in the results section describing the AHA experiment is now amended as follows:

" To validate these observations by an orthogonal method, we pulse-labelled cells with methionine analogue L-azidohomoalanine (Dieterich et al, 2006). AHA is an exogenous substrate, that cells have lower affinity to than methionine, and it could potentially impact on stability of the labelled proteins (Ma & Yates, 2018) – therefore, we only used AHA to assess nascent complex synthesis, rather than turnover. We analysed the incorporation of the newly synthesised, AHA labelled proteins into highest molecular weight protein species detected under native-PAGE conditions (Fig 3H, S3F). We observed a high amplitude daily rhythm of AHA labelling, indicating the rhythmic translation and assembly of nascent protein complexes. Taken together, these results show that daily rhythms in synthesis and degradation may be particularly pertinent for subunits of macromolecular protein complexes"

Fig 4. I was a little disappointed here that the authors did not directly assess macromolecular assembly of at least one of their "hits" and demonstrate functional relevance and most of the analysis is maintained at a very superficial, systemic level. STRING assemblies are not terribly helpful without clear k-means clustering or some other clearly visualizable metric for stratifying and organizing the putative PPI data - this figure (S3) could be markedly improved.

We agree that validation is important. The ribosome is by far the most abundant macromolecular complex in the cell, and was one of the major complexes to show clear evidence for circadian regulation of turnover, but not abundance, by our pSILAC proteomics. To validate this result, we took advantage of two important observations: (1) that all fully assembled ribosomes incorporate ribosomal RNA (rRNA) which can readily be separated from other cellular RNA by density gradient centrifugation; (2) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Thus, combining stable isotope labelling with ribosome purification, we can distinguish nascently assembled ribosomes from total when the RNA is extracted, digested with RNAse, and the % heavy/total UMP quantified by mass spectrometry. These data are presented in new figure 5, and are consistent with findings in Figures 3/4 that circadian regulation of ribosome turnover is prevalent over abundance, and that the phase of highest ribosome turnover coincides with the phases of high translation and turnover overall. We hope by addressing the reviewer's question by an entirely orthogonal method, they can share more confidence in our conclusions.

The statistical metric for STRING, specifically the p-value for enrichment in physical protein-protein interactions, is presented in the main Fig. 3G. It is now also reported in the legend for new Figure S4 itself.

* Is it possible that some macromolecular complexes have rhythms because their constituent proteins have differential half-lives when in one complex compared with another in circadian time? This possibility was not discussed. *

To our knowledge, there is no evidence that any major macromolecular complex in the cell has a functionally significant rhythm in abundance on a cell-autonomous basis. The reviewer’s suggestion is an intriguing possibility, but we can think of no way that it could be measured, even in principle. The simplest interpretation of our data from the independent techniques we employ (pSILAC with fractionation, native PAGE + AHA incorporation) is a rhythm in synthesis.

*Fig. 5. Why is the first histogram in 3c not at unity? *

This measures the average fold-induction in aggregation when cells are treated with MG132 for 4h at the indicated timepoints. Unity would indicate no induction at all, so the presented quantifications show that MG132 always elicited an increase in aggregation, with an effect size that varied with circadian phase.

* Do ZT24 and ZT48 differ, similarly do ZT36 and ZT60?*

No, neither difference is statistically significant (adjusted p-values of p=0.9 and p=0.07, respectively). This is now specified in the figure legend. Tendency to aggregate is also likely to change as a function of time in culture, which is why we think there is a slight increase overall in the second day of the experiment.

* Fig S4f is not of good quality with missing eIF2a total and therefore no loading controls. *

Thank you for prompting us to double-check this. We found that the levels of eIF2a were quite variable between the animals, and therefore we performed this experiment with 6 biological replicates. We have double-checked the quantification, and have now excluded 3 unreliable samples (the ones with undetectable levels of total eIF2a – ZT18 +BTZ replicate 1 & ZT18 -BTZ replicate 2, as well as ZT6 +BTZ replicate 4, where a smear does not allow for a reliable quantification of phospho-eIF2a) instead of 2 that were excluded originally. This still leaves at least 5 biological replicates in each group. In fact, the difference between BTZ and control in ZT6 is now deemed to be even more significant, going down to adjusted p=0.0007.

*S4e? true regression lines? *

The same method was used as in Figure 1. The fit lines are produced by statistical comparison of fits, i.e. our hypothesis (damped cosine fit) vs null hypothesis (no change over time, linear fit), using sum-of-squares F test. The statistically preferred fit is plotted and p-value displayed on the graph. These details are reported in the figure legends and methods section.

While I thought these experiments were effective, they did not tie back well to the rest of the paper. What are the consequences of a temporally sensitive ISR? Which pathways does it effect in circadian time? Here, the main holes in this study are somewhat exposed; namely, a lack of mechanistic depth in explaining the very fascinating, albeit mostly descriptive, findings. The implicit assumption made here is that aggregation is 'bad' but could the opposite be just as true? Taking these considerations in account would further strengthen the discussion.

The purpose of (former) Fig 5 was entirely to test the functional consequences and potential translational relevance of a daily rhythm in protein turnover. The mechanisms upstream and downstream of the ISR, and link with many diseases, are already quite well understood but we apologise that we did not draw more heavily on the prior literature to provide sufficient context for this experiment. Protein aggregation has long been associated with proteotoxic stress, and we do not assume it is good or bad, we simply use it as an additional validation of a temporally sensitive ISR. To correct this omission we have added the following to the results section before these experiments are introduced:

"Disruption of proteostasis and sensitivity to proteotoxic stress are strongly linked with a wide range of diseases (Wolff et al, 2014; Harper & Bennett, 2016; Labbadia & Morimoto, 2015; Hipp et al, 2019). Evidently, global protein translation, degradation and complex assembly are crucial processes for cellular proteostasis in general, so cyclic variation in these processes would be expected to have (patho)physiological consequences....

...Informed by our observations, we predicted that circadian rhythms of global protein turnover would have functional consequences for maintenance of proteostasis. Specifically, we expected that cells would be differentially sensitive to perturbation of proteostasis induced by proteasomal inhibition using small molecules such as MG132 and BTZ, depending on time-of-day."

Reviewer #2 (Significance (Required)):

This is a fascinating paper that addresses key questions in the circadian organization of the proteome. The paper's main findings are that rhythms of protein synthesis and degradation are temporally coordinated to maintain overall stability of the proteome in mouse fibroblasts. Furthermore, the authors present evidence that this temporal organization may be important for assembly of macromolecular complexes. While very interesting, the main limitations are a lack of biochemical and mechanistic explanation and evidence that verifies these, mostly descriptive, findings.

The fundamental biochemical mechanisms of protein synthesis, degradation, protein quality control and stress response have been studied for decades and are increasingly well understood, at least in cultured cancer cells. What is not understood is the extent to which all of these essential cellular systems are subject to physiological variation over the circadian cycle in quiescent cells. This is the fundamental knowledge gap our study attempts to fill by testing the discrete hypotheses that (1) circadian regulation of macromolecular complex turnover is more prevalent than abundance and that (2) proteome renewal is more prevalent than compositional variation. We suggest that establishing these essential principles of circadian cellular physiology is an essential prerequisite for performing the type perturbational experiments we presume the reviewer would prefer. We would like to reassure the reviewer that such studies have been and are being performed, but we are concerned that the inclusion of a very extensive additional body of work within this manuscript would detract from the clear communication of our major finding that complex turnover and proteome renewal has a cell-autonomous basis.

*There are some relatively minor statistical and data quality issues that are probably addressable relatively quickly.

**Upon revision the study would be a welcome addition to investigators interested in proteostasis, circadian biology, cell biology and proteomics.

**I am a physician-scientist with expertise in circadian rhythms, cell biology, protein synthesis, and biochemistry.

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

**Seinkmane et al investigate circadian regulation of protein synthesis and degradation in cultured cells and in mice. Their main new finding is that protein synthesis and degradation are in many cases rhythmic but coordinated such that the proteome is rhythmically renewed without an apparent rhythm in total protein abundance. Particularly the pool of large protein complexes is rhythmically renewed in this fashion.

Using pulsed SILAC in combination with mass spectrometry, the authors are able to distinguish between total and newly synthesized protein levels in mouse lung fibroblasts. Analysis of these data shows that the synthesis of a large number of proteins is rhythmic although the total amount is constant, or that proteins are synthesized at a constant rate but the total amount is rhythmic, suggesting that degradation is rhythmic. By analyzing macromolecular complexes, defined as a high-speed pellet, they also present evidence that the rhythmic components of large complexes oscillate in the same phase and have a similar protein turnover rate. The authors conclude that complexes assemble rhythmically. **The authors also present evidence that the activity of the proteasome oscillates in a circadian manner. Based on this observation, they show (in fibroblasts and in mice) that the response to proteotoxic stress (monitored by eIF2alpha phosphorylation levels, protein aggregation, and apoptosis) is higher at circadian times of high proteasome activity.

**I am an expert in the circadian field, and the hypothesis and concept behind the work presented here are potentially very interesting, and the experimental design is in principle suitable to answer these questions. However, after reading the paper several times, I cannot find the set of experiments that would convincingly support the authors' conclusions.

**Major questions/points:

*The major limitation of the manuscript is that the conclusions rely heavily on statistical analysis and massive processing of data from a bewilderingly large number of very different experiments. In looking at the figures, I have often wondered if the presence or absence of a rhythm is real or a product of the heavily processed data. The fact that a cosine wave fits through data points better than a straight line does not necessarily mean that a circadian rhythm is present.

We agree that comparison of fits alone does not provide sufficiently reliable evidence. However, the fact that many independent methods (cosinor, RAIN, ANOVA) yield similar overall findings lends more confidence to our findings. We would also argue that the large number of different experiments is a positive aspect of the paper and lends weight to the general conclusions. We instead ask the reviewer to consider an alternative question - we and many other labs have found no evidence for any change in total cellular protein content, and yet there is extensive evidence from independent labs for a 'translational rush hour' whilst (excepting some low abundance transcription factors) very few cellular proteins change by more than 10% over the circadian cycle (see Stangherlin et al, COISB, 2022 for extended discussion of this). We hypothesised a parsimonious explanation for this clear contradiction, and designed experiments whose data were analysed by widely used methods that yielded results that were consistent with prediction. Perhaps the reviewer will at least concede that, if the presented findings do not refute the hypothesis, it should not be rejected until a superior one is proposed?

* I think that in particular, the SILAC experiment(s) should be repeated and also performed with an arrhythmic control (such as CRY1/2 KO). *

Whilst we agree that CRY1/2 KO cells show no circadian regulation of transcription and much more variable rhythms in PER2::LUC activity than wild type controls (Putker et al., EMBO J, 2021), in our hands circadian rhythms in proteome composition and protein phosphorylation in CRY1/2 KO are at least as prevalent as in wild type cells (see Wong et al., EMBO J, 2022). Indeed, when we performed a proteasome activity assay in CRY1/2 KO fibroblasts, we observed there was an apparent circadian variation, similar to WT but with a different phase. These data are now presented in revised Figure S1. Similarly, Lipton et al (Cell, 2015) showed circadian translational rhythms in cultured Bmal1 KO cells (see final figure), therefore it is not clear what would constitute an appropriate 'arrhythmic' control.

In this study, for proteomics experiments, we used a combination of SILAC and TMT, as each technique alone would not be sufficient to answer our specific questions. These two techniques are very resource-intensive on their own, and even more so in combination. We therefore had to prioritise and for the second SILAC-TMT experiment decided to focus on cellular fractionation and questions pertaining macromolecular complexes, which were directly relevant to our hypothesis. While it would undoubtedly also be interesting to study how canonical clock genes, such as Cry1/2, impact turnover on a proteome-wide scale, the focus of our study is physiological regulation of proteome composition, rather than the function of Cryptochrome genes which we already explored in previous work (Putker et al., EMBO J, 2021; Wong et al., EMBO J, 2022).

Comparability between the whole cell and MMC SILAC experiments is also limited due to the different experimental conditions (6h vs. 1.5h pulse, +booster).

We do not make any direct comparisons, other than to report that broadly comparable numbers of proteins were detected. Implicitly this means there must be greater coverage of protein complexes in the second pSILAC experiment, which our data bears out. If we were not to report the first experiment, the reader would not understand why we refined the method used in the second. In reporting the results of the 6h pulse, we make the limitations of this experiment very clear i.e. biased towards highly abundant, highly turnover proteins, irrespective of cellular compartment. We should add that even in this experiment there was a clear trend towards rhythmic turnover of ribosomal proteins, but this did not quite achieve significance (p = 0.07) and so we did not want to make claims beyond the data.

*The essential and new message of the paper is that (at least some) macromolecular complexes undergo circadian renewal (degradation and synthesis). Rather than just analysing an operationally defined pellet fraction by mass spectrometry, this could be shown in more detail and directly for one or two specific macromolecular complexes. Ribosomes, for example, seem particularly suitable, because there would also be the very simple approach of measuring the synthesis of ribosomal RNA by pulse labelling. To me, such an analysis would be perfectly sufficient as a proof of principle. I would then omit aspects such as rhythmic stress response, since many additional experiments are needed to demonstrate this convincingly. *

Thank you for the excellent suggestion, we agree that validation is important. The ribosome is by far the most abundant macromolecular complex in the cell and was one of the major complexes to show clear evidence for circadian regulation of turnover, but not abundance, by our pSILAC proteomics. To validate this result, we took advantage of two important observations: (1) that all fully assembled ribosomes incorporate ribosomal RNA (rRNA) which can readily be separated from other cellular RNA by density gradient centrifugation; (2) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Thus, combining stable isotope labelling with ribosome purification, we can distinguish nascently assembled ribosomes from total ribosomes when the RNA is extracted, digested with RNAse, and the ratio of light to heavy UMP quantified by mass spectrometry. These data are presented in new figure 5, and are consistent with findings in Figures 3/4 that circadian regulation of ribosome turnover is prevalent over abundance, and that the phase of highest ribosome turnover coincides with the phases of high translation and turnover overall. We hope by addressing the reviewer's question by an entirely orthogonal method, he/she can share more confidence in our conclusions.

The final figure is included because it tests predictions that were informed by the preceding experiments. It is not intended to be comprehensive exploration of how the integrated stress response changes with the circadian cycle, nor have we claimed this.

* Specific points: The reader is strongly influenced by the cosine wave or straight lines in the graphs (e.g. 1c, e, 3h, 5b, etc) produced by the analysis of rhythmicity, which basically only gives a yes or no answer. But it is not really that simple. If the algorithm detects a rhythm what is its period? Is it the same as the period of the luciferase reporter? If the period lengths correlate, do the phases as well (e.g. see differences in phases 1c and e)? These questions are not addressed. *

The temporal resolution of the time course data is much lower than the luciferase reporter and so the error of the fit is greater (usually 1-2h). For the cosine wave curve fit and the associated extra sum-of-squares F test, the period of the oscillation was fixed at either 24h or 25h, as determined from a parallel PER2::LUC control recording. This is now explicitly stated in the methods section

In terms of phase, the general trend across all experiments is that bulk protein turnover, synthesis and degradation is higher during the 6-8h following the peak of PER2::LUC than at any other point in the circadian cycle. This is also consistent with our previous findings in mouse and human cells (Feeney et al, Nature, 2016; Stangherlin et al., Nat Comms, 2021) as well as findings from many different labs in vivo (e.g. Janich et al., Genome Res, 2016; Atger et al., 2015, PNAS; Sinturel et al., 2017, Cell). We are cautious about trying to be any more specific than this because each assay is measuring something different, and (as can be seen across the figures) there is also some modest variation in the phase of PER2::LUC between experiments, with respect the prior entraining temperature cycle (this will be reported in our forthcoming publication, Rzechorzek et al, in prep). To address the reviewer's point therefore, we have added the following to the discussion:

"Across all experiments in this study, we find that protein synthesis, degradation and turnover is highest during the 6-8h that follow maximal production of the clock protein PER2. This is coincident with increased glycolytic flux and respiration (Putker et al, 2018), increased macromolecular crowding in the cytoplasm, decreased intracellular K+ concentration and increased mTORC activity (Feeney et al, 2016a; Stangherlin et al, 2021b; Wong et al, 2022)."

* **The algorithm in Fig 1c predicts a rhythm for the chymotrypsin-like and the trypsin-like but not for the caspase-like activity. The peptide assay measures core proteasome activity independent of ubiquitylation and should therefore be dependent on proteasome concentration in the sample. How can then only two of the three proteasomal activities be rhythmic? Please elaborate and repeat with arrhythmic cells (e.g. CRY1/2 KO). The period length does not seem to correlate with the one of the reporter. Why is that? *

The arrhythmic controls idea is partially addressed in the response above. We did perform a proteasome activity assay in CRY1/2 KO fibroblasts, and observed daily variation similar to WT, albeit with a different apparent phase. These data are now shown in Figure S1, and referred to in the main text as follows:

"Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-like proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B-E)".

Besides this study, our two previous proteomic investigations of the fibroblast circadian proteome detected no biologically significant or consistent rhythm in proteasome subunit abundance (Wong et al., EMBO J, 2021; Hoyle et al., Science Translational Medicine, 2017). Moreover, proteasomes are long-lived stable complexes whose activity is determined by a combination of substrate-level, allosteric and post-translational regulatory mechanisms that includes their reversible sequestration into storage granules (Albert et al., PNAS, 2020; , Fu et al., PNAS, 2021; Yasuda et al., Nature, 2020). It is therefore very likely that the observed rhythm in trypsin- and chymotrypsin-like activity occurs post-translationally. Proteasome subunit composition is also known to change, which might be another reason for differences between the protease activities (Marshall and Vierstra, Front Mol Biosci, 2019; Zheng et al., J Neurochem, 2012).

To communicate this succinctly, we have revised the relevant text as follows:

Page 7: "Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-like proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B, (Wong et al, 2022)). Previous proteomics studies under similar conditions have revealed minimal circadian variation in proteasome subunit abundance (Wong et al, 2022), suggesting that proteasome activity rhythmicity, and therefore rhythms in UPS-mediated protein degradation, are regulated post-translationally (Marshall & Vierstra, 2019; Hansen et al, 2021)."

Regarding period length, we apologise for an oversight in Fig 1c: unlike all other experiments presented here, these fits were originally done with a flexible period length (between 20h and 36h). This has now been re-fitted in a similar manner to the other experiments (fixed period of 24h, same as the parallel PER2::LUC controls), and the updated data are presented. This has not influenced the results of the statistical tests (only changed the p-values slightly, but the significance levels remain the same).

Fig. 1a,b suggest that there is a rhythm in global protein synthesis with a significant peak at 40h. Yet, Fig. 1e suggests otherwise. How can that be? Also, the degradation graph (lower panel 1c) has to be plotted with the ratios calculated from the data points and not the heavily processed fitted graphs. This can be very misleading.

Fig1a,b was performed under quite different conditions to 1e. As described in the methods section, 35S-labelling experiments require a medium change during both pulse and chase (to replace normal Met with radioactive Met, and vice versa). To avoid growth factor/mTORC1-mediated stimulation of protein synthesis & turnover, these acute media changes must occur in the absence of serum; otherwise media changes would introduce artifacts. In contrast, puromycin labelling (Fig 1e) is performed without any media changes (as puromycin can be added directly to culture cell media), and therefore was performed in normal culture conditions of 10% serum. Thus, due to its well-established effect of growth factor/mTORC1 signalling on bulk translation rate, it is very likely that differences in the phase of translational rhythms between Fig1a,b and 1e are attributable to differing serum concentrations – this phenomenon of serum-dependency of phase is also described in Beale et al, 2023, bioRxiv https://doi.org/10.1101/2023.06.22.546020. The only important point, is that neither of these proof-of-principle experiments support the null hypothesis: that translation rate and turnover remains constant over the circadian cycle. Thus, the hypothesis being tested in Figure 1 is not rejected, and provides the rationale for the subsequent proteome-wide analyses.

With respect to 1E, given the variance of measurement, the curve fits to Puro and Puro+BTZ already serve to test whether there is any significant ~24h component, a ratio of the respective data points would simply compound the error of measurement. The degradation plot is provided purely for illustrative purposes to help the reader i.e. if these fits were true, what would be expected? We have revised the figure to more clearly communicate that the degradation plot is presented purely as a visual aid, labelled “inferred”, and now show ratio plots in revised Figure 1.

* **It also strikes me as odd that the amplitude of degradation increases (peak at 28h lower than at 30h) while the amplitude of the core clock oscillation dampens over time (peak at 54h higher than at 53h due to desynchronisation. Only two data values around 54h are responsible for the detected rhythm (2nd peak). Furthermore, phase and period do not agree with the rhythm of proteolytic activities shown in 1c. How can this be explained? *

Due to the nature of the experiment, the degradation rate inferred from Figure 1B & 1E does not reflect proteasome activity exclusively. Rather it reflects the combined sum of processes that remove nascently produced proteins from the cell's digitonin-soluble fraction, which includes proteasomal degradation, but also autophagy, protein secretion and sequestration into other compartments. Therefore, the peak degradation in Fig 1B & E would not necessarily be expected to coincide with the peak of proteasome activity in Fig 1C. Again, these experiments in Figure 1 simply serve to test the hypothesis (change over circadian cycle) vs the null hypothesis (no change over the circadian cycle).

To the question of amplitude increase, we speculate that this is due to metabolic changes in cultures over the course of three days – as serum and nutrients from the last medium change at T0 are depleted, cells need to increase degradation to promote turnover and recycling. As we suggest that the rhythms in turnover help cellular bioenergetic efficiency, it is quite plausible that amplitude increases as nutrient-concentrations fall. We are in process of further investigation into how exactly these rhythms vary with nutrient and serum status.i

* Regarding the MS data shown in Figure 2, is it possible to show a positive / quality control? Best would be MS data of Luciferase (or PER2,3, RevErb/alpha, DBP) to show oscillation of protein levels with the same phase and period as the reporter. *

Unfortunately, none of these low abundance transcription factors were detected in our MS runs. This is not surprising, given that their copy numbers are estimated at * In Fig. 2c examples of the 4 groups of proteins presented in 2e should be shown (both synthesis and total abundance arrhythmic, either one rhythmic or both rhythmic) and not just what appears to be random examples of rhythmic and arrhythmic proteins. *

As also requested by another reviewer, we have revised the figure to include examples of each of the rhythmicity categories. No specific meaning is inferred from the chosen protein identities.

Is it possible at all to distinguish between synthesis/turnover and assembly/disassembly of macromolecular complexes in the MMC SILAC experiment? If so, how?

We followed the established protocol originally developed in our collaborator Kathryn Lilley's lab, where it has previously been shown that most proteins in the MMC fraction are in macromolecular assemblies (Geladaki et al, Nat Commun, 2019). Proteins that are rhythmically abundant in this fraction, but without an accompanying synthesis rhythm (e.g. Beta-actin, see Hoyle et al., Sci Trans Medicine, 2017) can be reliably assumed to arise solely from rhythmic assembly/disassembly i.e. they are captured in this fraction when assembled, but lost, and therefore not detected, in this fraction when disassembled. However, in the case of rhythmic synthesis and abundance, it is not possible with this technique to directly infer that rhythmic synthesis of a given protein is responsible for its rhythmic assembly in a complex, though they do correlate.

Therefore, our new figure 5 (with thanks again for this suggestion) approaches this by an orthogonal method, relying on the important observations that a) ribosomes incorporate ribosomal RNA (rRNA) b) this can be readily separated from most other cellular RNA by density gradient centrifugation and c) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Using this technique, we validate a rhythm in production and assembly of mature ribosomes, with its peak consistent with the highest turnover time as measured in Figs 1 and 3, and MMC fraction proteomics (Supplemental table 3), at the descending phase of PER2::LUC.

* **Looking at Fig. 4b,c, what is the fraction of rhythmic proteins from the MMC experiment that also oscillate in either synthesis, total abundance or both in the whole cell? Is there a general correlation at all? Please show. *

There were no correlations greater than would be expected by chance (the sets of proteins rhythmic in either synthesis or degradation did not overlap significantly between whole-cell and MMC fractions, as determined by an odds ratio test).

To communicate this we have added the following text:

"It is also worth noting that although there were small sets of proteins that were rhythmic in both whole-cell (Figure 2) and MMC fractions (Figure 3), in both synthesis and total abundance, none of these four overlaps were higher than would have been expected by chance."

* **Why is the phase of the oscillating proteins different in the two experiments (compare Figs. 2f,g and 4a) and does either of them match with the phase of the PER2::LUC reporter, which should be the peak synthesis phase of the clock? *

This was a labelling error on our part, our apologies and thanks for drawing it to our attention. We had attempted to harmonise all these phase values so that they were mutually comparable between the two mass spec experiments, but omitted to update all the figures. They have now all been updated to be inter-consistent. From our experiments, the peak of PER2::LUC consistently precedes the timing of maximum bulk translation. This phase difference is, at least in part, attributable to the inactivation kinetics of firefly luciferase (see Feeney et al., J Biol Rhythms, 2016), i.e., under conditions of saturating luciferin substrate, PER2 protein abundance peaks several hours later than PER2::LUC activity when measured in longitudinal live cell assays.

* Regarding the sensitivity to MG132 in Fig. 5b it doesn't make sense that, while eIF2alpha phosphorylation is arrhythmic in untreated cells and the levels of eIF2alpha phosphorylation are (apparently) not exhibiting a rhythmic change by administration of MG132 at different circadian timepoints, the ratio of P-eIF2alpha with and without MG132 suddenly is. Please show in Fig. S4b quantifications of the individual experiments with and without MG132. What is presented in 5b is after all the ratio of ratios of quantifications of Western blots, each of which individually does not display any appreciable rhythm. For me this is two much of processing of data. In my opinion, the MG132 4h acute treatment must show a detectable rhythm.*

We apologise for being unclear in this panel and description. Our hypothesis concerned the fold-induction of the p-eIF2alpha:eIF2alpha ratio changing as a function of MG132 and time. Our reasoning being that the ratio may be more biologically-relevant as it is the relative change that cells sense and respond to, and not the absolute abundance of p-eIF2alpha. We applied a quantitative, two-channel fluorescent antibody technique to enable detection and quantification of p-eIF2alpha and eIF2alpha from each replicate at each time point from the same band of the same blot. We agree that no p-eIF2alpha rhythm is evident from a cursory inspection of any of the blots. This is due to the innate variance between dishes in extracted protein concentration, as well as the levels of basal eIF2alpha and its phosphorylation, and is the reason that we took great pains to be as quantitative as possible using the two-channel immuno-detection (LICOR). Due to the natural and stochastic variation in eIF2alpha levels and extraction between replicates and over time, it is difficult to get identical eIF2alpha loading to reveal the overlying rhythm in p-eIF2alpha, and furthermore, identical loading would give a misleading impression of the level of temporal variation of eIF2alpha levels. Quantification reveals temporal variation in the MG132 treated samples but not in the untreated controls (Supp Fig 5A) – suggesting that there may be circadian regulation of the cellular response to MG132 challenge, rather than a cell-autonomous p-eIF2alpha rhythm under basal conditions. We quantified fold-induction from MG132 vs untreated to present in Figure 6A. We have presented all the raw data in supplementary figure 5 for readers to validate through their own analysis.

*Minor:

In Fig. 1f please show dot blot with error bars as well as the individual experiments in the supplementals. Please check the graph legend (N>=3?) *

Thank you for pointing out these omissions. The dot blot with error bars is now shown in Fig. 1F, and the full gels are now included as Fig. S2B. The main figure legend for 1f has also had the following added (explaining the N numbers):s

"Four mice were used per condition, but in some cases one of the four injections were not successful i.e. no puromycin labelling was observed and so no quantification could be performed (full data in Fig. S2B)."

* Please explain the mechanism of the "booster" used in the second SILAC experiment. *

The following has been revised in the text:

" Namely, we added a so-called booster channel: an additional fully heavy-labelled cell sample within a TMT mixture (Klann et al, 2020). When the mixture is analysed by MS, heavy peptides from the booster channel increase the overall signal of all identical heavy peptides at MS1 level; at MS2 and MS3 this results in improved detection of heavy proteins in the other TMT channels of interest, and is particularly advantageous for the proteins with lower turnover that would fall below the MS1 detection limit without the booster."

*

**p10 3rd paragraph: S2e not S3e *

Thank you, this has been fixed.

p12 last paragraph please add reference to Figs. 5f,g

Thank you, this has been added.

*Reviewer #3 (Significance (Required)): *

xxxxx

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Referee #3

Evidence, reproducibility and clarity

Seinkmane et al investigate circadian regulation of protein synthesis and degradation in cultured cells and in mice. Their main new finding is that protein synthesis and degradation are in many cases rhythmic but coordinated such that the proteome is rhythmically renewed without an apparent rhythm in total protein abundance. Particularly the pool of large protein complexes is rhythmically renewed in this fashion.

Using pulsed SILAC in combination with mass spectrometry, the authors are able to distinguish between total and newly synthesized protein levels in mouse lung fibroblasts. Analysis of these data shows that the synthesis of a large number of proteins is rhythmic although the total amount is constant, or that proteins are synthesized at a constant rate but the total amount is rhythmic, suggesting that degradation is rhythmic. By analyzing macromolecular complexes, defined as a high-speed pellet, they also present evidence that the rhythmic components of large complexes oscillate in the same phase and have a similar protein turnover rate. The authors conclude that complexes assemble rhythmically. The authors also present evidence that the activity of the proteasome oscillates in a circadian manner. Based on this observation, they show (in fibroblasts and in mice) that the response to proteotoxic stress (monitored by eIF2alpha phosphorylation levels, protein aggregation, and apoptosis) is higher at circadian times of high proteasome activity.

I am an expert in the circadian field, and the hypothesis and concept behind the work presented here are potentially very interesting, and the experimental design is in principle suitable to answer these questions. However, after reading the paper several times, I cannot find the set of experiments that would convincingly support the authors' conclusions.

Major questions/points:

The major limitation of the manuscript is that the conclusions rely heavily on statistical analysis and massive processing of data from a bewilderingly large number of very different experiments. The critical experiments lack replicates and obvious controls. In looking at the figures, I have often wondered if the presence or absence of a rhythm is real or a product of the heavily processed data. The fact that a cosine wave fits through data points better than a straight line does not necessarily mean that a circadian rhythm is present. I think that in particular, the SILAC experiment(s) should be repeated and also performed with an arrhythmic control (such as CRY1/2 KO). Comparability between the whole cell and MMC SILAC experiments is also limited due to the different experimental conditions (6h vs. 1.5h pulse, +booster). The essential and new message of the paper is that (at least some) macromolecular complexes undergo circadian renewal (degradation and synthesis). Rather than just analysing an operationally defined pellet fraction by mass spectrometry, this could be shown in more detail and directly for one or two specific macromolecular complexes. Ribosomes, for example, seem particularly suitable, because there would also be the very simple approach of measuring the synthesis of ribosomal RNA by pulse labelling. To me, such an analysis would be perfectly sufficient as a proof of principle. I would then omit aspects such as rhythmic stress response, since many additional experiments are needed to demonstrate this convincingly.

Specific points:

The reader is strongly influenced by the cosine wave or straight lines in the graphs (e.g. 1c, e, 3h, 5b, etc) produced by the analysis of rhythmicity, which basically only gives a yes or no answer. But it is not really that simple. If the algorithm detects a rhythm what is its period? Is it the same as the period of the luciferase reporter? If the period lengths correlate, do the phases as well (e.g. see differences in phases 1c and e)? These questions are not addressed.

The algorithm in Fig 1c predicts a rhythm for the chymotrypsin-like and the trypsin-like but not for the caspase-like activity. The peptide assay measures core proteasome activity independent of ubiquitylation and should therefore be dependent on proteasome concentration in the sample. How can then only two of the three proteasomal activities be rhythmic? Please elaborate and repeat with arrhythmic cells (e.g. CRY1/2 KO). The period length does not seem to correlate with the one of the reporter. Why is that?

Fig. 1a,b suggest that there is a rhythm in global protein synthesis with a significant peak at 40h. Yet, Fig. 1e suggests otherwise. How can that be? Also, the degradation graph (lower panel 1c) has to be plotted with the ratios calculated from the data points and not the heavily processed fitted graphs. This can be very misleading. It also strikes me as odd that the amplitude of degradation increases (peak at 28h lower than at 30h) while the amplitude of the core clock oscillation dampens over time (peak at 54h higher than at 53h due to desynchronisation. Only two data values around 54h are responsible for the detected rhythm (2nd peak). Furthermore, phase and period do not agree with the rhythm of proteolytic activities shown in 1c. How can this be explained?

Regarding the MS data shown in Figure 2, is it possible to show a positive / quality control? Best would be MS data of Luciferase (or PER2,3, RevErb/alpha, DBP) to show oscillation of protein levels with the same phase and period as the reporter. In Fig. 2c examples of the 4 groups of proteins presented in 2e should be shown (both synthesis and total abundance arrhythmic, either one rhythmic or both rhythmic) and not just what appears to be random examples of rhythmic and arrhythmic proteins.

Is it possible at all to distinguish between synthesis/turnover and assembly/disassembly of macromolecular complexes in the MMC SILAC experiment? If so, how? Looking at Fig. 4b,c, what is the fraction of rhythmic proteins from the MMC experiment that also oscillate in either synthesis, total abundance or both in the whole cell? Is there a general correlation at all? Please show.

Why is the phase of the oscillating proteins different in the two experiments (compare Figs. 2f,g and 4a) and does either of them match with the phase of the PER2::LUC reporter, which should be the peak synthesis phase of the clock?

Regarding the sensitivity to MG132 in Fig. 5b it doesn't make sense that, while eIF2alpha phosphorylation is arrhythmic in untreated cells and the levels of eIF2alpha phosphorylation are (apparently) not exhibiting a rhythmic change by administration of MG132 at different circadian timepoints, the ratio of P-eIF2alpha with and without MG132 suddenly is. Please show in Fig. S4b quantifications of the individual experiments with and without MG132. What is presented in 5b is after all the ratio of ratios of quantifications of Western blots, each of which individually does not display any appreciable rhythm. For me this is two much of processing of data. In my opinion, the MG132 4h acute treatment must show a detectable rhythm.

Minor:

In Fig. 1f please show dot blot with error bars as well as the individual experiments in the supplementals. Please check the graph legend (N>=3?)

Please explain the mechanism of the "booster" used in the second SILAC experiment.

p10 3rd paragraph: S2e not S3e

p12 last paragraph please add reference to Figs. 5f,g

Significance

xxxxx

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Referee #2

Evidence, reproducibility and clarity

Summary:

This is a very interesting and well written paper that addresses key questions in the circadian organization of proteostasis. The paper investigates origins of cellular circadian rhythms, invoking a premise early that there is a poor correlation between rhythmic gene expression - regulated by the canonical TTFL - and rhythms of the proteome, which are rather meager. Specifically, they ask how a relatively stable proteome is possible if cells engage in rhythms of cellular protein synthesis? Their hypothesis is that protein degradation must rhythmically compensate for rhythms of synthesis and much of the manuscript is focused on defining the relationship between rhythmic global synthesis and rhythmic degradation. They employ a series of detailed proteomic investigations and biochemical assessments of protein synthesis coupled with various circadian reporters to assess proteosome function. The proteomic experiments reveal a limited number of proteins with oscillations in either synthesis or abundance or both and no discernible pathway organization however, a followup and more refined study that utilized fractionated samples and boosted heavy SILAC identified strikingly, that many proteins in relatively heavy fractions are rhythmic and that these fall into possible complexes including ribosome and chaperonins. Finally, they perform in vivo experiments testing whether the timing of proteotoxic stimuli regulates the degree of the integrated stress response measured as pEif2a.

Overall, I think that this is a fascinating paper that addresses and important question but falls short on mechanistically unifying them and completely contextualizing the findings in light of the canonical modes of circadian timekeeping leaving us with an important, but mostly descriptive set of findings. In addition, there are a number of important questions about data interpretation, some issues with data quality that should be addressed outlined below. With revision and further explication, this study will be an excellent addition to the growing field of circadian organization of the cellular proteome.

Major and minor Comments.

Figure 1.

Fig 1a. The difference in Pulse and Chase at ZT24 does not appear to reflect the quantified data in 1b. This should be reconciled to make the figure convincing. How was the timing of the chase collection determined? Fig 1d-e. What is the evidence that puro labeling results in 'rapid' turnover. Fig 1e seems to be missing the data from the treated and untreated conditions? How are the lines produced (e.g. linear versus rhythmic? Are these drawn lines or actual regressions?). Why was 30 minutes chosen as labeling time? It seems hard to understand here how protein degradation kinetics can be measured by puromycin labeling if the authors' claim that puromycin labeling potentially changes degradation rates as a function - primary or secondary - of the labeling itself. It seems they are measuring the potential to degrade proteins. How do they determine that they are measuring degradation of functionally relevant proteins as opposed to a host of premature truncations? Fig 1e bottom - again is this a true regression line? Perhaps two time points should be examined here - similar to the pulse chase performed with 35S labeling? Fig 1f. It appears that Puro labeling results in a rhythm between ZT1 and ZT13 but no statistic is provided and appears that the 'ns' is the results of variance in the data as opposed to difference in means? - would this not contradict the cellular result? What accounts for the rhythm reversal in the presence/absence of BTZ.

While the authors have previously demonstrated an increase in rhythmicity of the proteome in Cry1/Cry2 double knockout cells, it would have been welcome here to test a global loss of circadian transcription in the degradation assay. One might expect that these rhythms would also be even higher. What I am really asking is: what is the mechanism for rhythmic degradation and is it dependent on the canonical clock?

Fig 2. How was the 'fixed window' timeframe determined?

Fig 3h. While admittedly difficult, the native PAGE is not of great quality and kind of unconvincing. Also not really sure why the AHA labeling is used here an nowhere else in the paper.

Fig 4. I was a little disappointed here that the authors did not directly assess macromolecular assembly of at least one of their "hits" and demonstrate functional relevance and most of the analysis is maintained at a very superficial, systemic level. STRING assemblies are not terribly helpful without clear k-means clustering or some other clearly visualizable metric for stratifying and organizing the putative PPI data - this figure (S3) could be markedly improved.

Is it possible that some macromolecular complexes have rhythms because their constituent proteins have differential half-lives when in one complex compared with another in circadian time? This possibility was not discussed.

Fig. 5.

Why is the first histogram in 3c not at unity? Do ZT24 and Zt48 differ, similarly do ZT36 and ZT60? Fig S4f is not of good quality with missing eIF2a total and therefore no loading controls. S4e? true regression lines?

While I thought these experiments were effective, they did not tie back well to the rest of the paper. What are the consequences of a temporally sensitive ISR? Which pathways does it effect in circadian time? Here, the main holes in this study are somewhat exposed; namely, a lack of mechanistic depth in explaining the very fascinating, albeit mostly descriptive, findings. The implicit assumption made here is that aggregation is 'bad' but could the opposite be just as true? Taking these considerations in account would further strengthen the discussion.

Significance

This is a fascinating paper that addresses key questions in the circadian organization of the proteome. The paper's main findings are that rhythms of protein synthesis and degradation are temporally coordinated to maintain overall stability of the proteome in mouse fibroblasts. Furthermore, the authors present evidence that this temporal organization may be important for assembly of macromolecular complexes. While very interesting, the main limitations are a lack of biochemical and mechanistic explanation and evidence that verifies these, mostly descriptive, findings.

There are some relatively minor statistical and data quality issues that are probably addressable relatively quickly.

Upon revision the study would be a welcome addition to investigators interested in proteostasis, circadian biology, cell biology and proteomics.

I am a physician-scientist with expertise in circadian rhythms, cell biology, protein synthesis, and biochemistry.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Circadian regulation of protein turnover and proteome renewal" investigates the role of protein degradation in the circadian control of proteostasis. The researchers suggest that the relatively static levels of protein levels in a cell are incongruent with the known oscillation in protein synthesis. They therefore hypothesize that there should be a compensatory mechanism to counteract rhythmic protein synthesis, rhythmic protein degradation. To investigate this, they employ bulk pulse chase labeling to study the process of degradation. They identify a synchronization between the creation and turnover of proteins in a cell, implying the clock helps to maintain homeostasis through a novel mechanism. They note that these phases align with energy availability, granting a plausible reasoning behind the biological implementation of this regulation. In summary, this is a sound manuscript that adds to the research field. The experiments in this manuscript are well thought out, organized, and explained. In general, the authors do not go further in their conclusions than I think is warranted given the data that they have, though I think that there are some key items that should be addressed before the publication of this manuscript.

Major notes:

1. In figure 1, a clearer idea of what the ** means would be appreciated. What was the standard of significance for this measure?
2. In Figure 1b, it is important to note clearly in the text that the this is not a direct measure of protein degradation, but a subtractive proxy. Though I don't think that necessarily makes the authors conclusions incorrect, the same result could also be obtained if an extra 15% of the proteins were moved into the insoluble fraction. This is the same for Figure 1E and F.
3. In figure 1c, is the noted oscillation in protease activity due to the oscillation of these proteins? What are the predicted mechanisms behind this? I don't think that this is necessarily within the scope of this paper but should be addressed in the discussion. Also, the peak degradation rate from Figure 1B is 4 hours before the peak enzyme activities. How can this observation be reconciled?
4. For the pSILAC analysis, the incorporation scheme has a six-hour window between the comparison of the light and heavy peptides. This makes it somewhat difficult to assess whether you are looking a clock effect from T1 or T1+6. This does not negate the findings, but it does question when the synthesis is occurring and what is being compared, which I think should be more clearly discussed in the manuscript. This is discussed later in the manuscript but should be mentioned in this section.
5. There are no error bars on figure 2C. What the pSILAC just done in a singlet? If so, the rhythms estimation is likely a large overestimate and should be noted.
6. Why were the genes selected in 2C? these are not discussed anywhere else in the manuscript.
7. The authors note that for Figure 2 "These observations are consistent with widespread rhythmic regulation of protein degradation." However, only 5-10% of the proteome is oscillating at any level and less with a discrepancy between synthesis and abundance, so "widespread" is an exaggeration and this statement should be limited to the degradation in the rhythmic proteome.
8. The authors note that their more developed strategy in figure 3 would allow for the detection of less abundant proteins. However, they do not discuss that they in fact found less proteins overall, or if they were able to detect proteins of lower abundance. This is of some concern in determining if this is indeed the better method that they predict. How can the authors reconcile this issue? How can they rationalize this explains their increase in oscillating elements?
9. In the comparison of complex turnover rates, the authors need to provide a metric that backs their statement that "the majority of component subunits not only showed similar average heavy to total protein ratios but also a similar change in synthesis over the daily cycle" for figure 3F.
10. In reference to the AHA incorporation, why is the hypothesis not that, like the puramycin, you would not see oscillation unless you add BTZ? Shouldn't the active degradation regulate the incorporation of AHA such that there is no visible rhythm unless you suppress degradation?
11. The authors claim that there is enrichment of the actin cytoskeleton, but where this data can be found should be explained. The only thing that is shown is a few selected graphs of proteins in this pathway.
12. The authors note an oscillation in the total levels of p-eif2, commenting that these do not arise from the rhythms in total eif2a but temperature and feeding rhythms. However, unless I misunderstood, this work was done in fibroblast cell culture, so in this case, where would these temperature and feeding rhythms come from?
13. In Figure 5d, the treatment impeding degradation is causing cell death while the inhibition of translation does not. However, wouldn't too much, or not enough, translation, without compensatory regulation from degradation cause a problem in the same way that degradation does?

Significance

The information that stems from this work is relevant and of interest to circadian clock field as how the regulation of the output of the circadian clock is implemented is still a major question in the field. This manuscript suggests a novel and plausible method for how, at least in part, this regulation occurs. However, the manuscript uses methods that do not measure degradation directly, which is a minor limitation. In addition, the mechanisms by which this regulation is imparted are not addressed in any meaningful way, even in the discussion.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Abe et al. generated multiple novel mouse model that follows and labels Col4a2 by fusing it with GFP. The creation of this mouse model allowed for the analysis of the basement membrane in real-time using live imaging of embryonic explant cultures. The combination of the mouse model with live imaging revealed new insights into how the basement membrane turnover occurs during early hair follicle development. After setting the stage the authors establish its utility with embryonic tissue, which revealed membrane buds that could be visualized with eGFP at different time intervals for 19h. The growth of the hair follicle bud during that time could be divided three distinct areas, the upper, lower stocks, and the tip. Where the tip and lower stalk increased in BM length, while the upper stalk decreased. BM length correlated with increased cellular replication. Using a double transgenic model system, they evaluated the differences between 'cell displacement', 'BM expansion', and 'cell autonomous movement'. Diving deeper with the Col4a2-mKiGR mouse model investigated Col4a2 turnover to reveal similar results mentioned above. Lastly MMP inhibitors were used to investigate how hair follicle growth is affected, which revealed inhibition of cellular replication and inhibition of Col4a2 turnover. These results inhibited hair follicle elongation which made the forming hair follicles thicker.

Overall, this is an interesting paper for hair follicle biologists since it investigates the early moments of the budding follicle in real time using a ex vivo culture model. In addition, there is additional appeal because the authors use live imaging the hair follicle neogenesis as a basement membrane model, which is interesting and novel. The manuscript is clearly written, and the data support the overall conclusions. My comments below are to help in clarity which may be used to develop clearer figures and additional text.

Major:

In Figure 2 for the cell displacement and expansion part. I found the figure and text confusing, particularly in regard to how the data shows the bleached edge of the BM moving alongside the cells. Could the authors make this clearer in the figure and in the writing of the text?

The authors created a Col4a2-mKikGR mouse line that is supposed to follow Col4a2 turnover. It is difficult to understand how the authors can claim that it was turnover with the explanation in the text of how the mouse model works. Could the authors write a better description of the mouse model in the text?

Significance

The strengths of the paper are the use of a novel mouse model that can track collagen (Col4a2) with a tagged GFP and the live imaging model system. This has led to a novel and important knowledge on the interplay between the BM and cells. The limitation of the manuscript is that the entire manuscript utilizes a single protocol (live imaging) to investigate BM dynamics. This might be due to the sophisticated nature of the model systems, but it is a limitation.

To my knowledge the study is novel because of the mouse model to track Col4a2 dynamics with GFP. This model led to some interesting findings about hair follicle development in that different regions expand differently with the BM. This is good foundational knowledge using the latest state of the art techniques in live imaging of embryonic tissue culture systems.

The audience that would be interested in this manuscript is broad, which would span cell and developmental biology but also specialists in membrane and protein biology that can finally see in real time the dynamics of Col4a2 building skin and hair.

My expertise in in hair follicle development and repair and stem cell biology.

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Referee #2

Evidence, reproducibility and clarity

The authors successfully generated a knock-in mouse line expressing fluorescence-tagged endogenous collagen IV. Homozygous mice exhibited normal survival with no apparent developmental abnormalities. Through imaging of the back skin of COL4A2-eGFP mice in ex vivo culture, the authors observed a faster expansion rate of the basement membrane (BM) at the growing tips of developing hair follicles, while the upper stalk region showed a slower BM expansion rate. Real-time imaging also revealed that the BM and basal epithelial cells moved in the same direction. Fluorescence recovery after photobleaching (FRAP) and the photoconvertible protein mKikGR experiments demonstrated a faster turnover rate of COL4A2 at the tips of the hair follicles. The authors used MMP inhibitors to suppress the recovery of COL4A2-eGFP, BM expansion, and observed abnormalities in the developmental process of hair follicle morphology. The findings are novel and interesting, some aspects of how the experiments and quantifications were conducted should be clarified to allow the readers to fully appreciate the results.

Major Comments:

1. BM Expansion Statistics: Regarding the statistical analysis of BM expansion, is the length of the BM affected by the z-axis plane at the time of imaging? How is it ensured that the BM length measured at different time points corresponds to the same z-axis?
2. Cell Movement Statistics (Figure 2): In the statistical analysis of cell movement in Figure 2, the lack of other references raises questions about ensuring that the cells measured at different time points are the same cells.
3. The authors concluded that the inhibition of MMP delayed the recovery of COL4A2-eGFP after photobleaching, indicating the crucial role of MMP activity in the incorporation of COL4A2 into the BM. Does MMP inhibition lead to a reduction in the synthesis of the COL4A2 protein, thereby delaying the recovery of COL4A2 in the BM?

Minor Comments:

In Figure 1D, the representative image and the statistical graph are inconsistent. For example, in the upper stalk region, all basal epithelial cells have Ki67 signals according to the representative image.

Significance

The authors successfully generated knock-in mice expressing fluorescence-tagged endogenous collagen IV. With this novel mouse model, researchers can directly observe the dynamic changes in the extracellular matrix of different organs in mammals during development and disease, revealing the potential roles of the extracellular matrix.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Wuergezhen et al. generated two fluorescently tagged Col4a2 mouse models, including EGFP-Col4a2 and the photoconvertible mKikGR-Col4a2. They showed that tagged collagen IV get incorporated in the basement membranes of various tissues in the developing and adult mice, and fully support embryonic development, fertility, and physiological functions. The authors followed up investigating Col4a2 dynamics during embryonic development of the hair follicle. Using FRAP, they showed that the basement membrane expands with a faster rate near the tip region. This coincided with faster turnover rates of Col4a2 at the tip relative to the lower and upper stalk. In addition, the authors demonstrated that Col4a2 turnover depends on MMPs.

Major comments:

• Are the key conclusions convincing?

The major conclusions of the manuscript are convincing. These include that tagging collagen IV does not compromise its function, differential expansion of the basement membrane, differential turnover of the Col4a2, the MMP dependence for normal basement membrane expansion and turnover. However, some claims detailed below need to be clarified or addressed to improve the manuscript. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

In Figure 2B-C, the authors conclude that basement membrane expands at different rates, depending on the region with higher expansion rates near the hair follicle tip. From their methods, they conducted repetitive photobleaching cycles every 2-3 hours to maintain the bleached status of ROIs and tracked changes in basement membrane length. However, it sounds challenging to repetitively photobleach the same ROI in a dynamically expanding tissue, which may compromise the accuracy of length measurements. It would be helpful if the authors could provide movies corresponding to these experiments for clarity. In addition, this repetitive bleaching should be highlighted in the figure and figure legend, as readers could get confused about why there is no recovery here when comparing to the FRAP experiment.

In Lines 180-198 and Figure 2F-H, the authors interpreted cell movement as contributed by cell-autonomous vs basement membrane expansion, which is speculative. Another possibility is that cell movement was all autonomous, while basement membrane expansion was caused by mechanical stretching that was in turn caused by cell proliferation. This conclusion should be rephrased.

Following MMPi treatment, the authors found that basement membrane expansion was halted (Figure 4C-D). Yet, they later showed that hair follicles widened under MMPi treatment (Figure 4E-J). Under these conditions, I would have expected such widening to be accompanied by basement membrane expansion at the lower or upper stalk, which is not the case, at least for the first 7 hours (Figure 4C-D). How do the authors interpret this? - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Considering the rapid expansion of BM near the tips, I wonder whether the authors have explored possible structural differences of the basement membrane in different regions? Is the basement membrane near the tips thinner and/or does it have microperforations as reported in other systems? Looking into this may further support their observations, not only in control conditions but also in MMPi treated follicles. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Yes, for possible structural changes, 3D rendering of fluorescence imaging as shown in Figure 1J may be sufficient.

Increasing sample number using existing mouse strains should also be feasible. It would take 2-3 weeks from setting up timed pregnant mice to imaging the embryonic skin explants. Adding image analysis and figure preparation, it should be doable within 1 month. - Are the data and the methods presented in such a way that they can be reproduced?

In Figure 2D/ Figure 5C, it is unclear how ROIs corresponding to tip/lower/upper stalk are being drawn for quantification of Ki67+ cells.

The images in 2B and 4C, 3A and 4E, are identical. Images should not be re-used in figures. This raised the concern that probably not sufficient samples were imaged to have different representative images. It should also be clarified where the data was re-used, for example, the control data in 2C and 4D, 3B and 4B. - Are the experiments adequately replicated and statistical analysis adequate?

A few experiments have low sample numbers while the data was quite variable. These include Figure 2G-H (n = 3 cells), Figure 3C (unknown sample number), Figure 4B (n = 3 hair follicles), Figure 5B (n = 3 hair follicles). More sample numbers (~10 total) should be included to solidify the findings.

For the mKikGR experiment in Figure 3C, quantification should be included. A ratiometric measurement of green/red fluorescence over time should be a good complementary way of demonstrating region-specific recovery.

In Figure 5B, the authors claim that the percentage of dividing cells in control follicles being different from that of MMPi-treated follicles. How are they extracting these percentages? From the plots, control and MMPi-treated columns do not appear to be normalized as 100% to make such comparisons. Moreover, having two mean+/-SD in each column makes these data confusing to interpret. The authors should consider replotting their data either by combining their data into a unique population per conditions and reporting the percentages, or alternatively, they may consider splitting each of these columns into two (i.e., dividing vs. non-dividing cells), and comparing both conditions as ratios of dividing versus/non-dividing cells.

Minor comments:

• Specific experimental issues that are easily addressable.

Already addressed above. - Are prior studies referenced appropriately?

I believe so. <br /> - Are the text and figures clear and accurate?

All plots measuring basement membrane length are labeled as 'increase in BM length', even when in some cases the BM length is reduced. The authors should consider relabeling these as 'BM length change' or something similar.

The second and third paragraphs of the discussion are too long and should be condensed into a single paragraph. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Use better color combination for visualization of multi-channel images. For instance, magenta/green is a better combination than red/green for the color blind. Color combinations are not consistent across figures in the manuscript.

Include movies for all data derived from live imaging.

Include statistical tests used for all plots, some are missing.

The authors should consider fitting their FRAP data in each condition and report percentages corresponding to the mobile and immobile fractions.

Examples of horizontal vs perpendicular cell division appear to be mislabeled in Video5.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
• The large molecular weight of extracellular proteins makes it challenging to generate genetically engineered versions of such proteins to investigate their function and dynamics in vivo. The present study has addressed such issues for Col4a2, a major component of the basement membrane. This study further provides insights towards the understanding of BM dynamics during embryonic organ development.
• Place the work in the context of the existing literature (provide references, where appropriate).
• Addressed above
• State what audience might be interested in and influenced by the reported findings.
• Cell and developmental biology, extracellular matrix biology, organ development and regeneration.
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.
• Tissue morphogenesis, extracellular matrix

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

This manuscript has potential interest as a preclinical study for glioblastoma treatment. There is a substantial amount of data that is promising, but there are numerous issues that will require additional experimental effort before publication.

Major concerns:

1. The title is overly general and uninformative. The authors should include the drug name (mubritinib) and the specific tumour type (glioblastoma).
2. The concept that mubritinib functions through metabolic effects is not surprising given recent publications (PMID: 37382244; PMID: 35429141; PMID: 33245718; PMID: 31287994) and that it impacts the blood-brain barrier (PMID: 36178590). However, there are limitations to the strength of this observation. Most of the experiments are associations between drug treatment and metabolic changes. The NDI1 partially rescue experiments in Figures 1h and 1i are nice but show that NDI1 expression itself increases OCR. This experiment is also performed over a very brief window of time. A better set of experiments would include measurement of cell number over a prolonged time course (Figure 2d has one time point) and to use a genetic targeting strategy against ETC complex 1.
3. The authors observe that EGFR expressing lines are more sensitive to mubritinib. As the rescue experiments are only partially effective and ERBB family members may be targeted by mubritinib, it is critical to address the effects of mubritinib on EGFR activation and perform rescue studies, as the application of mubritinib in patients may be guided by the EGFR mutational state.
4. The differences found with NSC responses is interesting but needs to be developed. Why are there differences in mubritinib responses? For example, do NSCs not require ETC complex 1 as much?
5. I would suggest that the authors also compare sensitivity of the BTSCs (I would suggest a change in nomenclature as these are only from GB) and differentiated tumour cells to determine if the stem cells have greater dependence. Please use similar culture conditions.
6. The differences in cell cycle are useful but the mechanism is lacking. The claim that self-renewal is drastically or markedly changed is overstated. The ELDAs are not striking. There is no evidence that stemness is a direct target.
7. The in vivo effects on cell biology need greater analysis in mechanism. I am also not sure why the authors switch lines tested in different assays.
8. The mechanism of interaction with radiation is not developed. What is happening here? Are there changes in DNA damage repair or simply growth? This is a nice observation that could be better developed.

Minor concerns:

1. Grammar needs attention.
2. Please remove the overuse of "strikingly", "drastically", "importantly", etc. Most of these descriptions are overstated.
3. The number of in vivo replicates needs to be addressed.
4. All gene expression data should be deposited. All raw data (numeric) should be made available.
5. Please replace all normalized data with raw data. The statistical testing was likely incorrectly performed, and this can give rise to false conclusions. I am particularly concerned about the normalization to cell numbers.

Significance

This manuscript has potential interest as a preclinical study for glioblastoma treatment. There is a substantial amount of data that is promising, but there are numerous issues that will require additional experimental effort before publication.

Major concerns:

1. The title is overly general and uninformative. The authors should include the drug name (mubritinib) and the specific tumour type (glioblastoma).
2. The concept that mubritinib functions through metabolic effects is not surprising given recent publications (PMID: 37382244; PMID: 35429141; PMID: 33245718; PMID: 31287994) and that it impacts the blood-brain barrier (PMID: 36178590). However, there are limitations to the strength of this observation. Most of the experiments are associations between drug treatment and metabolic changes. The NDI1 partially rescue experiments in Figures 1h and 1i are nice but show that NDI1 expression itself increases OCR. This experiment is also performed over a very brief window of time. A better set of experiments would include measurement of cell number over a prolonged time course (Figure 2d has one time point) and to use a genetic targeting strategy against ETC complex 1.
3. The authors observe that EGFR expressing lines are more sensitive to mubritinib. As the rescue experiments are only partially effective and ERBB family members may be targeted by mubritinib, it is critical to address the effects of mubritinib on EGFR activation and perform rescue studies, as the application of mubritinib in patients may be guided by the EGFR mutational state.
4. The differences found with NSC responses is interesting but needs to be developed. Why are there differences in mubritinib responses? For example, do NSCs not require ETC complex 1 as much?
5. I would suggest that the authors also compare sensitivity of the BTSCs (I would suggest a change in nomenclature as these are only from GB) and differentiated tumour cells to determine if the stem cells have greater dependence. Please use similar culture conditions.
6. The differences in cell cycle are useful but the mechanism is lacking. The claim that self-renewal is drastically or markedly changed is overstated. The ELDAs are not striking. There is no evidence that stemness is a direct target.
7. The in vivo effects on cell biology need greater analysis in mechanism. I am also not sure why the authors switch lines tested in different assays.
8. The mechanism of interaction with radiation is not developed. What is happening here? Are there changes in DNA damage repair or simply growth? This is a nice observation that could be better developed.

Minor concerns:

1. Grammar needs attention.
2. Please remove the overuse of "strikingly", "drastically", "importantly", etc. Most of these descriptions are overstated.
3. The number of in vivo replicates needs to be addressed.
4. All gene expression data should be deposited. All raw data (numeric) should be made available.
5. Please replace all normalized data with raw data. The statistical testing was likely incorrectly performed, and this can give rise to false conclusions. I am particularly concerned about the normalization to cell numbers.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript Burban et al explore the effect of the mitochondrial oxidative phosphorylation (OXPHOS) inhibitor Mubritinib on patient derived glioblastoma stem cells and murine xenografts. The authors first show that i) Mubritinib is an inhibitor of OXPHOS in brain tumor stem cells (BTSC), ii) that it impairs cell growth and self-renewal of patient-derived BTSC with different genetic background and iii) has an effect on the expression of genes related to stemness. In addition, the authors convincingly show that Mubritinib is a brain penetrant drug, and by transplanting luciferase expressing BTSC into the brain of immunodeficient mice they show it delays GB tumorigenesis and the animal lifespan (either alone, or more efficiently if combined with IR treatment). Finally, by performing toxicological and behavioral studies in mice models, Burban et al demonstrate that Mubritinib has a well-tolerated and safe profile and does not induce damage to healthy cells.

The manuscript is well written and organized and the data is clearly presented. The results are convincing, but a few additional experiments and controls would be beneficial to support the claims of the paper, most of which are easily addressable.

Main comments:

• Finding suitable control cells for BTSC experiments is a widely acknowledged challenge in the field. However, in line with other studies, it is recommended that the authors consider using a non-oncogenic NSC as control line to demonstrate that the effects reported in Figure 1 and Figure 2 are more pronounced in BTSC compared to NSC (as it was done in Suppl Fig3).
• Figure 5 presents a significant finding indicating that Mubritinib enhances the sensitivity of GB tumors to IR. Considering that Temozolomide (TMZ) is the primary chemotherapy drug for GB patients, it would be crucial to investigate the potential outcomes of a combined treatment involving Mubritinib and TMZ. This will help determine if the combination exhibits promising results, comparable to what is demonstrated in Figures 5d, 5g, and 5i for Mubritinib and IR. Such experiment would reinforce the drug's potential for clinical trials in GB treatment.

Minor comments:

• The authors should specify early in the paper what is the number of samples of patient-derived BTSC they use and the fact that their genetic mutations are known (this information is summarized in the supplemental table 1, but only reported later in the manuscript). This information is important and should be clearly stated at the beginning of the manuscript.
• In Figure 2a the inhibition at 20nM is significant but not very pronounced. Based on Figure 1 I would have expected to see a stronger effect at this concentration range. Can the authors comment/provide an explanation for this discrepancy?
• The EdU incorporation experiment presented in Figure2h-I should be repeat with lower concentrations of the drug (in most of the assays the effect of Mubritinib is detectable at much lower concentrations).
• Since the authors have done RNA-seq on the samples why don't they report the specific subtypes of their samples in the text and in Suppl Table 1 (Proneural, Neural, Classical or Mesenchymal) ? It is known that different molecular subtypes respond differently to treatments; therefore this information would be essential to understand if Mubritinib is effective on a wide range of GB subtypes.
• In Figure2b and Supplemental Figure1b-c : instead of correlating the effect with genetic mutations, it would be more relevant if the authors could correlate the data with the molecular subtypes inferred by RNA-seq (see my comment above)
• Regarding the RNA-seq experiment the authors should report what is the percentage (and numbers) of genes that change expression. Is there for example a preference for up- or down- regulation? It would be interesting to see a Gene Ontology (GO) analysis for the up-regulated genes versus a GO analysis of the down-regulated genes to confirm that the relevant categories show dysregulation as expected (e.g. enrichment for cell cycle and stemness genes in the down-regulated list, etc ).
• In Figure2 m-o the difference between CTL and Mubritinib treated cells do not seem substantial, although it is shown as statistically relevant. Can the authors specify the percentage to be able to better assess the differences?
• Add p-value for Figure3a-c
• In the western blot in Supplemental Figure 3b Vinculin shows twice
• Change" Given that Mubritinib is already completed a phase I clinical trial" into "...has completed..."

Referees cross-commenting

I agree with other reviewers that more data is needed to determine if mubritinib could be an effective treatment for various GB subtypes. The models used in this study do not encompass the full spectrum of GBM genetics. The authors should repreat the experiments using models that represent the major genetic/transcriptional subtypes of GBMs and clearly label and identify them in the study. Specifically, the authors should include models like 'classical/EGFR-amplified', 'mesenchymal', 'proneural/PDGFR amplified'. Alternatively, it is advisable to refrain from asserting that mubritinib is effective across genetic alterations in the manuscript.

Significance

Considering the limited effectiveness of existing treatments, it is crucial to explore alternative approaches to improve patient outcomes. This study demonstrates promising potential for the clinical translation of Mubritinib in GB treatment.

A major limitation of this study is the narrow numbers of patient-derived samples used and absence of a proper control cell line. Unfortunately, as evidenced by the existing literature in the field, selecting a control cell line for glioma stem cells research is challenging due to the unknown cell-of-origin for this type of tumor. In addition, all the toxicity/safety tests were performed in mice models and it is difficult to predict how this would translate into human patients. However, the fact that a phase I clinical trial has already been completed for Mubritinib (in the context of a different type of tumor) is encouraging.

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Referee #1

Evidence, reproducibility and clarity

The authors report the use of mubritinib, a drug targeting complex I of the mitochondrial electron transport chain, to halt the proliferation of brain tumor stem cells (BTSCs) isolated as neurospheres from glioblastomas. They demonstrate that mubritinib crosses the blood-brain barrier, and show that this drug delays GBM tumorigenesis and extends lifespan in mouse models that were generated by transplantation of human BTSCs or mouse cell lines. They also provide evidence that this potentially harmful drug is well-tolerated by mice.

The ability of mubritinib (initially conceived as a ERBB2 inhibitor) to block complex I of the electron transport chain was previously identified in acute myeloid leukemia, where this drug proved to selectively inhibit a subset of cases relying on oxidative phosphorylation (OXPHOS). However, the use of mubritinib is novel in GBM, a lethal malignancy for which a few therapeutic options are available, and no substantial progress has been reported since 2005. In addition, the authors show that accumulation of mubritinib in the brain tissue allows for the use of a reduced dose of mubritinib, thereby reducing the risk of the deleterious effects that blunt enthusiasms about targeting of mitochondrial respiration.

However, this manuscript presents significant weaknesses that are detailed below. In particular, the models used appear insufficient to support the conclusion, stated in the abstract, that the drug can be effective in GBMs with different oncogenic mutations. Based on the provided evidence, the claim that 'mubritinib potently impairs stemness and growth of patient-derived BTSCs harboring different oncogenic mutations' should be removed, or supported by using BTSCs that adequately represent the major GBM subtypes identified by genetic and transcriptional analysis. Specifically, BTSCs harboring EGFR amplification (displayed by 40% of GBMs) would need to be added. Equally, it is inappropriate to conclude (Discussion, page 14) that the models used, displaying EGFR mutations, are representative of widespread EGFR alterations: indeed the EGFR alteration observed in 40-50% of patients is EGFR amplification, whose pathogenic effects can not be recapitulated by the EGFR mutation harbored in the models used. If models harboring EGFR amplification are unavailable to these authors, making unrealistic to repeat the experiments in at least two different EGFR-amplified BTSCs in the timeframe allowed for revision, not only the claim that mubritinib inhibits BTSCs harboring different oncogenic mutations should be removed, but lack of experiments in EGFR-amplified BTSCs should be discussed as a limitation of this study. In addition, as detailed below, in vitro experiments should be expanded to corroborate mechanistic aspects of the drug, safety should be better demonstrated and some aspects of in vivo experiments should be clarified. Overall, the methodology seems sufficiently detailed to allow reproduction. The experiments are adequately repeated and the statistical analysis is appropriate, but in one case detailed below.

Major Point N.1

Figure 2a and 2c. Although statistically significant, the effect of mubritinib at 20 nM is biologically of limited significance in a subset of BTSCs, where the drug reduces viability by less than 25% (Fig. 2a). Therefore, the correlation between oxygen consumption rate (OCR) and mubritinib sensitivity (% of live cells), shown in Fig. 2c, should be presented for all mubritinib doses, and particularly for the dose of 500 nM, which is utilized in subsequent experiments. Additionally, it would be useful to display the correlation not only between viability and basal OCR but also with maximal OCR. This analysis could identify varying levels of sensitivity to ECT inhibition, aligning with the expectation that different BTSCs may exhibit varying degrees of dependency on mitochondrial OXPHOS. This would suggest that different GBMs may require different dosages of the drug. In all the experiments presented in the manuscript, the authors use the lines exhibiting the highest mubritinib sensitivity (BTSC 53, BTSC73), which might not be representative of all GBMs. This selection bias need explicit clarification in the text.

Major Point N.2.

In Fig. 2b, the statistics is significantly biased as it is calculated based on technical replicates, rather than on a significant number of independent models featuring either wild-type or mutated EGFR. Presented in this manner, this analysis is unacceptable. Additionally, as noted previously, the models used in this manuscript do not represent the overall GBM genetics, particularly due to lack of EGFR amplified models, which correspond to 40% of cases, and cannot be recapitulated by EGFR mutations. In general, the number of models is too small to draw any conclusion regarding the relationship between genetics and mubritinib sensitivity (including conclusions concerning TP53, or the MGMT status, shown in supplementary figures 1b-c). If the authors intend to claim that GBMs are sensitive to mubritinib independently of the genetic status, they should repeat their experiments by using models representative of the major genetic/transcriptional subtypes of GBMs, by clearly characterizing and identifying them in the experiments: e.g. 'classical/EGFR-amplified'; 'mesenchymal'; 'proneural/PDGFR amplified'. Otherwise (more realistically), it is suggested to remove claims that mubritinib is effective independently of genetic alterations throughout the manuscript (including the abstract and the discussion).

Major Point N.3

Fig. 2k-l present a transcriptional analysis with questionable representativeness as it is performed on the single line BTSC147 from a recurrent GBM, which is unlikely to represent primary GBMs. The analysis appears overly descriptive and fails to add significant information beyond the observation that mubritinib induces a proliferative arrest, as assessed in biological experiments. Additionally, the claim that the Neftel 'Neural Progenitor Cell' signature is altered in a biologically significant manner after only 24 hours of mubritinib treatment seems questionable. As such, this analysis should be moved to supplementary information. A more intriguing alternative would be to compare groups of BTSCs that exhibit high or low sensitivity to mubritinib and attempt to identify gene sets that can correlate with and possibly contribute to explain differences in drug sensitivity.

Major point N. 4

Figure 3. LDA need to be measured at longer timepoints (14-21 days vs. 7 days shown).

Major point N. 5

Supplementary Figure 3c aims to demonstrate that neural stem cells are unaffected by mubritinib merely by showing stem markers in western blots, which is insufficient. To provide convincing evidence, an LDA should be performed using human Neural Progenitor Cells.

Major Point N. 6

Page 9. The mechanistic nexus between OXPHOS inhibition and radiosensitization described by the authors remains unclear. In particular, the link between enrichment in OXPHOS proteins observed in recurrent vs.primary GBMs on the one hand, and downregulation of homologous recombination related-pathways on the other hand is difficult to grasp. The authors should endeavor to more clearly explain how mubritinib can interfere with the adaptive response to ionizing radiation, thereby providing a rationale for experiments combining the two treatments. As noted in the discussion (page 14), 'targeting mitochondrial respiration is an emerging strategy to overcome radioresistance in the tumour hypoxic areas'. Thus, a plausible mechanism of mubritinib-induced radiosensitization may involve reducing oxygen consumption, thereby leaving more oxygen available for diffusion and improving radiation response (by increasing generation of reactive oxygen species). To provide convincing mechanistic evidence, the authors should include in vitro experiments assessing the ability of mubritinib to radiosensitize BTSC in both normoxic and hypoxic conditions. LDA or radiobiological clonogenic assays showing the effect of combination treatment on stem cell frequency are recommended.

Major Point N. 7

Fig. 5d. Concerning the scheme of in vivo treatment, it is unclear why irradiation is administered 5 days after the beginning of mubritinib treatment, considering that mubritinib reaches its peak brain concentration much earlier, as shown in Fig. 4d. Furthermore, if mubritinib alone is effective against the tumor, comparing tumors that have been treated with IR alone at the same time-point as those treated with IR + mubritinib seems inappropriate. This is because, in the latter scenario, IR is applied to tumors that are likely reduced in volume compared to those treated with vehicle prior to IR. This discrepancy could introduce bias in the evaluation of the combined treatment's efficacy.

Major Point N. 8.

Figure 6b. The methodology employed to measure the effect of mubritinib on human neural progenitor cells should be the same as that used for BTSC. Moreover, a positive control (a treatment inducing death, such as bosentan for hepatocytes) needs to be added.

Minor points

Minor point N.1

Please use consistent units (nM or uM) for mubritinib.

Minor point N.2

ND1 expression in transduced cells should be shown by western blot (in Supplementary Figures).

Significance

This manuscript reports preclinical results on the use of mubritinib, a drug targeting the mithochondrial electron chain transport complex 1, to halt proliferation of glioblastoma (GBM) stem cells in vitro and treat experimental GBMs generated by stem cell transplantation. Given that the standard therapy for GBM still relies on a limited number of conventional options, evidence demonstrating the preclinical effectiveness of mubritinib could exert a significant translational impact. Mubritinib has not yet been proposed for GBM treatment, but there is convincing evidence that the drug may be effective in subsets of acute myeloid leukemia that rely on oxidative phosphorylation (Baccelli et al., Cancer Cell 36:84, 2019. PMID: 31287994). Data provided in this manuscript on potential effectiveness of mubritinib are overall convincing. However, in its current form, the manuscript present major limitations regarding the representativeness of models used, which do not support the claim that mubritinib could be universally useful in GBM, and regarding mechanistic aspects of mubritinib combination with radiotherapy. These and other aspects could be addressed through additional experiments.

The audience interested in the reported findings includes preclinical and clinical neuro-oncologists. My field of expertise is biology and genetics of glioblastoma stem cells and generation of in vitro and in vivo GBM preclinical models.

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Reply to the reviewers

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

Summary Maintenance of the histone H3 variant CENP-A at centromeres is necessary for proper kinetochore assembly and correct chromosome segregation. The Mis18 complex recruits the CENP-A chaperone HJURP to centromeres to facilitate CENP-A replenishment. Here the authors characterise the Mis18 complex using hybrid structural biology, and determine complex interface separation-of-function mutants.

Major Comments The SAXS and EM data on the full-length Mis18 components must be included in the main Figures, either as an additional figure or by merging/rearranging the existing figures. The authors discuss these results in three whole paragraphs, which are a very important part of the paper.

We thank the reviewer for this constructive suggestion. We have now included an additional figure (new Fig. 2, attached below), that highlights the fit of the integrative model against the SAXS and EM data.

Could the authors also compare the theoretical SAXS scattering curves generated by their final model(s) with the experimental SAXS curves? This would provide some additional evidence for the overall shape of their complex model beyond the consistency with the Dmax/Rg.

We acknowledge the importance of this suggestion. We have now compared the theoretical SAXS scattering curve of the Mis18a/b core complex (named Mis18a/b DN), which lacks the flexible elements (disordered regions and the helical region flexibility connected to the Yippee domains). The theoretically calculated SAXS scattering curve of the model matches nicely with the experimental data with c2 value of 1.36. This data is now included in new Fig. 2 (Fig. 2f) and is referenced on page 9 line 21.

Minor Comments

While the introduction is clearly written, an additional cartoon schematic, representing the system/question would be helpful to a non-specialist reader to interpret the context of the study.

We have now included a cartoon in the revised Fig. 1 to support the introduction on centromere maintenance and the central role of the Mis18a/b/BP1 complex in this process. Please find the new Fig. 1 below.

No doubt the authors had a reason for choosing their figure allocation, but I wonder if more material couldn't be brought from the supplementary into the main figures?

As addressed in our response to one of the major comments, we have now moved key CLMS, SAXS and EM data from the supplemental figure into the main figure, new Fig. 2.

Page 6 "Mis18-alpha possesses an additional alpha-helical domain" - please make it clear in addition to what (I assume it's in addition to Mis18-beta).

Apologies for the lack of clarity. We have now rephrased this sentence to highlight that this difference is in comparison with Mis18b on page 6 line 15.

Page 7 - Report the RMSD of the Pombe vs. Human Mis18-alpha yipee structures?

The S. pombe Mis18 Yippee structure superposes on to the Human Mis18a Yippee domain with an RMSD of 0.92 angstroms with is now mentioned on page 7 line 9.

Page 7 - "We generated high-confidence structural models...." is there a metric for the confidence as reported by RaptorX? Perhaps includinging the PAE plots in the supplementary for the AlphaFold generated models would be useful?

We thank the reviewer for the valid suggestion. We have now included the PAE plot corresponding to the AlphaFold model in the supplementary Fig. S1d and reference on page 7 line 18. RaptorX ranks models based on estimated error. We have now included this information in the new figure legend for Supplementary Fig. S1.

Figure 1 - Perhaps label figure 1b as being experimentally determined, with the R values (as for Figure 1d), and 1c being a predicted model.

We have included Rfree and Rwork values for the Mis18a Yippee homo dimer structure and labelled Mis18a/b Yippee hetero-dimer as the predicted model in Fig. 1c and 1d.

Page 8 "This observation is consistent with the theoretically calculated pI of the Mis18alpha helix" This is a circular argument, of course this region has a low pI due to the amino acid composition. Please remove this statement.

We have now removed this statement as suggested.

Page 8 "...reveals tight hydrophobic interactions" these are presumably shown in Figure 1d rather than in the referenced 1e.

We apologise for the oversight. We have now referred to the correct figure (Fig. 1f in the revised Fig. 1).

Page 8 - The authors should briefly somewhere discuss why there is a difference between their results and those in Pan et al 2009. As I understand it, the Pan et al paper was based in part on modelling with CLMS data as restraints.

We thank the reviewer for this suggestion. According to Pan et al., 2009, the model shown by them was generated using CCBuilder, and their CLMS data could not differentiate the two models with the 2nd Mis18a C-terminal helix in either parallel or anti-parallel orientation. We now briefly discuss this on page 8 and line 22 as follows: "Although the Pan et al., 2019 model presented the 2nd Mis18a in a parallel orientation, they did not rule out the possibility of this assembling in an anti-parallel orientation within the Mis18a/b C-terminal helical assembly (Pan et al., 2019)."

Figure 1 - The labelling of the residues for Mis18-alpha in Figure 1d is problematic, they are black on dark purple (might be my printer/screen/eyes) suggest amending.

We have now rearranged the label positions to overcome this issue. For clarity, the labels that could not be moved appropriately are shown in white.

Figure S3a - Do the authors have some data to show the mass of the cross-linked complex that was loaded onto grids is consistent with what is expected?

Unfortunately, the amount of material that we recover after performing GraFix is not sufficient enough to determine the molecular weight of the crosslinked sample by techniques such as SEC-MALS. However, GraFix fractions were analysed by SDS PAGE, and fractions that ran around the expected molecular weight were selected for EM analysis. We have now included the corresponding SDS-PAGE showing the migration of the crosslinked sample analysed by EM (Supplementary Fig. S3a).

Figure S3b - scale bar

Revised Fig. 2d now includes the scale bar shown.

Figure S3c - Could the authors show or explain the differences between these different 3D reconstructions?

The models mainly differ in the relative orientations of the bulkier structural features that are referred to as 'ear' and 'mouth' pieces of a telephone handset. This has been mentioned in the text, but we note that the figure is not referenced right next to this statement. We have now amended this (Page 9 line 19), and to make it clear, we have also highlighted the difference using an arrowhead in Fig. 2e and S3b. The different orientations are also stated in the corresponding figure legends.

Page 9 - The use of "AFM" for AlphaFoldMultimer" is a little confusing since AFM is the established acronym for Atomic Force Microscopy. Perhaps AF2M?

We have now replaced AFM with AF2M on page 9 to avoid confusion.

Figure S4a - Control missing for Mis18-alpha wild-type

Apology for the confusion, this control is present in Fig. 4a. We have now stated this in the figure legend of S4a for clarity.

Figure S4 d and e - The contrast between the bands and the background is very bad (at least in my copy).

We have now adjusted the contrast of the blots in Fig. S4d and S4e response to this comment.

Page 13 "Our structural analysis suggests that two Mis18BP1 fragments.....". How did you arrive at this conclusion? Is this based on the AlphaFold/RaptorX model? What additional evidence do you have that the positioning of the Mis18BP1 is correct? Does the CLMS data support this?

We confirm that this statement is based on AlphaFold model. We have now explicitly highlighted this on page 14, line 5. As noted in the same paragraph (page 14, line 19), this model agrees with the contacts suggested by the cross-linking mass spectrometry data presented here.

Figure 4a - Would the authors like to consider using a different colour for Mis18BP1? The contrast is not great, especially in the electrostatic surface inset.

In response to this suggestion, the Mis18BP1 helix is now shown in grey in the inset of Fig. 5a.

Reviewer #1 (Significance (Required)):

General Assessment The paper is extremely clearly written. Likewise the figures are beautifully presented and the data extremely clean and fully supportive of the authors conclusions. Indeed it is seldom that one sees the depth of the structural approaches (X-ray, CLMS, EM, SAXS) in one paper which is a huge strength of the manuscript. In addition the translation of this data into very clean cell biological experiments, makes the paper truly outstanding.

Advance The authors provide the first model of the Mis18 complex, with extensive evidence to back up this model. The authors provide additional evidence as to how the deposition/renewal of CENP-A might be mediated by the Mis18 complex. The advance comes from both the level of clarity, detail, and scope achieved in this paper.

Audience This will likely be of great interest to anyone with an interest in chromosome biology, plus be of interest to structural biologists as an outstanding example of hybrid structural biology.

Expertise I am a biochemist with a background in structural biology with some familiarity with centromere biology

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

Summary: The manuscript "structural basis for Mis18 complex assembly: implications for centromere maintenance" by Thamkachy and colleagues describes a study that uses structural analysis to test essential candidate residues in Mis18 complex components in CENP-A loading. For chromosomes to faithfully segregate during cell division, CENP-A levels must be maintained at the centromere. How CENP-A levels are maintained is therefore important to understand at the mechanistic level. The Mis18 complex has been found to be important, but how exactly the various Mis18 complex components interact and how they regulate new CENP-A loading remains not fully understood. This study set out to characterize the critical residues using X-ray crystallography, negative staining EM, SEC analysis, molecular modeling (Raptorx, AlphaFold2, and AlphaFold-multimer) to identify the residues of Mis18a and Mis18b that are critical for the formation of the Mis18a/b hetero-hexamer and which residues are important for Mis18a and Mis18BP1 interactions. A complex beta-sheet interface dictates the Mis18a and Mis18b interactions. Mutating the Mis18a residues that are important for the Mis18a/b interactions resulted in impaired pull-down of Mis18b and reduced centromeric levels of mutated Mis18a. The functional consequences of mutating residues that impair Mis18a/b interactions is that with reduced centomeric levels of Mis18a, also impaired new CENP-A loading. Interestingly, mutated Mis18b did not impact centromeric Mis18a levels and only modestly impaired new CENP-A loading. These data were interpreted that Mis18a is critical for new CENP-A loading, whereas Mis18b might be involved in finetuning how much new CENP-A is loaded. Overall, it is a very well described and well written study with exciting data.

Major comments:

• Overall, the structural data and the IF data support the importance of Mis18a residues 103-105 are critical for centromeric localization and new CENP-A loading, whereas Mis18b residues L199 and I203 are critical for centromeric localization, but only very modestly impair centromeric Mis18a localization and new CENP-A loading. In the discussion the authors argue that the N-terminal helical region of Mis18a mediate HJURP binding. This latter is postulated based on published work, but not tested in this work. This should be clarified as such.

We thank the reviewer for this comment. Our very recent study aimed at understanding the licencing role of Plk1, independent of the work reported here, serendipitously has now validated this suggestion and demonstrates that a Plk1-mediated phosphorylation cascade activates the Mis18a/b complex via a conformational switch of the N-terminal helical region of Mis18a, which facilitates a robust HJURP-Mis18a/b interaction (Parashara et al. bioRxiv 2024). An independent study from the Musacchio lab (Conti et al. bioRxiv, 2024) also reports similar findings, mutually strengthening our independent conclusions. Overall, these studies highlight the importance of the critical structural insights into the Mis18 complex this study reports. We now explicitly discuss the validation of our original hypothesis by citing our recent work along with that of the Musacchio lab. The corresponding section of the last paragraph now reads as follows (page 17 line 10): "Previously published work identified amino acid sequence similarity between the N-terminal region of Mis18a and R1 and R2 repeats of the HJURP that mediates Mis18a/b interaction (Pan et al., 2019). Deletion of the Mis18a N-terminal region enhanced HJURP interaction with the Mis18 complex (Pan et al., 2019). Here, we show that the N-terminal helical region of Mis18a makes extensive contact with the C-terminal helices of Mis18a and Mis18b, which had previously been shown to mediate HJURP binding by Pan et al., 2019. Collectively these observations suggest that the N-terminal region of Mis18a might directly interfere with HJURP - Mis18 complex interaction. Two independent recent studies (Parashara et al., 2024, Conti et al., 2024) reveal that this is indeed the case and a Plk1-mediated phosphorylation cascade involving several phosphorylation and binding events of the Mis18 complex subunits relieve the intramolecular interactions between the Mis18a N-terminal helical region and the HJURP binding surface of the Mis18a/b C-terminal helical bundle. This facilitates robust HJURP-Mis18a/b interaction in vitroand efficient HJURP centromere recruitment and CENP-A loading in cells. Overall, these studies also highlight the importance of the critical structural insights into the Mis18 complex we report here."

• Overall, the authors clearly describe their data and methodology and use adequate statistical analyses. The structural data of the Mis18a/b complex being a hetero-hexamer is convincing, but the validation in vivo is missing. As structural experiment are not performed under physiological conditions, it is important to establish the stoichiometry in vivo to further support the totality of the findings of the structural experiments and modeling. The data for the hierarchical assembly of Mis18a and Mis18b at the centromere and its importance in new CENP-A loading is convincing. An additional open question is whether "old" centromeric CENP-A or HJURP:new CENP-A complex is needed to recruit Mis18a to the centromere and whether the identified residues have a role in Mis18a centromeric localization. These data would provide a solid link between the Mis18 complex and how it is directly linked to new CENP-A loading.

We agree that establishing the stoichiometry of Mis18 subunits of the Mis18 complex in vivo would be insightful. However, considering that the Mis18 complex assembles in a specific window of the cell cycle (late Mitosis and early G1), we think characterising the stoichiometry in cells is extremely difficult and technically challenging. However, consistent with our structural model, several lines of independent evidence (Pan et al., 2017 and Spiller et al., 2017) using different biophysical methods (Analytical Ultra Centrifugation (Pan et al., 2017), SEC-MALS (Spiller et al., 2017)) showed that recombinantly purified Mis18 complex (irrespective of the expression host, from both E. Coli or insect cells) is a hetero-octamer made of a hetero-hexameric Mis18a/b (4 Mis18a and 2 Mis18 b) complex bound to two copies of Mis18BP1. These observations suggested that hetero-hexamerisation of the Mis18a/b complex may be needed to bind and dimerise Mis18BP1 in cells. Previously published cellular studies support the in vivo requirement of the hetero-octameric Mis18 assembly as: (i) Perturbing the hetero-hexamerisation of the Mis18a/b complex (by introducing mutations at the Mis18a/b Yippee dimerisation interface, which while did not disrupt Mis18a/b complex formation, perturbed its hetero-hexamerisation and resulted in a hetero-trimeric Mis18a/b complex made of 2 Mis18aand 1 Mis18b) abolished Mis18BP1 binding in vitro and in cells, consequently abolished CENP-A deposition (Spiller et al., 2017) and (ii) artificial dimerisation of Mis18BP1, by expressing Mis18BP1 as a GST-tagged protein, enhanced the centromere localisation of Mis18BP1 highlighting the requirement of Mis18a/b hexameric assembly mediated dimerization of Mis18BP1 in cells (Pan et al., 2017). While these studies highlighted the importance of maintaining the right stoichiometry (hetero-octamer of 4 Mis18a, 2 Mis18b and 2 Mis18BP1), lack of structural information on how this essential biological assembly is established remained a major knowledge gap. Our work presented here fills this critical knowledge gap by showing that a segment of Mis18BP1 (aa 20-51) also binds at the Yippee dimerisation interface. To highlight this, we have included the following statements in the introduction on page 5 and 20 "Perturbing the Yippee domain-mediated hexameric assembly of Mis18a/b (that resulted in a Mis18a/b hetero-trimer, 2 Mis18a and 1 Mis18b) abolished its ability to bind Mis18BP1 in vitro and in cells (Spiller et al., 2017), emphasising the requirement of maintaining correct stoichiometry of Mis18a/b subunits. Consistent with this, artificial dimerisation of Mis18BP1, by expressing Mis18BP1 as a GST-tagged protein, enhanced the centromere localisation of Mis18BP1 (Pan et al., 2017)." and in the Results section on page 14 line 12: "Mis18BP120-51 contains two short b strands that interact at Mis18a/b Yippee interface extending the six-stranded-b sheets of both Mis18a and Mis18b Yippee domains. This provides the structural rationale for why Yippee domains-mediated Mis18a/b hetero-hexamerisation is crucial for Mis18BP1 binding (Spiller et al., 2017)."

Regarding the question "whether 'old' centromeric CENP-A or HJURP:new CENP-A complex is needed to recruit Mis18a centromere localisation and whether identified residues have a role in Mis18a centromere localisation": According to the published literature, the Mis18 complex associates with centromeres through interaction with CCAN components CENP-C and CENP-I (Shono et al., 2015, Dambacher et al., 2012, Moree et al., 2011, Hoffmann et al., 2020). Considering CCAN assembles on CENP-A nucleosomes, and HJURP:new CENP-A centromere recruitment depends on the Mis18 complex, it will be reasonable to argue that the 'old' centromeric CENP-A contributes to the centromere localisation of the Mis18 complex. Amongst the components of the Mis18 complex, Mis18BP1 and Mis18bhave previously been suggested to interact with CENP-C. Within the Mis18 complex, we (Spiller et al., 2017) and others (Pan et al., 2017) have shown that Mis18a can directly interact with Mis18BP1, but it does so more efficiently when Mis18a hetero-oligomerises with Mis18b via their Yippee domains. Here, our structural analysis mapped the interaction interfaces and showed that Mis18a residues E103, D104 and T105 contribute to Mis18BP1 binding, as mutating these residues abolishes centromere localisation of Mis18a (Fig. 5c and 5d). To accentuate our findings, we have now included the following paragraph in the discussion section (page 17 line 26): "One of the key outstanding questions in the field is how does the Mis18 complex associate with the centromere. Previous studies identified CCAN subunits CENP-C and CENP-I as major players mediating the centromere localisation of the Mis18 complex mainly via Mis18BP1 (Shono et al., 2015, Dambacher et al., 2012, Moree et al., 2011), although Mis18b subunit has also been suggested to interact with CENP-C (Stellfox et al., 2016). Within the Mis18 complex, we and others have shown that the Mis18a/b Yippee hetero-dimers can directly interact with Mis18BP1. Here our structural analysis allowed us to map the interaction interface mediating Mis18a/b-Mis18BP1 binding. Perturbing this interface on Mis18a completely abolished Mis18a centromere localisation and reduced Mis18BP1 centromere levels. These observations show that Mis18a associates with the centromere mainly via Mis18BP1, and assembly of the Mis18 complex itself is crucial for its efficient centromere association, as previously suggested. Future work aimed at characterising the intermolecular contact points between the subunits of the Mis18 complex, centromeric chromatin and CCAN components and understanding if the Mis18 complex undergoes any conformational and/or compositional variations upon centromere association and/or during CENP-A deposition process, will be crucial to delineate the mechanisms underpinning the centromere maintenance."

Minor comments:

• The bar graphs shown ideally also show the individual data points for the authros to appreciate the spread of the data. These figures can be replicated in the Supplemental to avoid making the main figures look too busy.

We thank the reviewers for this suggestion. Reviewer #3 made a similar comment and suggested we use Superplot, which allows visualisation of individual data points of independent experiments. We have now revised all bar graphs using Superplot to address both reviewers' suggestions.

Reviewer #2 (Significance (Required)):

• This study uses a broad range of structural techniques, including molecular modeling which were subsequently validated by in vitro pull-down assays, co-IP, and IF. This combination of these techniques is important because many structural techniques cannot be performed under physiological conditions. Validating the main findings of the structural results by IF and co-IP is therefore critical.
• This work greatly advances our structural understanding how Mis18a, Mis18b, and Mis18BP1 form the Mis18 complex and how the critical residues in especially Mis18a help the Mis18 complex localize to the centromere and influence new CENP-A loading. This study also provides the first strong evidence in hierarchical assembly of the Mis18 complex.
• How centromere identity is maintained is a critical question in chromosome biology and genome integrity. The Mis18 complex has been identified as an important complex in the process. Several structural and mutational studies (all adequately cited in this manuscript) have tried to address which residues guide the assembly and functional regions of the Mis18 complex. This work builds and expands our understanding how especially Mis18a holds a pivotal role in both Mis18 complex formation and its impact on maintaining centromeric CENP-A levels.
• This work will be of interest to the chromosome field in general and anyone studying the mechanism of cell division.
• Chromatin, centromere, CENP-A, cell division. This reviewer has limited expertise in structural biology.

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

Centromere identity is defined by CENP-A loading to specific sites on genomic DNA. CENP-A loading is known to rely on the Mis18 complex, and several regulators are known; yet how the Mis18 complex achieves this complex process has remained puzzle. By elucidating the structural basis of Mis18 complex assembly using integrative structural approaches the authors show that multiple homo and heterodimeric interfaces of Mis18alpha, beta and Mis18BP1 are involved in centromere maintenance. The authors show that Mis18alpha can associate with centromeres and deposit CENP-A independent of Mis18 β. Mis18α functions in CENP-A deposition at centromeres independent of Mis18β. Mis18β is required for maintaining a specific level of CENP-A occupancy at centromeres. Thus, using structure-guided and separation-of-function mutants the study reveals how Mis18 complex ensures centromere maintenance. Major comments: This is an excellent study on centromere inheritance, combining structural and cell biology techniques. The comments here primarily refer to Cell biology aspect of the work.

Figures show that new CENP-A deposits in Mis18βL199D/I203D mutants, but the level was reduced moderately. Based on this observation, the authors make a strong conclusion that Mis18β licenses the optimal levels of CENP-A at centromeres. Mis18α may be essential for both CENP-A incorporation and depositing a specific amount of CENP-A, as Mis18α and CENP-A levels are both reduced in Mis18βL199D/I203D mutants which failed to form the triple helical assembly with Mis18α as shown in Figure 3B and 3C. The authors may want to qualify some of these claims as preliminary or speculative.

We thank the reviewer for this suggestion. We agree that although the reduction in CENP-A levels upon replacing WT Mis18b with Mis18b L199D/I203D is more prominent than the reduction in centromere localised Mis18a, one cannot completely rule out the contribution of reduced Mis18a on CENP-A loading. This also raises an interesting possibility where Mis18b ensures the correct amount of CENP-A deposition by facilitating the optimal level of Mis18a at centromeres. We now explicitly discuss this in the discussion as follows (page 16 line 26): "Whilst proteins involved in CENP-A loading have been well established, the mechanism by which the correct levels of CENP-A are controlled is yet to be thoroughly explored and characterised. The data presented here suggest that Mis18b mainly contributes to the quantitative control of centromere maintenance - by ensuring the right amounts of CENP-A deposition at centromeres - and maybe one of several proteins that control CENP-A levels. We also note that the Mis18b mutant, which cannot interact with Mis18a, moderately reduced Mis18a levels at centromeres, and hence, it is possible that Mis18b ensures the correct level of CENP-A deposition by facilitating optimal Mis18a centromere recruitment. Future studies will focus on dissecting the mechanisms underlying the Mis18b-mediated control of CENP-A loading amounts along with any other mechanisms involved."

This work and others show that phosphorylation of Mis18BP1 by CDK1 can interfere with complex function (Spiller et al., 2017, Pan et al., 2017). Does the structure provide any insight into PLK1-mediated phosphorylation surfaces for activation of the complex? If yes, a brief discussion would help to link CDK1 and PLK1 mediated opposing actions will strengthen the work.

As described in our response to the first major comment of Reviewer 2, our very recent study aimed at understanding the licencing role of Plk1, independent of the work reported here, identified and evaluated the functional contribution of Plk1 phosphorylation on the subunits of the Mis18 complex (Parashara et al., bioRxiv 2024). Serendipitously, this recent work has now validated our hypothesis proposed based on the structural characterisation reported here and demonstrates that a Plk1-mediated phosphorylation cascade activates the Mis18a/b complex via a conformational switch of the N-terminal helical region of Mis18a which facilitates a robust HJURP-Mis18a/b interaction (Parashara et al. bioRxiv 2024). An independent study from the Musacchio lab (Conti et al., bioRxiv 2024) also reports similar findings, mutually strengthening our independent conclusions. Overall, these studies highlight the importance of the critical structural insights into the Mis18 complex this study reports. We now explicitly discuss the validation of our original hypothesis by citing our recent work along with that of the Musacchio lab. The corresponding section of the last paragraph now reads as follows (page 17 line 10): "Previously published work identified amino acid sequence similarity between the N-terminal region of Mis18a and R1 and R2 repeats of the HJURP that mediates Mis18a/binteraction (Pan et al., 2019). Deletion of the Mis18a N-terminal region enhanced HJURP interaction with the Mis18 complex (Pan et al., 2019). Here, we show that the N-terminal helical region of Mis18a makes extensive contact with the C-terminal helices of Mis18a and Mis18b, which had previously been shown to mediate HJURP binding by Pan et al., 2019. Collectively these observations suggest that the N-terminal region of Mis18a might directly interfere with HJURP - Mis18 complex interaction. Two independent recent studies (Parashara et al., 2024, Conti et al., 2024) reveal that this is indeed the case and a Plk1-mediated phosphorylation cascade involving several phosphorylation and binding events of the Mis18 complex subunits relieve the intramolecular interactions between the Mis18a N-terminal helical region and the HJURP binding surface of the Mis18a/b C-terminal helical bundle. This facilitates robust HJURP-Mis18a/b interaction in vitro and efficient HJURP centromere recruitment and CENP-A loading in cells. Overall, these studies also highlight the importance of the critical structural insights into the Mis18 complex we report here."

I am happy with the way cell biology data and the methods are presented so that they can be reproduced. The experiments are adequately replicated and the statistical analysis adequate. It will help to include sample size of cells or centromeres used for building the graphs.

We have now included this information in figure legends of Fig. 3a, 3c, 4b, 4c, 5b, 5c and 5d.

This is a strong interdisciplinary study using a variety of in vitro and in vivo techniques. Can the authors discuss if they expect chromatin associated Mis18 complex to host a similar structure as the soluble one? In other words, are they able to comment on any key differences between chromatin and non-chromatin associated Mis18 complexes.

We thank the reviewer for the suggestion. We agree that one cannot rule out the possibility of the Mis18 complex undergoing compositional and/or conformational variations during the processes of CENP-A loading at centromeres. We now explicitly discuss this possibility in the last paragraph of the discussion section (page 18 line 10): "Future work aimed at characterising the intermolecular contact points between the subunits of the Mis18 complex, centromeric chromatin and CCAN components and understanding if the Mis18 complex undergoes any conformational and/or compositional variations upon centromere association and/or during CENP-A deposition process, will be crucial to delineate the mechanisms underpinning the centromere maintenance."

Minor comments: -

In cell biology experiments, fluorescence intensities could be presented as a superplot for added value across cells and repeats (instead of bar graphs). More on superplot:https://doi.org/10.1083/jcb.202001064.

We thank the reviewers for this kind suggestion. We have now included graphs made using 'superplot' as suggested.

In general, ACA levels do not appear to change significantly between WT and mutant expressing cells although new CENP-A loading is significantly absent in the presence of a few mutants - please comment if ACA used here can recognise CENP-A. Would this mean that old CENP-A remains normally?

We thank the reviewer for this comment. While new CENP-A incorporated at centromeres is selectively labelled using the SNAP-tag, the ACA antibody used in these experiments can recognise CENP-A, CENP-B and CENP-C, with CENP-B being the primary target (Kallenberg, Clinical Rheumatology,1990). We would also like to note that ACA has commonly been used to locate the centromere in CENP-A loading assays where new CENP-A levels are assessed via selective labelling (e.g. McKinley 2014).

It is unclear whether any of the mutant acted in a dominant negative fashion in the presence of endogenous Mis18 proteins. It would have been useful to test this particularly in the context of mis18alpha mutants that seem to fully abolish new CENP-A recruitment.

As Mis18 subunits oligomerise (homo and hetero), we thought expressing these mutants in the presence of endogenous proteins might interfere with endogenous protein in a heterogenous manner and might make the interpretation difficult. Hence, we did not test this. Instead, as described in the manuscript we have tested these mutants in siRNA rescue experiments (Fig. 3, 4 and 5).

In figure 3a, GFP panel (input lane, 1) is shown to mark a band corresponding to GFP. Is this expected? Please comment.

Yes, as a control, an empty vector was transfected to express just GFP along with Mis18a-mCherry. These were used to show that there was no unspecific interaction between the beads used for IP or Mis18a-mCherry and GFP tag, and that any interaction seen was due to Mis18b. A similar control was used in S4b, where mCherry was expressed along with Mis18b-GFP. We have now clarified this in the corresponding legends of Fig. 4a and S4b.

Would be useful to have the scale for the cropped images presented as insets. Figure 4B should read YFP and not YPF.

We apologise for this typographical error. We have now corrected this.

The authors may want to explain whether the tag differences matter for their study (Case in point: His-SUMO-Mis18a191-233 WT and mutant His-MBP-Mis18b188-229 proteins).

The MBP tag was chosen to perform amylose pull-down assays, whereas the SUMO tag was chosen to increase the protein size. This is crucial as the C-terminal fragments of Mis18a and Mis18b are less than 50 amino acids long and are not easy to visualise by the band intensity in the Coomassie-stained SDS PAGE gels.

Reviewer #3 (Significance (Required)):

This work elucidates the structural basis of Mis18 complex assembly and the intermolecular interfaces essential for Mis18 functions. This is a significant advance in the field as it helps researchers in the field better understand CENP-A deposition and mechanism underpinning the maintenance of centromere identity. This is a broad area of research benefitting those studying cell division, genome stability, centromere identity and epigenetics might all be interested in and influenced by these findings. Novelty and strength lies in combining structural and cell biology work. Strengths of the work are structural details of the Mis18 complex. Minor weakness is the link between Mis18 structure and Centromere inheritance is limited to one immunostaining assay (I have mentioned this as a minor comment because addressing this may not be within the scope of this manuscript and is likely to require a repeat of a vast majority of the work with additional reagents which may not directly add value to the current manuscript).

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

Centromere identity is defined by CENP-A loading to specific sites on genomic DNA. CENP-A loading is known to rely on the Mis18 complex, and several regulators are known; yet how the Mis18 complex achieves this complex process has remained puzzle. By elucidating the structural basis of Mis18 complex assembly using integrative structural approaches the authors show that multiple homo and heterodimeric interfaces of Mis18alpha, beta and Mis18BP1 are involved in centromere maintenance. The authors show that Mis18alpha can associate with centromeres and deposit CENP-A independent of Mis18 β. Mis18α functions in CENP-A deposition at centromeres independent of Mis18β. Mis18β is required for maintaining a specific level of CENP-A occupancy at centromeres. Thus, using structure-guided and separation-of-function mutants the study reveals how Mis18 complex ensures centromere maintenance.

Major comments:

This is an excellent study on centromere inheritance, combining structural and cell biology techniques. The comments here primarily refer to Cell biology aspect of the work.

1. Figures show that new CENP-A deposits in Mis18βL199D/I203D mutants, but the level was reduced moderately. Based on this observation, the authors make a strong conclusion that Mis18β licenses the optimal levels of CENP-A at centromeres. Mis18α may be essential for both CENP-A incorporation and depositing a specific amount of CENP-A, as Mis18α and CENP-A levels are both reduced in Mis18βL199D/I203D mutants which failed to form the triple helical assembly with Mis18α as shown in Figure 3B and 3C. The authors may want to qualify some of these claims as preliminary or speculative.
2. This work and others show that phosphorylation of Mis18BP1 by CDK1 can interfere with complex function (Spiller et al., 2017, Pan et al., 2017). Does the structure provide any insight into PLK1-mediated phosphorylation surfaces for activation of the complex? If yes, a brief discussion would help to link CDK1 and PLK1 mediated opposing actions will strengthen the work.
3. I am happy with the way cell biology data and the methods are presented so that they can be reproduced. The experiments are adequately replicated and the statistical analysis adequate. It will help to include sample size of cells or centromeres used for building the graphs.
4. This is a strong interdisciplinary study using a variety of in vitro and in vivo techniques. Can the authors discuss if they expect chromatin associated Mis18 complex to host a similar structure as the soluble one? In other words, are they able to comment on any key differences between chromatin and non-chromatin associated Mis18 complexes.

Minor comments:

In cell biology experiments, fluorescence intensities could be presented as a superplot for added value across cells and repeats (instead of bar graphs). More on superplot: https://doi.org/10.1083/jcb.202001064. In general, ACA levels do not appear to change significantly between WT and mutant expressing cells although new CENP-A loading is significantly absent in the presence of a few mutants - please comment if ACA used here can recognise CENP-A. Would this mean that old CENP-A remains normally?

It is unclear whether any of the mutant acted in a dominant negative fashion in the presence of endogenous Mis18 proteins. It would have been useful to test this particularly in the context of mis18alpha mutants that seem to fully abolish new CENP-A recruitment.

In figure 3a, GFP panel (input lane, 1) is shown to mark a band corresponding to GFP. Is this expected? Please comment. Would be useful to have the scale for the cropped images presented as insets.

Figure 4B should read YFP and not YPF.

The authors may want to explain whether the tag differences matter for their study (Case in point: His-SUMO-Mis18a191-233 WT and mutant His-MBP-Mis18b188-229 proteins).

Significance

This work elucidates the structural basis of Mis18 complex assembly and the intermolecular interfaces essential for Mis18 functions. This is a significant advance in the field as it helps researchers in the field better understand CENP-A deposition and mechanism underpinning the maintenance of centromere identity. This is a broad area of research benefitting those studying cell division, genome stability, centromere identity and epigenetics might all be interested in and influenced by these findings. Novelty and strength lies in combining structural and cell biology work.

Strengths of the work are structural details of the Mis18 complex. Minor weakness is the link between Mis18 structure and Centromere inheritance is limited to one immunostaining assay (I have mentioned this as a minor comment because addressing this may not be within the scope of this manuscript and is likely to require a repeat of a vast majority of the work with additional reagents which may not directly add value to the current manuscript).

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript "structural basis for Mis18 complex assembly: implications for centromere maintenance" by Thamkachy and colleagues describes a study that uses structural analysis to test essential candidate residues in Mis18 complex components in CENP-A loading. For chromosomes to faithfully segregate during cell division, CENP-A levels must be maintained at the centromere. How CENP-A levels are maintained is therefore important to understand at the mechanistic level. The Mis18 complex has been found to be important, but how exactly the various Mis18 complex components interact and how they regulate new CENP-A loading remains not fully understood. This study set out to characterize the critical residues using X-ray crystallography, negative staining EM, SEC analysis, molecular modeling (Raptorx, AlphaFold2, and AlphaFold-multimer) to identify the residues of Mis18a and Mis18b that are critical for the formation of the Mis18a/b hetero-hexamer and which residues are important for Mis18a and Mis18BP1 interactions. A complex beta-sheet interface dictates the Mis18a and Mis18b interactions. Mutating the Mis18a residues that are important for the Mis18a/b interactions resulted in impaired pull-down of Mis18b and reduced centromeric levels of mutated Mis18a. The functional consequences of mutating residues that impair Mis18a/b interactions is that with reduced centomeric levels of Mis18a, also impaired new CENP-A loading. Interestingly, mutated Mis18b did not impact centromeric Mis18a levels and only modestly impaired new CENP-A loading. These data were interpreted that Mis18a is critical for new CENP-A loading, whereas Mis18b might be involved in finetuning how much new CENP-A is loaded. Overall, it is a very well described and well written study with exciting data.

Major comments:

• Overall, the structural data and the IF data support the importance of Mis18a residues 103-105 are critical for centromeric localization and new CENP-A loading, whereas Mis18b residues L199 and I203 are critical for centromeric localization, but only very modestly impair centromeric Mis18a localization and new CENP-A loading. In the discussion the authors argue that the N-terminal helical region of Mis18a mediate HJURP binding. This latter is postulated based on published work, but not tested in this work. This should be clarified as such.
• Overall, the authors clearly describe their data and methodology and use adequate statistical analyses. The structural data of the Mis18a/b complex being a hetero-hexamer is convincing, but the validation in vivo is missing. As structural experiment are not performed under physiological conditions, it is important to establish the stoichiometry in vivo to further support the totality of the findings of the structural experiments and modeling. The data for the hierarchical assembly of Mis18a and Mis18b at the centromere and its importance in new CENP-A loading is convincing. An additional open question is whether "old" centromeric CENP-A or HJURP:new CENP-A complex is needed to recruit Mis18a to the centromere and whether the identified residues have a role in Mis18a centromeric localization. These data would provide a solid link between the Mis18 complex and how it is directly linked to new CENP-A loading.

Minor comments:

• The bar graphs shown ideally also show the individual data points for the authors to appreciate the spread of the data. These figures can be replicated in the Supplemental to avoid making the main figures look too busy.

Significance

• This study uses a broad range of structural techniques, including molecular modeling which were subsequently validated by in vitro pull-down assays, co-IP, and IF. This combination of these techniques is important because many structural techniques cannot be performed under physiological conditions. Validating the main findings of the structural results by IF and co-IP is therefore critical.
• This work greatly advances our structural understanding how Mis18a, Mis18b, and Mis18BP1 form the Mis18 complex and how the critical residues in especially Mis18a help the Mis18 complex localize to the centromere and influence new CENP-A loading. This study also provides the first strong evidence in hierarchical assembly of the Mis18 complex.
• How centromere identity is maintained is a critical question in chromosome biology and genome integrity. The Mis18 complex has been identified as an important complex in the process. Several structural and mutational studies (all adequately cited in this manuscript) have tried to address which residues guide the assembly and functional regions of the Mis18 complex. This work builds and expands our understanding how especially Mis18a holds a pivotal role in both Mis18 complex formation and its impact on maintaining centromeric CENP-A levels.
• This work will be of interest to the chromosome field in general and anyone studying the mechanism of cell division.
• Chromatin, centromere, CENP-A, cell division. This reviewer has limited expertise in structural biology.

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Referee #1

Evidence, reproducibility and clarity

Summary

Maintenance of the histone H3 variant CENP-A at centromeres is necessary for proper kinetochore assembly and correct chromosome segregation. The Mis18 complex recruits the CENP-A chaperone HJURP to centromeres to facilitate CENP-A replenishment. Here the authors characterise the Mis18 complex using hybrid structural biology, and determine complex interface separation-of-function mutants.

Major Comments

The SAXS and EM data on the full-length Mis18 components must be included in the main Figures, either as an additional figure or by merging/rearranging the existing figures. The authors discuss these results in three whole paragraphs, which are a very important part of the paper.

Could the authors also compare the theoretical SAXS scattering curves generated by their final model(s) with the experimental SAXS curves? This would provide some additional evidence for the overall shape of their complex model beyond the consistency with the Dmax/Rg.

Minor Comments

While the introduction is clearly written, an additional cartoon schematic, representing the system/question would be helpful to a non-specialist reader to interpret the context of the study.

No doubt the authors had a reason for choosing their figure allocation, but I wonder if more material couldn't be brought from the supplementaries into the main figures?

Page 6 "Mis18-alpha possesses an additional alpha-helical domain" - please make it clear in addition to what (I assume it's in addition to Mis18-beta).

Page 7 - Report the RMSD of the Pombe vs. Human Mis18-alpha yipee structures?

Page 7 - "We generated high-confidence structural models...." is there a metric for the confidence as reported by RaptorX? Perhaps includinging the PAE plots in the supplementary for the AlphaFold generated models would be useful?

Figure 1 - Perhaps label figure 1b as being experimentally determined, with the R values (as for Figure 1d), and 1c being a predicted model.

Page 8 "This observation is consistent with the theoretically calculated pI of the Mis18alpha helix" This is a circular argument, of course this region has a low pI due to the amino acid composition. Please remove this statement.

Page 8 "...reveals tight hydrophobic interactions" these are presumably shown in Figure 1d rather than in the referenced 1e.

Page 8 - The authors should briefly somewhere discuss why there is a difference between their results and those in Pan et al 2009. As I understand it, the Pan et al paper was based in part on modelling with CLMS data as restraints.

Figure 1 - The labelling of the residues for Mis18-alpha in Figure 1d is problematic, they are black on dark purple (might be my printer/screen/eyes) suggest amending.

Figure S3a - Do the authors have some data to show the mass of the cross-linked complex that was loaded onto grids is consistent with what is expected?

Figure S3b - scale bar

Figure S3c - Could the authors show or explain the differences between these different 3D reconstructions?

Page 9 - The use of "AFM" for AlphaFoldMultimer" is a little confusing since AFM is the established acronym for Atomic Force Microscopy. Perhaps AF2M?

Figure S4a - Control missing for Mis18-alpha wild-type

Figure S4 d and e - The contrast between the bands and the background is very bad (at least in my copy).

Page 13 "Our structural analysis suggests that two Mis18BP1 fragments.....". How did you arrive at this conclusion? Is this based on the AlphaFold/RaptorX model? What additional evidence do you have that the positioning of the Mis18BP1 is correct? Does the CLMS data support this?

Figure 4a - Would the authors like to consider using a different colour for Mis18BP1? The contrast is not great, especially in the electrostatic surface inset.

Significance

General Assessment

The paper is extremely clearly written. Likewise the figures are beautifully presented and the data extremely clean and fully supportive of the authors conclusions. Indeed it is seldom that one sees the depth of the structural approaches (X-ray, CLMS, EM, SAXS) in one paper which is a huge strength of the manuscript. In addition the translation of this data into very clean cell biological experiments, makes the paper truly outstanding.

Advance

The authors provide the first model of the Mis18 complex, with extensive evidence to back up this model. The authors provide additional evidence as to how the deposition/renewal of CENP-A might be mediated by the Mis18 complex. The advance comes from both the level of clarity, detail, and scope achieved in this paper.

Audience

This will likely be of great interest to anyone with an interest in chromosome biology, plus be of interest to structural biologists as an outstanding example of hybrid structural biology.

Expertise

I am a biochemist with a background in structural biology with some familiarity with centromere biology

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Reply to the reviewers

Reply to the Reviewers

We would like to thank the reviewers for their insightful comments, which will significantly guide us in enhancing our manuscript. We are capable of addressing most of the concerns raised by the reviewers. However, we encounter limitations in addressing Reviewer 2's comment regarding the delineation between cell autonomy and non-autonomy. As highlighted by the reviewer, ideally, we would dissect the mechanisms underlying cell turnover within the M/+ wing pouch, particularly in terms of cell autonomy and non-autonomy. Unfortunately, clonal analysis is not feasible due to the 'salt and pepper' distribution pattern of cell death and subsequent proliferation within the M/+ wing pouch. Despite these challenges, we commit to making efforts to address these issues to the best of our ability. Furthermore, we will aim to present our findings with greater precision and without speculation, an approach we believe will significantly enhance the quality of our manuscript.

In this manuscript, we extend the insights gained from our previous study (Akai et al., PLOS Genetics, 2021) by uncovering a novel mechanism within the context of the M/+ mutant. We demonstrate that JNK-dependent exocytosis in dying cells is crucial for cell turnover in the M/+ wing pouch. This phenomenon of cell turnover, initiated by cell death and the following proliferation, is fundamental to a variety of processes in multicellular organisms, such as normal development, tissue homeostasis, wound healing, tumor development, and potentially tumor recurrence. While our analysis is specific to the M/+ mutant, the underlying mechanisms of cell-cell communication between dying and proliferating cells, which are still not fully understood, may have broader implications. Our findings offer significant contributions to the field of cell competition and suggest a framework for understanding the operating principles of multicellular communities through cell-cell communications. Although it is yet to be determined how these insights apply in various contexts, they possess the potential to guide future research.

Referee #1

It would be important to check how much JNK is sufficient to trigger the exocytosis upregulation. Is the accumulation of Cyt1 and CD63 vesicles in apoptotic cell common to any JNK dependent death or does it require the Minute background? Could the authors check whether clones expressing HepCA transiently in WT background also accumulate the same vesicles?

Response:

Following the reviewer's suggestion, we plan to examine whether the accumulation of Syt1- and CD63-positive vesicles in apoptotic cells is a general characteristic of JNK-dependent cell death or requires the Minute background. Specifically, we intend to check whether mitotic clones expressing HepCA in the wild-type eye-antennal disc to see if these vesicles also accumulate. Additionally, we will assess mitotic clones expressing Eiger in the wild-type eye-antennal disc, which activates JNK signaling. This is due to concerns that HepCA may induce cell death too strongly, potentially resulting in clones too small for effective analysis. Moreover, we also plan to express HepCA transiently only in the posterior region of the wing disc to further explore its effects.

1. It would be relevant to have the status of JNK in Minute disc upon downregualtion of exocytosis. One could imagine some positive feedback between JNK activation, exocytosis, cell death and further JNK activation.

Response:

We thank the reviewer for the comment. As pointed out by the reviewer, there could be a positive feedback loop involving JNK activation, exocytosis, cell death, and further JNK activation. Our observations lend support to this hypothesis, as we specifically noted a significant reduction in the number of JNK-activating cells following targeted rab3 knockdown in these cells using puc-gal4 driver within the RpS3/+ wing disc (Fig R1, below). To further confirm the positive feedback loop between JNK activation and exocytosis, we plan to investigate the effects of downregulating unc-13 on JNK activation within the M/+ wing pouch, employing the JNK reporter TRE-DsRed for this purpose.

Additionally, we need to elucidate the molecular mechanism linking cell death and exocytosis. We are currently exploring two potential relationships between JNK activation, caspase signaling, and exocytosis, as depicted in Fig R2 below. To assess these possibilities, we aim to investigate if inhibiting apoptosis-either by introducing the H99/+ mutation or by overexpressing DroncDN or mirRHG-can affect JNK-mediated exocytosis in the RpS3/+ wing pouch.

So far, the evidence for the epistatic link between exocytosis, Wg and cell turnover is mostly based on colocalization and the similarity of the phenotype but I believe this may need some additional evidences. Ideally one would need to be able to enhance exocytosis and test whether Wg downregulation suppress the phenotype, but I am not sure that upregulation of core exocytosis genes will be sufficient to do this. Alternatively, if Wg is indeed downstream of the upregulation of exocytosis, the reduction of cell turnover upon Wg flattening (e.g. : ftz2-/+ background) should not be enhanced by the reduction of exocytosis. Moreover, could the authors test the status of Wg downstreams targets upon inhibition of exocytosis in the Minute background (for instance, do they see a supression of the nmo-LacZ upregulation that they previously characterised in Minute wing disc in 2021) ?

Response:

We thank the reviewer for the comment. In line with the reviewer's suggestion, exploring the enhancement of exocytosis would be valuable to elucidate the epistatic relationship between exocytosis, Wg signaling, and cell turnover. Therefore, we plan to attempt the overexpression of exocytosis-related genes to check if we can indeed enhance exocytosis. Additionally, in response to the reviewer's comment, we intend to investigate whether the reduction in cell turnover observed upon Wg attenuation (ftz2-/+background or Wg-/+ background) is not exacerbated by further reducing exocytosis. Furthermore, we intend to investigate the status of the Wg downstream target, specifically using nmo-lacZ, when exocytosis is inhibited in the RpS3/+ wing pouch.

Since Cyt1 and CD63 seem to mostly accumulate in apoptotic cells, it would be interesting to check their status in Minute wing disc upon apoptosis inhibition (e.g. : with H99 or mirRHG).

Response:

We thank the reviewer for the comment. Following the reviewer's suggestion, we intend to investigate whether inhibiting apoptosis, either through the introduction of H99/+ or by overexpressing DroncDN or mirRHG, could suppress the increase in CD63- or Sty1-positive vesicles in the M/+ wing pouch.

I would remain cautious about some of the statements, notably in the abstract, since some of them are mostly speculative and not really based on any experiments. For instance, the statement "This interaction between dying cells and their neighboring living cells is pivotal in determining cell fate, dictating which cells will undergo apoptosis and which cells will proliferate" is not backed up by any experiment (which would require to show that exocytosis and Wg from the dying cell specifically is required for the survival and proliferation of their neighbours, and/or showing that cell death occurs specifically in cells with local differences in Wg signaling). I would recommend to be more cautious here and us a clear conditional statement.

• *Response:

We thank the reviewer for their insightful comment. In response, we aim to present our findings with greater precision and to avoid speculative interpretations. At this stage, we have focused on revising the Abstract to include clear conditional statements, as suggested. Furthermore, we plan to comprehensively update the remaining sections of the manuscript to reflect the additional experiments requested by the reviewers. These updates will ensure a more cautious approach throughout the paper, aligning with the reviewer's recommendations.

__(page 2, line 34-39 in the "Abstract") __

"Our data also suggest a potential role for the Wg receptor Frizzled-2 (Fz2) in inducing cell-turnover within the M/+ wing pouch. Overall, our findings provide mechanistic insights into robust tissue growth through the orchestration of cell-turnover, which is primarily governed by JNK-mediated exocytosis in the context of Drosophila Minute/+ wing morphogenesis."

Other minor point:

The authors document Wg localisation in Minute wing disc upon expression of P35. It would be interesting to describe what is the status of Wg in Rps3+/- compared to WT without p35 (if I am correct, this was done in their previous article, and in that case it would be relevant to describe these former results in the main text).

Response:

We thank the reviewer for the comment. In the RpS3/+ wing pouch without p35, we were unable to detect any upregulation of Wg using the anti-Wg antibody (Fig R3, below). However, we observed an increase in GFP-Wg-positive puncta originating from a knock-in allele (McGough et al., Nature, 2020) within areas of massive cell death in the RpS3/+ wing pouch lacking p35, compared to the wild-type control (Fig 3B, compared to Fig 3A in the transferred manuscript). This increase is similar to the phenotype observed in the RpS3/+ wing pouch expressing p35, where Wg-positive puncta are significantly elevated (Fig R4B below, corresponding to Fig 3B in the original manuscript). Moreover, the increase in GFP-Wg-positive puncta in regions of massive cell death in the RpS3/+ wing pouch becomes more pronounced when utilizing a membrane-tethered anti-GFP nanobody (Vhh4-CD8) (McGough et al., Nature, 2020) (Fig 3G, compared to Fig 3F in the transferred manuscript). These observations indicate that Wg-positive puncta are indeed upregulated in the RpS3/+ wing pouch without p35 compared to the wild-type control.

In the transferred manuscript, we have now made modifications to Fig. 3 by replacing images of the RpS3/+ wing pouch overexpressing p35, which were stained with the anti-Wg antibody, with new images. These new images depict the RpS3/+ wing pouch that harbors the GFP-Wg knock-in allele, which was stained with both anti-GFP and anti-cDCP1 antibodies.

To clarify this point, we have now modified the sentence as follows:

(page 7, line 204-210)

Interestingly, we found that the RpS3/+ wing pouch expressing the cell death inhibitor p35 (which allows dying RpS3/+ cells to survive) exhibited elevated levels of Wg protein, compared to the wild-type control (Fig 3A and 3B). This increase in Wg protein was significantly diminished by overexpressing the JNK inhibitor Puc (Fig 3C), suggesting that Wg expression is upregulated via JNK signaling in the M/+ wing pouch, similar to apoptotic cells in which JNK signaling induces the production of secreted growth factor, including Wg (18, 53, 54). In addition, ____W____e found t____hat GFP-Wg-positive puncta, derived from a knock-in allele ____(34)____, ____were more abundant in the RpS3/+ wing pouch compared to the wild-type control (Fig 3A and 3B). This increase in GFP-Wg-positive puncta, ____especially in the area with massive cell death within the RpS3/+ wing pouch (Fig S3C-S3D'')_, was more evident when using a membrane-tethered anti-GFP nanobody (Vhh4-CD8), which immobilizes GFP-Wg on the cell surface _(34)____ (Fig 3F and 3G, quantified in Fig 3J).

Referee #2

Primary Concerns:

A significant challenge arises concerning the delineation of cell autonomy/non-autonomy. This study focuses on two distinct cell types, namely dying cells and proliferating cells. However, the consistent use of nub-gal4, a wing pouch driver, and the heterozygous minute mutant throughout the paper impedes the ability to conclusively analyze the autonomy of events. The authors previously posited that caspase-induced cell death triggers non-autonomous proliferation, but recent studies also suggested caspase-induced autonomous proliferation in both flies and mammals (Yosefzon et al. Mol. Cell 2018, Shinoda et al., PNAS 2019). Therefore, a meticulous distinction between autonomous and non-autonomous events, particularly through experimentation involving clones, is imperative. This necessity is particularly evident in Fig 4.

Response:

• As pointed out by the reviewer, it is ideal to dissect the mechanisms underlying cell turnover within the M/+ wing pouch, especially concerning cell autonomy and non-autonomy. However, clonal analysis is not feasible due to the pattern of cell death and subsequent proliferation occurring in a 'salt and pepper' distribution within the M/+* wing pouch. In response to this challenge, we found that almost dying cells do not undergo proliferation, as assessed by staining with the M phase marker phospho-Histone H3 (Fig R5, below).

We also plan to investigate whether JNK-activating cells similarly refrain from proliferating, which will be assessed by staining with the anti-phospho-Histone H3 antibody.

Additionally, about Fig 4, considering the evidence presented in this study, which demonstrates that dying cells increase Wg secretion through JNK-dependent exocytosis (Fig 3G-3H'), and given that Fz2 is expressed in adjacent cells within the M/+ wing pouch (Fig 4B-C'' and Fig S4B-C''), it is plausible that these neighboring cells could receive Wg via Fz2, leading to the upregulation of Wg signaling in these cells in the M/+ wing pouch. This upregulation of Wg signaling is supported by Fig S3A in the transferred manuscript. However, we were unable to delineate the specific role of Fz2, particularly in terms of cell autonomy and non-autonomy. In response to this challenge, we aim to explore whether cell turnover can be inhibited by enhancing Wg signaling exclusively in JNK-activated cells through the overexpression the active form of ArmadilloS10 (Baena-Lopez LA et al., Sci Signal., 2009), utilizing the puc-gal4 driver. Should cell turnover be inhibited under these conditions, it would indicate that differences in Wg signaling activity between dying cells and their neighboring cells drive cell turnover. While the exact mechanism of Fz2 remains unclear, the inhibition of cell turnover under these conditions clearly demonstrates that differences in Wg signaling activity play a significant role in cell turnover. Additionally, in our response to Reviewer 2's comment No. 2, we outline our intention to investigate whether the increase in Wg signaling could be induced by JNK-dependent exocytosis. Accordingly, we plan to assess the effects of downregulating JNK signaling or exocytosis on the elevated Wg signaling activity observed in the RpS3/+ wing pouch.

Furthermore, we intend to present our findings with greater precision, steering clear of speculative interpretations. At this stage, we have focused on revising the Abstract to include clear conditional statements, as detailed below. We plan to comprehensively update the remaining sections of the manuscript to reflect the additional experiments requested by the reviewers.

(page 2, line 34-39 in the "Abstract")

"Our data also suggest a potential role for the Wg receptor Frizzled-2 (Fz2) in inducing cell-turnover within the M/+ wing pouch. Overall, our findings provide mechanistic insights into robust tissue growth through the orchestration of cell-turnover, which is primarily governed by JNK-mediated exocytosis in the context of Drosophila Minute/+ wing morphogenesis."

Closely tied to the issue of cell autonomy/non-autonomy is the question of how cells differentiate Wg from dying cells and the dorsal-ventral boundary.

Response:

Wg is expressed at the dorsal-ventral boundary in both wild-type and M/+ wing discs. However, we observed in our previous study that Wg signaling activity was significantly more elevated in the RpS3/+ pouch compared to the localized activation in wild-type controls at the same developmental stage, as assessed by the nmo-lacZ reporter (Fig 3C-D' in Akai et al., PLOS Genetics, 2021, as also shown in Fig R6A-B' below). Interestingly, the areas of massive cell death in the RpS3/+ wing pouch always corresponded to the areas of relatively lower Wg signaling activity (Fig S3A in the transferred manuscript). Moreover, our previous study revealed that decreasing or increasing Wg signaling activity, thus reducing the aberrant Wg signaling gradient, significantly inhibited cell death in the M/+ wing pouch (Fig 3I-K in Akai et al., PLOS Genetics, 2021, as also shown in Fig R6C-E' below). This suggest that the aberrant Wg signaling gradient is crucial for massive cell-turnover in the M/+ wing pouch. As also described above, considering the evidence presented in this study, which demonstrates that dying cells increase Wg secretion through JNK-dependent exocytosis (Fig 3G-3H'), and given that Fz2 is expressed in adjacent cells (Fig 4B-C'' and Fig S4B-C'') within the M/+ wing pouch, it is plausible that these neighboring cells could receive Wg via Fz2, leading to the upregulation of Wg signaling in these cells within the M/+ wing pouch. To further investigate whether the increase in Wg signaling could be induced by JNK-dependent exocytosis, we plan to examine the effects of downregulating JNK signaling or exocytosis on the elevated Wg signaling activity observed in the RpS3/+ wing pouch. Should Wg signaling activity decrease as a result of these genetic interventions, it would imply that the enhanced Wg signaling in the M/+ wing pouch depends on JNK-mediated exocytosis.

In Fig 1, the authors interpret the upregulation of exocytosis-related genes as indicative of increased exocytosis. However, this interpretation lacks direct evidence and overlooks the possibility of opposing effects. For example, autophagosome accumulation means either activation or inhibition of autophagy. Or, in case of Dilp secretion, absence of vesicles indicates upregulation of secretion. To substantiate their claim, the authors must provide more conclusive evidence of increased exocytosis. Fig 2 suggests that inhibiting exocytosis-related genes suppresses caspase activation, favoring the proposition that exocytosis is upregulated. However, demonstrating a direct increase in exocytosis in minute cells would bolster their argument. Higher resolution imaging of the exosome marker, with overlayed images, would enhance clarity too.

Response:

We have demonstrated an increase in the number of vesicles positive for EGFP-CD63 (an exosome marker) and Syt1-EGFP (a vesicle marker) in the RpS3/+ wing pouch compared to the wild-type control (Fig 1A, 1B, 1G, and 1H in the transferredmanuscript). To more directly investigate whether exocytosis is indeed elevated in the M/+ wing pouch, we plan to assess if cells activating JNK signaling upregulate the production of extracellular vesicles. This will be done by specifically expressing the EGFP-CD63 probe in JNK-activating cells, utilizing the puc-gal4 driver for targeted expression. Additionally, following the reviewer's suggestion, we plan to prepare high resolution images of the exosome marker, with overlayed images in the revised manuscript.

Fig 3 introduces ambiguity regarding the relationship between cell death and exocytosis. The authors assert that dying cells exhibit elevated Wg protein levels compared to the wild-type control but omit an important comparison to the minute disc. Moreover, while Figs 1-2 propose a signaling cascade involving minute>JNK>exocytosis>cell death, Fig 3 implies that cell death regulates exocytosis. The coherence of their model and logic requires clarification - specifically, elucidating the molecular coupling mechanism between cell death and exocytosis.

Response:

We observed an increase in GFP-Wg-positive puncta originating from a knock-in allele (McGough et al., Nature, 2020) in the area of massive cell death within the RpS3/+ wing pouch, compared to the wild-type control (Fig 3A and 3B in the transferredmanuscript). However, as pointed out by the reviewer, it is challenging to determine whether the GFP-Wg-positive puncta are emanating from dying cells, given that Wg is secreted from the cells that produce it. To address this issue, we employed a membrane-tethered anti-GFP nanobody (Vhh4-CD8 morphotrap) designed to capture GFP-Wg on the cell surface, thereby preventing the diffusion of GFP-Wg from its producing cells. By utilizing the Vhh4-CD8 morphotrap, we found that GFP-Wg levels are indeed elevated in areas of cell death compared to adjacent regions within the RpS3/+ wing pouch (Fig 3G in the transferred manuscript).

To clarify this point, we have now modified the sentence as follows:__ __

(page 7, line 204-210)

In addition, ____W____e found t____hat GFP-Wg-positive puncta, derived from a knock-in allele ____(34)____, ____were more abundant in the RpS3/+ wing pouch compared to the wild-type control (Fig 3A and 3B). This increase in GFP-Wg-positive puncta, ____especially in the area with massive cell death within the RpS3/+ wing pouch (Fig S3C-S3D'')_, was more evident when using a membrane-tethered anti-GFP nanobody (Vhh4-CD8), which immobilizes GFP-Wg on the cell surface _(34)____ (Fig 3F and 3G, quantified in Fig 3J).

Additionally, as pointed out by the reviewer, we need to elucidate the molecular mechanism linking cell death and exocytosis. We are currently exploring two potential relationships between JNK activation, caspase signaling, and exocytosis, as depicted in Fig R2 below. To assess these possibilities, we aim to investigate if inhibiting apoptosis-either by introducing the H99/+ mutation or by overexpressing DroncDN or mirRHG-can affect JNK-mediated exocytosis in the RpS3/+ wing pouch.

Specific Points:

In Fig S1D, contrary to the authors' claim, cadp2 is not upregulated in a JNK-dependent manner.

Response:

We apologize for any confusion caused. We found that Cadps expression in the RpS3/+ wing pouch was increased compared to both the wild-type control (2.29-fold increase, RpS3/+ compared to wild-type) and the RpS3/+ wing pouch expressing Puckered (Puc), driven by the nub-gal4 driver (3.33-fold increase, RpS3/+ compared to RpS3/+ + Puckered). This suggests that the increase in Cadps expression in the RpS3/+ wing pouch is dependent on JNK signaling. We have now revised Fig. S1D for clearer representation. We also have made modifications in the transferred manuscript as follows:

(page 5, line 107-113)

"Mining the list of genes differentially expressed in the RpS3/+ wing pouch cells dependent on JNK signaling (Fig S1C and S2 Table), we noticed that among the genes associated with the "secretion by cell" GO term (Fig S1B), the evolutionarily conserved exocytosis-related genes unc-13, SNAP25, and cadps (Calcium-dependent secretion activator) were upregulated in a JNK-dependent manner (2.29-fold increase, RpS3/+ compared to wild-type; 3.33-fold increase, RpS3/+ compared to RpS3/+ +_ Puckered)_ (Fig S1D)."

When detecting multiple proteins in the same tissue, it is advisable for the authors to present overlayed images to enhance the clarity of their findings. Many pictures require higher magnification too.

Response:

Following the reviewer's suggestion, we have overlayed images in Fig 1A-D, Fig 1G-J, and Fig S1E in the transferredmanuscript. Additionally, following the reviewer's suggestion, we plan to prepare high resolution images in the revised manuscript.

In Fig 1A, the observed upregulation of EGFP-CD63 and Syt1-EGFP may potentially result from an artifactual effect of apoptosis. To validate their findings are specific, the authors should include negative controls that do not exhibit upregulation in dying cells.

Response:

Following the reviewer's suggestion, we used the CD8-PARP-Venus probe as a negative control. We observed that CD8-PARP-Venus-positive puncta were minimally present (Fig R7, below), indicating that the upregulation of EGFP-CD63 and Syt1-EGFP in the RpS3/+ wing pouch is indeed occurring, rather than being an artifactual effect of apoptosis. We intend to incorporate this negative control into the revised manuscript.

Referee #3

Major comments:

Figure 1A-H, S1E. The authors used EGFP-CD63 and Syt1-EGFP as markers of exocytosis. They see an increased number of puncta in apoptotic cells. Is this a specific effect in the dying cells in M mutant discs, or is it a general effect in apoptotic cell death? This should be examined in a condition where apoptosis is induced independently of M mutants such as nub-reaper or nub-hid.

Response:

We thank the reviewer for the comment. To ascertain whether the increase in EGFP-CD63-/Sty1-EGFP-positive puncta is specific to dying cells in M/+ mutants or a general characteristic of apoptotic cell death, we examined the presence of EGFP-CD63-positive puncta in the wing pouch, where Reper (Rpr) was expressed under the control of the nub-gal4 driver. Unfortunately, the expression of Rpr driven by nub-gal4 resulted in significant cell death, preventing us from drawing a definitive conclusion (Fig R8, below). Nonetheless, we did observe EGFP-CD63-positive puncta under these conditions, as indicated by the arrowheads in Fig R8 below. To further investigate, we plan to induce temporary expression of Rpr in the wing pouch using a combination of the temperature-sensitive Gal80 and the nub-gal4 driver.

Is exocytosis actually upstream or downstream of cell death, or both? The authors are kind of vague about it. On one hand, they say the dying cells induce exocytosis and secrete Wg. On the other hand, unc13RNAi can suppress cell death (Figure 1D', J'). Please clarify.

Response:

As pointed out by the reviewer, we need to clarify whether exocytosis actually occurs upstream or downstream of cell death. We are currently exploring two potential relationships between JNK activation, caspase signaling, and exocytosis, as depicted in Fig R2 below. To assess these possibilities, we aim to investigate if inhibiting apoptosis-either by introducing the H99/+ mutation or by overexpressing DroncDN or mirRHG-can affect JNK-mediated exocytosis in the RpS3/+ wing pouch.

Figure 1L-P. The observation of Ca++ flashes is very interesting. However, are they important for exocytosis, cell death and compensatory proliferation? Right now, this is just a stand-alone observation. Can mutants affecting Ca++ signaling block exocytosis, cell death and comp prol?

Response:

We thank the reviewer for the comment. we plan to investigate whether the downregulation of Ca++ signaling impacts exocytosis, cell death, and compensatory proliferation in the M/+ wing pouch. This will be achieved by downregulating genes essential for sensing intracellular calcium concentrations (Rizo J and Rosenmund C, Nat Struct Mol Biol., 2008; Sudhof TC, Annu Rev Neurosci., 2004) and genes encoding voltage-gated calcium channels (Kuromi H et al., Neuron, 2004).

Figure 3B'. Can you visualize aberrant wg expression in RpS3/+ wing discs only in the presence of p35? The expression of p35 in apoptotic cells generates undead cells which by itself induce Wg expression in a JNK-dependent manner (Perez-Garijo et al 2004; Ryoo et al 2004). Also, in Figure 3B', Wg is upregulated in the ventral half of the pouch, whereas in other figures (4B for example) apoptosis is strongly induced in the dorsal half. Does that make sense?

Response:

We thank the reviewer for the comment. In the RpS3/+ wing pouch without p35, we were unable to detect any upregulation of Wg using the anti-Wg antibody (Fig R3, below). However, we observed an increase in GFP-Wg-positive puncta, derived from a knock-in allele (McGough et al., Nature, 2020), in areas of massive cell death within the RpS3/+ wing pouch without p35, relative to the wild-type control (Fig 3B, compared to Fig 3A in the transferred manuscript). This increase is similar to the phenotype observed in the RpS3/+ wing pouch expressing p35, where Wg-positive puncta are significantly elevated (Fig R4B below, corresponding to Fig 3B in the original manuscript). Moreover, the increase in GFP-Wg-positive puncta in regions of massive cell death in the RpS3/+ wing pouch becomes more pronounced when utilizing a membrane-tethered anti-GFP nanobody (Vhh4-CD8) (McGough et al., Nature, 2020) (Fig 3G, compared to Fig 3F). These observations indicate that Wg-positive puncta are indeed upregulated in the RpS3/+ wing pouch without p35 compared to the wild-type control.

In the transferred manuscript, we have now made modifications to Fig. 3 by replacing images of the RpS3/+ wing pouch overexpressing p35, which were stained with the Wg antibody, with new images. These new images depict the RpS3/+ wing pouch that harbors the GFP-Wg knock-in allele, which was stained with both anti-GFP and anti-cDCP1 antibodies.

To clarify this point, we have now modified the sentence as follows:

(page 7, line 204-210)

Interestingly, we found that the RpS3/+ wing pouch expressing the cell death inhibitor p35 (which allows dying RpS3/+ cells to survive) exhibited elevated levels of Wg protein, compared to the wild-type control (Fig 3A and 3B). This increase in Wg protein was significantly diminished by overexpressing the JNK inhibitor Puc (Fig 3C), suggesting that Wg expression is upregulated via JNK signaling in the M/+ wing pouch, similar to apoptotic cells in which JNK signaling induces the production of secreted growth factor, including Wg (18, 53, 54). In addition, ____W____e found t____hat GFP-Wg-positive puncta, derived from a knock-in allele ____(34)____, ____were more abundant in the RpS3/+ wing pouch compared to the wild-type control (Fig 3A and 3B). This increase in GFP-Wg-positive puncta, ____especially in the area with massive cell death within the RpS3/+ wing pouch (Fig S3C-S3D'')_, was more evident when using a membrane-tethered anti-GFP nanobody (Vhh4-CD8), which immobilizes GFP-Wg on the cell surface _(34)____ (Fig 3F and 3G, quantified in Fig 3J).

Additionally, we apologize for any confusion caused by Fig 3B'. It is noteworthy that cell death sometimes occurs more prominently in the ventral half of the RpS3/+ wing pouch than in the dorsal half (Fig R9, below). Furthermore, the increase in Wg level can be more pronounced on the ventral side, or at times, it is equally strong on both the dorsal and ventral sides (Fig S3C-D in the transferred manuscript).

Can wg RNAi in cells destined to die (puc-Gal4 UAS-wgRNAi) suppress apoptosis and comp prol?

Response:

Following the reviewer's suggestion, we intend to investigate whether expressing Wg-RNAi in JNK activated cells, using the puc-gal4 driver, could suppress apoptosis and compensatory proliferation.

Figure 3D,E. Use cDcp1 as apoptotic marker instead of CD63-mCherry which is not an apoptotic marker.

Response:

Following the reviewer's suggestion, we have now utilized the cDCP1 antibody as an apoptotic marker in Fig S3B-D'' in the transferred manuscript, as described in the Reviewer 3's comment No.4.

Figure 4A' and B'. I am not sure there is much of a difference in the expression of fz2-lacZ in wild-type and RpS3/+ discs. The quantification in 4F shows there is no difference in the dorsal half of the pouch where massive apoptosis occurs. Can you generate a condition in which only one compartment (anterior or posterior) is mutant for RpS3/+, while the other compartment is wt? That would allow direct side-by-side comparison. Comparisons between different discs is problematic.

Response:

We thank the reviewer for the comment. Following the reviewer's suggestion, we conducted a more detailed investigation into the differences in fz2-lacZ expression levels between wild-type and RpS3/+ wing discs. We found that the expression level of fz2-lacZwas indeed elevated in the RpS3/+ wing pouch. This elevation in expression is demonstrated by the results of the genetic rescue experiment in the posterior compartment of RpS3/+ wing discs, where overexpression of RpS3 using the engrailed-gal4 driver led to a reduction in fz2-lacZ expression compared to the anterior RpS3/+ control (Fig R10, below).

After conducting statistical analysis, we plan to include Fig R10 in the revised manuscript.

There is some inconsistency in the presence of apoptotic cells and presence of cells which secrete Wg. Apoptotic cells occur in large cell clusters (Fig. 2G, 3H', S3A', S4B), while markers of exocytosis and Wg are present in individual puncta (Fig 3D', E', S3C,E). That does not seem to fit with the authors' conclusion that dying cells secrete Wg by exocytosis. Are all dying cells secreting Wg through exocytosis? Please explain.

Response:

We thank the reviewer for the comment. As highlighted by the reviewer, it appears that not all dying cells secrete Wg through exocytosis. Beyond exosomes, various mechanisms for Wg/Wnt transport have been proposed, including those mediated by lipoprotein particles, the cell-surface proteoglycan Dally-like protein (Dlp), and filopodia-like cellular extensions known as cytonemes. Therefore, it's plausible that dying cells may also utilize these additional mechanisms for Wg transport alongside exosomes. We have incorporated this explanation into the transferred manuscript as follows:

(page 9, line 272-286)

Previous studies have identified exosomes as carriers of Wnt/Wg in the extracellular space of both mammalian and Drosophila cells, including wing disc cells (28, 49, 50, 51, 52, 64). Concurrently, alternative mechanisms for Wg transport, such as those involving lipoprotein particles or a lipocalin Swim in the Drosophila wing disc, have been reported (29, 65). Additionally, the cell-surface proteoglycan Dally-like-protein (Dlp) has been reported to enable long-range signaling of the palmitoylated Wg _(51)._ Intriguingly, Wnt/Wg transport has also been observed through filopodia-like cellular extensions known as cytonemes (66, 67, 68, 69). In our study of the M/+_ wing disc, a model characterized by massive cell-turnover, we observed partial colocalization of Wg-GFP puncta with exosomal markers such as CD63-mCherry and Hrs._ Our data also suggest that Wg secretion through exocytosis may not uniformly occur among all dying cells within this context. It is noteworthy that whereas dying cells frequently form large clusters, exosomal markers and Wg typically localize within individual puncta. This disparity suggests that while exosomes from dying cells significantly contribute to Wg transport within the ____M/+____ wing pouch, other pathways may also be operative.

I was a bit confused by the conclusion of the authors about the results in Figure 4G-I. What do they mean by "difference in Fz2 expression"? Are they referring to the gradient that they described in their previous work? Or is it just the absolute level of Fz2 that determines apoptosis and proliferation? If the latter, is the gradient still present (at least in fz2/+), just at a lower level?

Response:

I apologize for any confusion caused by the way we presented our conclusions regarding the results depicted in Figure 4G-I in the original manuscript.

In our previous study, we observed that Wg signaling activity was elevated much more broadly in the RpS3/+ pouch compared to the localized activation observed in the wild-type control at the same developmental stage, as assessed by the nmo-lacZ reporter(Fig 3D in Akai et al., PLOS Genetics, 2021, as also shown Fig. R6 below). Interestingly, the areas of massive cell death in the RpS3/+ wing pouch always corresponded to the areas of relatively lower Wg signaling activity (as also shown in Fig S3A in the transferred manuscript). Moreover, our previous study revealed that decreasing or increasing Wg signaling activity, thus reducing the aberrant Wg signaling gradient, significantly inhibited cell death in the M/+ wing pouch (Fig 3I-K in Akai et al., PLOS Genetics, 2021, as also shown in Fig R6C-E' below). This suggest that the aberrant Wg signaling gradient is crucial for massive cell-turnover in the M/+ wing pouch.

Considering the evidence presented in this study, which demonstrates that dying cells increase Wg secretion through JNK-dependent exocytosis (Figure 3G-3H'), and given that Fz2 is expressed in adjacent cells within the M/+ wing pouch (Figure 4B-C'' and Fig S4B-C''), it is plausible that these neighboring cells could receive Wg via Fz2, leading to the upregulation of Wg signaling in these cells in the M/+ wing pouch.

However, we were unable to delineate the specific role of Fz2, particularly in terms of cell autonomy and non-autonomy as highlighted by Reviewer 2, through clonal analysis due to the occurrence of cell death and subsequent proliferation in a salt-and-pepper pattern within the M/+ wing pouch. In response to this challenge, we aim to explore whether cell turnover can be inhibited by enhancing Wg signaling exclusively in JNK-activated cells through the overexpression the active form of ArmadilloS10(Baena-Lopez LA et al., Sci Signal., 2009), utilizing the puc-gal4 driver. Should cell turnover be inhibited under these conditions, it would indicate that differences in Wg signaling activity between dying cells and their neighboring cells drive cell turnover. While the exact mechanism of Fz2 remains unclear, the inhibition of cell turnover under these conditions clearly demonstrates that differences in Wg signaling activity play a significant role in cell turnover. Additionally, in our response to Reviewer 2's comment No.2, we outline our intention to investigate whether the increase in Wg signaling could be induced by JNK-dependent exocytosis. Accordingly, we plan to assess the effects of downregulating JNK signaling or exocytosis on the elevated Wg signaling activity observed in the RpS3/+ wing pouch.

Furthermore, we intend to present our findings with greater precision, steering clear of speculative interpretations. At this stage, we have focused on revising the Abstract to include clear conditional statements, as detailed below. We plan to comprehensively update the remaining sections of the manuscript to reflect the additional experiments requested by the reviewers.

(page 2, line 34-39 in the "Abstract")

"Our data also suggest a potential role for the Wg receptor Frizzled-2 (Fz2) in inducing cell-turnover within the M/+ wing pouch. Overall, our findings provide mechanistic insights into robust tissue growth through the orchestration of cell-turnover, which is primarily governed by JNK-mediated exocytosis in the context of Drosophila Minute/+ wing morphogenesis."

Regarding point 8, given that reduction of Fz2 can suppress apoptosis in RpS3/+ wing discs, how does it regulate apoptosis when it is down-regulated anyway in apoptotic cells (Fig 4B', S4B')?

Response:

As described in our response to point 9, our previous study suggested that we observed that Wg signaling activity was elevated much more broadly in the RpS3/+ pouch compared to the localized activation observed in the wild-type control at the same developmental stage, as assessed by the nmo-lacZ reporter (Fig 3D in Akai et al., PLOS Genetics, 2021, as also shown Fig. R6 above). This elevation leads to the formation of an ectopic cell population with high Wg signaling activity in the wing pouch, potentially causing non-autonomous cell death among cells exhibiting lower Wg signaling activity, a process akin to cell competition. Notably, the significant reduction of apoptosis in RpS3/+ wing discs following Fz2 downregulation suggests that Fz2 may play a crucial role in the massive cell turnover, through a mechanism similar to cell competition, even though the exact mechanism remains unclear. We plan to incorporate such discussions into the discussion section of the revised manuscript.

Figure S1D. It seems that cadps is further up-regulated if JNK signaling is inhibited in RpS3/+ cells. Why did the authors select this gene?

Response:

We apologize for any confusion caused. We found that Cadps expression in the RpS3/+ wing pouch was increased compared to both the wild-type control (2.29-fold increase, RpS3/+ compared to wild-type) and the RpS3/+ wing pouch expressing Puc, driven by the nub-gal4 driver (3.33-fold increase, RpS3/+ compared to RpS3/+ +Puc). This suggests that the increase in Cadpsexpression in the RpS3/+ wing pouch is dependent on JNK signaling. We have now revised Fig S1D for clearer representation. We also have made modifications in the transferred manuscript as follows:

(page 5, line 107-113)

"Mining the list of genes differentially expressed in the RpS3/+ wing pouch cells dependent on JNK signaling (Fig S1C and S2 Table), we noticed that among the genes associated with the "secretion by cell" GO term (Fig S1B), the evolutionarily conserved exocytosis-related genes unc-13, SNAP25, and cadps (Calcium-dependent secretion activator) were upregulated in a JNK-dependent manner (2.29-fold increase, RpS3/+ compared to wild-type; 3.33-fold increase, RpS3/+ compared to RpS3/+ +_ Puckered)_ (Fig S1D)."

Figure S1H'. I don't see that Hrs is upregulated in this panel.

Response:

We thank the reviewer for the comment. Our quantitative analysis showed an increase in Hrs-positive puncta in the RpS3/+ wing pouch compared to the wild-type control (Fig S1I). We have substituted the relevant Figure with new images that more clearly demonstrate the elevation of Hrs-positive puncta (Fig S1G-H' in the transferred manuscript).

Minor points:

Describe in more detail, what are unc13, SNAP25 and cadps.

Response:

We thank the reviewer for the comment. We have now included an explanation for unc-13, SNAP25 and cadps in the transferredmanuscript as follows:

(page 5, line 117-126)

"It has been shown that unc-13, SNAP25, and cadps collectively regulate the docking process of secretory vesicles to the plasma membrane during Ca2+-mediated exocytosis ____((21, 23, 24), Reviewed in (22)). ____Specifically, UNC-13, a conserved presynaptic protein with calcium-binding domains, interacts with syntaxin to prime vesicles for fusion, crucial for calcium-regulated exocytosis (____23____). SNAP-25, in conjunction with syntaxin-1 and synaptobrevin, forms the pivotal SNARE complex for neuronal exocytosis, assembling into a four-helix bundle that is essential for drawing vesicle and plasma membranes close together to enable membrane fusion (____24, 25____). Like UNC-13, CAPS possesses conserved C-terminal domains that are instrumental in the assembly of SNARE complexes, thus priming vesicles for Ca2+-induced exocytosis (____26)____.____"

I wondered about the use of Hrs as exosome marker. To my knowledge, it is an endosomal marker. Same with Alix. Please clarify.

Response:

As pointed out by the reviewer, ESCRT-0 component Hrs is also localized to endosome. However, Hrs is also used as an exosome marker in the previous manuscript (McGough IJ et al., Nature, 2020), alongside Alix and Tsg101, which are widely recognized as exosome markers (Willms E et al., Sci Rep., 2016; Dear JW et al., Proteomics, 2013). Indeed, Hrs is a key factor for mediating ESCRT-dependent exosome secretion in mammals and flies (Tamai K et al., Biochem Biophys Res Commun., 2010; Gross JC et al., Nat Cell Biol., 2012; Colombo M et al., J Cell Sci., 2013; Vietri M et al., Nat Rev Mol Cell Biol., 2020). We have incorporated this explanation into the revised manuscript as follows:

(page 6, line 139-141)

"____Furthermore, we noted an increase in vesicles positive for the ESCRT protein Hrs, ____an additional exosome marker crucial for exosome secretion (____34, 35____), in the RpS3/+ wing pouch relative to the wild-type control (Fig S1G and S1H, quantified in Fig S1I)."

In the context of references 16 and 17, Huh et al. (2004), Current Biology needs also to be cited.

Response:

We thank the reviewer for the comment. We have referenced the paper by Huh et al. (2004) published in Current Biology in the transferred manuscript as follows:

(page 3, line 68-71)

"Apoptotic cells, for example, can secrete mitogens su____ch as Wingless ____(Wg; a Wnt homolog), dpp (a BMP homolog), and Hh, which could promote the proliferation of nearby cells in the Drosophila epithelium (15, _16_, 17, 18, 19)."

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Referee #3

Evidence, reproducibility and clarity

Summary: In previous work, the authors showed that in the pouch of wing imaginal discs in Minute (M) mutants apoptosis and compensatory proliferation are dramatically increased in a Wingless (Wg) and JNK-dependent manner. Here, they show that JNK-induced exocytosis is mediating the secretion of Wg in apoptotic cells. Wg in turn stimulates the Fz2 receptor in neighboring surviving cells promoting their proliferation.

Major comments:

1. Figure 1A-H, S1E. The authors used EGFP-CD63 and Syt1-EGFP as markers of exocytosis. They see an increased number of puncta in apoptotic cells. Is this a specific effect in the dying cells in M mutant discs, or is it a general effect in apoptotic cell death? This should be examined in a condition where apoptosis is induced independently of M mutants such as nub-reaper or nub-hid.
2. Is exocytosis actually upstream or downstream of cell death, or both? The authors are kind of vague about it. On one hand, they say the dying cells induce exocytosis and secrete Wg. On the other hand, unc13RNAi can suppress cell death (Figure 1D', J'). Please clarify.
3. Figure 1L-P. The observation of Ca++ flashes is very interesting. However, are they important for exocytosis, cell death and compensatory proliferation? Right now, this is just a stand-alone observation. Can mutants affecting Ca++ signaling block exocytosis, cell death and comp prol?
4. Figure 3B'. Can you visualize aberrant wg expression in RpS3/+ wing discs only in the presence of p35? The expression of p35 in apoptotic cells generates undead cells which by itself induce Wg expression in a JNK-dependent manner (Perez-Garijo et al 2004; Ryoo et al 2004). Also, in Figure 3B', Wg is upregulated in the ventral half of the pouch, whereas in other figures (4B for example) apoptosis is strongly induced in the dorsal half. Does that make sense?
5. Can wg RNAi in cells destined to die (puc-Gal4 UAS-wgRNAi) suppress apoptosis and comp prol?
6. Figure 3D,E. Use cDcp1 as apoptotic marker instead of CD63-mCherry which is not an apoptotic marker.
7. Figure 4A' and B'. I am not sure there is much of a difference in the expression of fz2-lacZ in wild-type and RpS3/+ discs. The quantification in 4F shows there is no difference in the dorsal half of the pouch where massive apoptosis occurs. Can you generate a condition in which only one compartment (anterior or posterior) is mutant for RpS3/+, while the other compartment is wt? That would allow direct side-by-side comparison. Comparisons between different discs is problematic.
8. There is some inconsistency in the presence of apoptotic cells and presence of cells which secrete Wg. Apoptotic cells occur in large cell clusters (Fig. 2G, 3H', S3A', S4B), while markers of exocytosis and Wg are present in individual puncta (Fig 3D', E', S3C,E). That does not seem to fit with the authors' conclusion that dying cells secrete Wg by exocytosis. Are all dying cells secreting Wg through exocytosis? Please explain.
9. I was a bit confused by the conclusion of the authors about the results in Figure 4G-I. What do they mean by "difference in Fz2 expression"? Are they referring to the gradient that they described in their previous work? Or is it just the absolute level of Fz2 that determines apoptosis and proliferation? If the latter, is the gradient still present (at least in fz2/+), just at a lower level?
10. Regarding point 8, given that reduction of Fz2 can suppress apoptosis in RpS3/+ wing discs, how does it regulate apoptosis when it is down-regulated anyway in apoptotic cells (Fig 4B', S4B')?
11. Figure S1D. It seems that cadps is further up-regulated if JNK signaling is inhibited in RpS3/+ cells. Why did the authors select this gene?
12. Figure S1H'. I don't see that Hrs is upregulated in this panel.

Minor points:

1. Describe in more detail, what are unc13, SNAP25 and cadps.
2. I wondered about the use of Hrs as exosome marker. To my knowledge, it is an endosomal marker. Same with Alix. Please clarify.
3. In the context of references 16 and 17, Huh et al. (2004), Current Biology needs also to be cited.

Referees cross-commenting

I think all three reviewers agree in their assessment of this manuscript. Some of the comments by the reviewers address the same concerns. I liked the comment by reviewer 2 about the autonomy/non-autonomy of the signaling events in this model. I was thinking that, too, but didn't express it in my review. So, thanks reviewer 2, for bringing this up.

Significance

General assessment. A major strength of the work is that the experiments are done in a very good manner. The authors used multiple assays to come to the same conclusions. Limitations and weaknesses are mentioned in "major comments".

Advance. In my mind, one problem is novelty of this work. The authors showed before that Wg is secreted by dying cells in Minute mutants. It was also shown that Wg can be secreted by exocytosis in many studies from different authors. Here, the authors basically combine both observations and show that Wg is secreted by exosomes in Minute mutants.

Audience. This work likely addresses a specialized audience involved in Minute-induced cell competition. I don't think it will be of interest beyond this specific field.

Background of the reviewer. I have an interest in cell competition, apoptosis and neurodegeneration.

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Referee #2

Evidence, reproducibility and clarity

The authors initiate their study by illustrating that minute cells undergo an augmentation in exocytosis-related proteins and calcium flashes (Fig 1). Subsequently, they establish a correlation between JNK-mediated exocytosis and the regulation of caspase activation in minute cells (Fig 2). Further, the authors unveil a dependency of Wg secretion on exocytosis, elucidated in Fig 3. Finally, they discern the involvement of one of the Wg receptors, Fz2, in the cell death/proliferation phenotype of minute cells. Despite the formulation of an intriguing hypothesis, the presented data falls short of robustly supporting their assertions.

Primary Concerns:

1. A significant challenge arises concerning the delineation of cell autonomy/non-autonomy. This study focuses on two distinct cell types, namely dying cells and proliferating cells. However, the consistent use of nub-gal4, a wing pouch driver, and the heterozygous minute mutant throughout the paper impedes the ability to conclusively analyze the autonomy of events. The authors previously posited that caspase-induced cell death triggers non-autonomous proliferation, but recent studies also suggested caspase-induced autonomous proliferation in both flies and mammals (Yosefzon et al. Mol. Cell 2018, Shinoda et al., PNAS 2019). Therefore, a meticulous distinction between autonomous and non-autonomous events, particularly through experimentation involving clones, is imperative. This necessity is particularly evident in Fig 4.
2. Closely tied to the issue of cell autonomy/non-autonomy is the question of how cells differentiate Wg from dying cells and the dorsal-ventral boundary.
3. In Fig 1, the authors interpret the upregulation of exocytosis-related genes as indicative of increased exocytosis. However, this interpretation lacks direct evidence and overlooks the possibility of opposing effects. For example, autophagosome accumulation means either activation or inhibition of autophagy. Or, in case of Dilp secretion, absence of vesicles indicates upregulation of secretion. To substantiate their claim, the authors must provide more conclusive evidence of increased exocytosis. Fig 2 suggests that inhibiting exocytosis-related genes suppresses caspase activation, favoring the proposition that exocytosis is upregulated. However, demonstrating a direct increase in exocytosis in minute cells would bolster their argument. Higher resolution imaging of the exosome marker, with overlayed images, would enhance clarity too.
4. Fig 3 introduces ambiguity regarding the relationship between cell death and exocytosis. The authors assert that dying cells exhibit elevated Wg protein levels compared to the wild-type control but omit an important comparison to the minute disc. Moreover, while Figs 1-2 propose a signaling cascade involving minute>JNK>exocytosis>cell death, Fig 3 implies that cell death regulates exocytosis. The coherence of their model and logic requires clarification - specifically, elucidating the molecular coupling mechanism between cell death and exocytosis.

Specific Points:

1. In Fig S1D, contrary to the authors' claim, cadp2 is not upregulated in a JNK-dependent manner.
2. When detecting multiple proteins in the same tissue, it is advisable for the authors to present overlayed images to enhance the clarity of their findings. Many pictures require higher magnification too.
3. In Fig 1A, the observed upregulation of EGFP-CD63 and Syt1-EGFP may potentially result from an artifactual effect of apoptosis. To validate their findings are specific, the authors should include negative controls that do not exhibit upregulation in dying cells.

Referees cross-commenting

I agree with comments by other reviewers.

Significance

The authors initiate their study by illustrating that minute cells undergo an augmentation in exocytosis-related proteins and calcium flashes (Fig 1). Subsequently, they establish a correlation between JNK-mediated exocytosis and the regulation of caspase activation in minute cells (Fig 2). Further, the authors unveil a dependency of Wg secretion on exocytosis, elucidated in Fig 3. Finally, they discern the involvement of one of the Wg receptors, Fz2, in the cell death/proliferation phenotype of minute cells. Despite the formulation of an intriguing hypothesis, the presented data falls short of robustly supporting their assertions.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, Akai and colleagues study the cellular mechanism leading to high cell turnover in the Minute mutant background in Drosophila wing disc. Previously, the same group characterised an unexpected high rate of proliferation in the wing pouch of the Minute heterozygous larvae, which have been long known to have slower development time. This high rate of proliferation is driven by high apoptosis rate, JNK activation, the release of Dilp8 hormone, and the upregulation of Wg signaling (downstream of JNK) necessary for increased apoptosis and proliferation ( Akai et al., Plos Genetics 2021). Here, the authors address now the molecular link connecting JNK activation and the increased turnover. Using RNAseq and comparing WT, M+/- wing disc with M+/- wing disc upon JNK inhibition, they found a number of genes associated with exocytosis that were upregulated in Minute disc which was lost upon JNK inhibition. The authors first confirm the existence of higher number of exocytic vesicles in Minute wing disc as well as higher calcium activity that were all reduced upon JNK inhibition. Moreover, downregulation of several components of the exocytosis machinery abolished the high turnover rate of Minute wing disc (reducing both apoptosis and proliferation) while leading to the appearance of morphological defects in adult wing, while having no effect in a WT background. Interestingly, Wg accumulates in these exocytosis vesicles, and this accumulation relies on JNK and core exocytosis machinery. The role of Wg is confirmed by reducing the concentration (using heterozygous mutant or RNAi) of the Wg receptor Fz2, which is also specifically downregulated in the cluster of apoptotic cells. Altogether, this study suggests that upregulation of exocytosis by JNK activation is a central regulator of the higher cell turnover in Minute background.

The article is well written and the data overall convincing, including a lot of genetic backgrounds confirming the impact of exocytosis, as well as all the necessary quantifications. Some additional epistatic experiments may help to clearly test to which extend exocytosis is the major downstream target of JNK, and additional control may also help to clarify the sufficiency of JNK for generating such phenotype. Finally, I believe the epistatic link between exocytosis and Wg would deserve more experiments to be definitly proven.

Major comments:

1. It would be important to check how much JNK is sufficient to trigger the exocytosis upregulation. Is the accumulation of Cyt1 and CD63 vesicles in apoptotic cell common to any JNK dependent death or does it require the Minute background ? Could the authors check whether clones expressing HepCA transiently in WT background also accumulate the same vesicles ?
2. It would be relevant to have the status of JNK in Minute disc upon downregualtion of exocytosis. One could imagine some positive feedback between JNK activation, exocytosis, cell death and further JNK activation.
3. So far, the evidence for the epistatic link between exocytosis, Wg and cell turnover is mostly based on colocalization and the similarity of the phenotype but I believe this may need some additional evidences. Ideally one would need to be able to enhance exocytosis and test whether Wg downregulation suppress the phenotype, but I am not sure that upregulation of core exocytosis genes will be sufficient to do this. Alternatively, if Wg is indeed downstream of the upregulation of exocytosis, the reduction of cell turnover upon Wg flattening (e.g. : ftz2-/+ background) should not be enhanced by the reduction of exocytosis. Moreover, could the authors test the status of Wg downstreams targets upon inhibition of exocytosis in the Minute background (for instance, do they see a supression of the nmo-LacZ upregulation that they previously characterised in Minute wing disc in 2021) ?
4. Since Cyt1 and CD63 seem to mostly accumulate in apoptotic cells, it would be interesting to check their status in Minute wing disc upon apoptosis inhibition (e.g. : with H99 or mirRHG).
5. I would remain cautious about some of the statements, notably in the abstract, since some of them are mostly speculative and not really based on any experiments. For instance, the statement "This interaction between dying cells and their neighboring living cells is pivotal in determining cell fate, dictating which cells will undergo apoptosis and which cells will proliferate" is not backed up by any experiment (which would require to show that exocytosis and Wg from the dying cell specifically is required for the survival and proliferation of their neighbours, and/or showing that cell death occurs specifically in cells with local differences in Wg signaling). I would recommend to be more cautious here and us a clear conditional statement.

Other minor point:

The authors document Wg localisation in Minute wing disc upon expression of P35. It would be interesting to describe what is the status of Wg in Rps3+/- compared to WT without p35 (if I am correct, this was done in their previous article, and in that case it would be relevant to describe these former results in the main text).

Referees cross-commenting

I overall agree with all the other comments. It seems that the overall assessment and criticisms (cell autonomy, better characterisation of the status of exocytsosi) are along the same line

Significance

This article is mostly a follow up of a former study published by the same authors in Plos Genetics in 2021. The high turnover (high proliferation and high apoptosis rate) in the minute background was the most surprising observations that was performed previously by the authors, and the role of JNK and Wg was already quite extensively explored in this previous article. The main novelty here is to provide a systematic analysis of expression profile of Minute disc upon JNK inhibition and identify the strong contribution of exocytosis for increased apoptosis and proliferation in Minute wing disc downstream of JNK. In that sense, I believe these are interesting results, but novelty remains a bit limited (at least relative to their previous study). Still, these results could be interesting for the community studying cell competition, ribosomopathies, and growth regulation specially in Drosophila (so mostly for a specialised readership).

I have expertise in epithelial cell death, apoptosis, and cell competition, specially in Drosophila. I feel confident to evaluate every part of the article.

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Reply to the reviewers

Manuscript number: RC-2024-02352

Corresponding author(s): Elise, Belaidi

1. General Statements

We would like to thank the reviewers for their constructive suggestions and comments. We hope that the “point by point answer” and the revision plan proposed below will convince the reviewers and the editor.

We thank the reviewer 1 for his/her comments. We would like to specify that the involvement of HIF-1 in IH-induced mitochondrial remodeling has indeed been initiated by RNA-seq analysis and confirmed in a cell-based model as well as in wild-type and HIF-1a+/- heterozygous mice subjected to intermittent hypoxia (IH). In vivo, we originally demonstrated that Metformin reversed IH-induced increase in myocardial infarct size through AMPKa2 and, we proposed that metformin could modify HIF-1 activity. Then, we validated our hypothesis in an in vitro model allowing to demonstrate that Metformin, by increasing HIF-1a phosphorylation decreases its activity. We acknowledge that we used several models and this is the reason why we detailed as much as possible the Materials and Methods section including all models, experimental sets designed and methods details. We hope that the point by point response that we made for the reviewer 1 will increase the clarity of our work and we hope that the new results provided will strengthen the evidences concerning the mechanisms by which metformin can inhibit and modulate the deleterious impact of HIF-1 on IH-induced an increase in myocardial infarct size.

We thank the reviewer 2 for his/her conclusion highlighting that “our work opens new avenues for exploring the potential effects of metformin as a modulatory of HIF-1𝛂 activity in obstructive sleep apnea syndrome”. We hope that the clarifications and/or justifications brought will convince him/her.<br /> We thank the reviewer 3 for having underlined that “metformin induces HIF-1α phosphorylation, decreases its nuclear localization and subsequently HIF-1 transcriptional activity are very much interesting” and for having highlighting that “our study is convincing”. We hope that the justification and the corrections brought in the point by point answer will convince him/her.

Alltogether, as underlined by the 3 reviewers, our study is very interesting for translational science in the fields of cardiovascular, respiratory and sleep medicine. We hope that the point by point answer and the revision plan proposed will allow the publication of our article in EMBO Molecular Medicine.

2. Description of the planned revisions

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Please find below the revision that we plan to address to answer to the questions of the reviewer 1.

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Figure 1 - it would be helpful to list all of the DEGs (what genes are changed?). Including the expression of HIF-1α and PHD isoforms would be informative. If there is a robust HIF-1α signal, changes in the expression of HIF and PHD isoforms would be anticipated. Fig 1F - with regards to glycolysis and hypoxia pathway analysis, most of the DEGs are not canonical HIF-1α/hypoxia targets.

Figure 1 aimed at better understanding and manipulate the well-recognized involvement of HIF-1 in response to our specific IH stimulus (Semenza, Physiology 2009; Belaidi, Pharmacol & Ther. 2016). __The results provided by the RNA-seq analysis shows that IH induces cardiac oxidative and metabolic stress which are inter-related with HIF-1 activation. __We did not claim that these genes are HIF-1 targets genes. The RNA seq analysis did not allow to reveal HIF-1a and PHD1-3 transcript as the most dysregulated genes of the panel. In case of publication, bulk data and DEGS will be provided in an online file. We agree with the reviewer that the list of the 40 up and down-regulated genes would be very informative and would increase the value of the paper. Thus, we plan to add the name of the 40 up and down-regulated genes on Figure 1B.

Figure 5G-I, show cytoplasmic HIF1a as well as nuclear.

Alternatively, why not use IHC for subcellular localization?

We think that the comments of the reviewer 1 concern Fig.4G-I and not 5G-I. In this figure, we showed that IH increases nuclear HIF-1____a____ expression compared to N condition and that this IH-effect is abolished in mice treated with Metformin, suggesting that, upon IH, Metformin impacts HIF-1__a __nuclear content and subsequently, its activity. The nuclear localization of HIF-1a is the most relevant mean to indicate its activation. We agree with the reviewer that IHC also allows for the indication of the nuclear localization of HIF-1a. Indeed, we previously performed IHC on nuclear HIF-1a localization and demonstrated that IH increased HIF-1a nuclear localization by IHC that was corroborated by Western-blot (Moulin S, TACD, 2020). Western-blot and IHC are both semi-quantitative techniques with different process of analyses. In this study, we choose Western-blot because we have the material to perform this technique and because IHC is associated with an analysis process (size of a slice, areas to analyze, colorimetry…) that is more complex than the analysis process of Western-blot (densitometry solely).

While the nuclear localization of HIF-1a is the most relevant mean to indicate its activation; it could be interesting to see that HIF-1a cytosolic content was neither modify by IH nor by Metformin. This would also corroborate the results of the RNA-seq that did not demonstrate any difference in DEGs of HIF-1a or of other members of the HIF family. This would also confirm that Metformin plays a major role on HIF-1 activaty regulation (and not transcription) in the context of IH.

Thus, we plan to perform a Western-blot of HIF-1a on cytosolic extracts of hearts from mice exposed to N or IH and treated or not with Metformin. These extracts are already available and Western-blot would be performed and replicated in 3 weeks. We could also provide a Western-blot in order to show the purity of our extraction protocol (nucleus vs cytosol).

Figure 5F, it would be important to show the levels of expression of HIF1a in these experiments. Are there positive and negative controls that the authors could use for HIF21a activity in this experiment?

In our manuscript, we aimed at demonstrating that Metformin decreases HIF-1 activity in a context of strong HIF-1____a____expression and/or stabilizion those mimics what happens after chronic IH in mice (Belaidi E, Int J Cardiol 2016, Moulin S, Ther Adv Chronic Dis 2020) and in apneic patients (Moulin S, Can J Cardiol 2020). Thus, we used a transfection allowing to overexpress HIF-1a that is one of the best means to increase HIF-1 activity. In the Figure 1 below, HA-HIF-1α-WT Addgene AmpR and 5 HRE GFP AmpR plasmids co-transfection induced a decrease in H9c2 viability and an increase in GFP-positive cells that were not observed in H9c2 transfected with pcDNA 3.1 HA-C AmpR (negative control). __This validates our in vitro model as a good positive control to mimic IH consequences. __ However, we agree with the reviewer that we could add a supplemental figure or a panel demonstrating that our transfection induced an increase in HIF-1a expression. Thus, we will perform a Western-blot targeting HIF-1a on H9c2 transfected with the control plasmid (pcDNA 3.1 HA-C AmpR) or the plasmid allowing the overexpression of HIF-1a (HA-HIF-1α-WT AmpR). This work would be performed in 2 months.

Moreover, we already improved the lisibility of the Figure 5F to clarify the experimental conditions (table inserted under the graphic); we also completed the Materials and Methods section to specify the plasmid used (modifications are in red in the manuscript).

Figure to see on the downloaded file.

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Figure 1 : GFP fluorescence in H9c2 cells transfected with pcDNA 3.1 HA-C AmpR (control condition) or HA-HIF-1α-WT AmpR (positive control, overexpression of HIF-1a) and 5 HRE-GFP AmpR plamids and treated with CoCl2 (1mM, 2h); magnification x100.

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This paragraph concerns only the point 4 of the fifth question.

In these experiments, as well as subsequent studies, it would be very informative to use a specific AMPK activator e.g. MK-8772, to compare with metformin. It is well known that metformin has a number of other targets in addition to AMPK.

We agree with the reviewer that metformin has pleiotropic effect. Very interestingly, we demonstrated that the reduced-infarct size is not related to the metabolic systemic effect of metformin since it failed to improve the IH-induced insulin resistance while it improves the answer to insulin in normoxic mice (supplemental Figure S3B). This demonstrates that in our model, the cardioprotective effects of Metformin are independent of a potential systemic effect. Then, we demonstrated that metformin protects the heart against ischemia-reperfusion through AMPK____a____2 activation by using AMPK____a____2KO exposed to IH in which Metformin failed to decrease infarct size (Fig.4N). MK-8772 is not widely used in vivo models. Moreover a recent study indicates that chronic treatment with MK-8772 (14 days 1 month in mice and rats, respectively) induces cardiac hypertrophy characterized by an increase in heart weight (Myers R, Science 2017). In vivo experiments with MK-8772 would be not clinically relevant as the use of metformin that is already used in clinic. However, in order to improve the mechanistic investigation concerning the role of AMPKa2 activation on inhibiting HIF-1 activity, we propose to perform the in vitroexperiments performed in Figure 5 with a specific allosteric small-molecule activator of AMPKa2 such as 991.

We plan to:

-Expose H9c2 to CoCl2 and treat them with 991 in order to measure HIF-1a phosphorylation.

-Transfect H9c2 with our plasmids HA-HIF-1α-WT AmpR and 5 HRE GFP AmpR and treat them or not with 991 in order to measure HIF-1 activity (GFP fluorescence). These experiments would be performed in 2 months.

__Please find below the revision that we plan to address to answer to the second question of the reviewer 2. __

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2) The WB images were cut and pasted. Please add the original images

We acknowledge the reviewer's comment and will address it by submitting a supplementary file containing the uncropped immunoblot images. Since this file already exists, our plan is to standardize it by providing, for each slide (immunoblot), all relevant information pertaining to our experiments, including groups, molecular weight markers, cutting, membrane stripping, and other pertinent details.

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

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__Please find below the answers or the revisions that have already been incorporated in response to the comments of the reviewer 1. Please note that we provided new results and new figures at the discretion of the reviewer, but we are ready to insert them as figures or supplemental figures in a new revised manuscript if the reviewers and the editor think that it would improve our message. __

Was mitochondrial content in the hearts after IH experiment measured e.g. mtDNA measurements? IH results in mitochondrial dysfunction/reduced mitochondrial content. It would have been good to show mitochondrial dysfunction by doing basic functional experiments (e.g. TMRM/MitoROS imaging etc.) by isolating cardiomyocytes from the N and IH experiments.

We thank the reviewer for these questions about the mitochondrial function and content. The impact of IH on mitochondrial function has already been demonstrated in heart (Moulin S, Antioxydants 2022, Wei Q, Am J Physiol 2012). __Indeed, we previously showed that mitochondria isolated from hearts of mice exposed to IH had a decrease in maximal respiration in complex I and II that was not observed in HIF-1_a_+/- ____mice (Moulin S, Antioxidants 2022), indicating that HIF-1 is responsible for IH-induced mitochondrial dysfunction. __

Figure 4 shows that Metformin abolished IH-induced mitochondrial remodeling similar to what we observed in HIF-1a+/-(Figure 2). This means that treating with Metformin or partially deleting the gene encoding for HIF-a induce the same impact on IH. Then, we demonstrated that Metformin can control HIF-1 activation and we concluded that metformin could be cardioprotective through inhibiting HIF-1 activation and subsequent mitochondrial stress and remodeling. In this study, we focused on the effects of Metformin on HIF-1 and we did not aim at directly test the effect of metformin on mitochondrial function. Actually, metformin exhibits biphasic effects on bioenergetics of cardiac tissue depending on the modality of administration (i. e. single injection, time of administration during an ischemia-reperfusion procedure); the dose administered and the tissue studied (i. e. hiPSC-CMs, isolated mitochondria…) (Emelyanova N, Transl Res 2021). But, we collected some data that we would like to submit at the discretion of the reviewer. Using oximetry, we measured maximal respiration in complex 1 and 2 on isolated mitochondria from hearts of mice exposed to N, IH and treated or not with metformin during the exposure__. While we observed that IH decreases maximal respiration in complex 1 and 2, we did not find any effect of metformin on mitochondrial respiration alteration induced by IH (Figure 2A, B). Using spectrofluorometry, we measured the mitochondrial membrane potential using TMRM; __we did not find any modification of membrane potential in IH or Metformin-treated mice (Figure 2C). Because we previously did not observe any impact of IH on mtDNA/gDNA ratio (Figure 2D), we did not test metformin on this parameter.

To conclude, we think that these results are not directly in the scope of our work but if the reviewer thinks that they deserve to be discussed, we could add them in a supplementary figure.

Please, see the figure on the dowloaded file

Figure 2 : Mice were exposed to 21 days of Normoxia (N) or Intermittent Hypoxia (IH) (1-min cycle of FiO2 5%-21%) and treated with vehicle (Vh, CmCNa 0.01%, 0,1ml.10g-1) or Metformin (Met, 300mg.kg-1.d-1). (A, B) Mitochondrial function __was measured by oximetry with sequential addition of substrate (state 2), ADP (200mM, state 3, maximal respiration) and oligomycin (12.5 mM, state 4) ; quantification of O2 consumption for NADH-linked mitochondrial respiration (complex I-glutamate-malate, GM, 20mM) (A), and for FADH2-linked mitochondrial respiration (complex II-succinate, S, 5mM, in presence of complex I inhibition by rotenone, 6.25mM) (B) (n=8). (C) Mitochondrial membrane potential measured by spectrofluorometry after Tetramethylrhodamine Methyl Ester (TMRM, 0.2mM) in presence of GM (basal condition), maximal respiration (ADP) and uncoupling condition Carbonyl cyanide 4-(trifluoromethoxy)phenylhydrazone, FCCP, 3mM); fluorescence intensity is expressed relative to fuorescence at baseline (before GM) (n=8). (D__) Mitochondrial content assessed by the expression of mitochondrial DNA (mtDNA, COX1) relative to genomic DNA (gDNA, ApoB) measured after PCR (n=6); *p

Fig 2A-D - CoCl2 is not a good model to mimic hypoxia due its effect on disrupting iron homeostasis in cells, which can mean that some of the effects are due to changes in iron levels and not HIF stabilisation.

The capacity of CoCl2 to chelate iron is the main property of CoCl2 that we used in order to stabilize HIF-1____a____. Actually, prolyl-4-hydroxylases need Fe2+ to hydroxylate HIF-1____a____ and induce its degradation. __Then, intermittent hypoxia (IH) is characterized by very rapid changes in PO2. This stimulus was designed to reproduce sleep apnea syndrome and its associated disorders (i. e. insulin-resistance, hypertension, increase in myocardial infarct size). This model was firstly developed and validated in rodents (Dematteis M, ILARJ 2008, Belaidi E, Eur Resp Rev 2022, Harki , Eur Resp J 2022). Compelling evidence indicate that the involvement of HIF-1 in IH-deleterious consequences is related to the repetitive phases of oxygenation and especially to IH-induced oxidative stress (Semenza Physiology 2009, Belaidi Pharmacol. & Ther 2016). In order to increase the level of mechanistic insights on HIF-1, we next attempted to optimize in vitro models. A device was developed by Minoves et al. (Minoves M, Am J Physiol, 2017) to expose endothelial and cancer cells to IH. __However, as illustrated below, this device does not mimic efficient rapid hypoxia-reoxygenation cycles able to induce cardiac cell death (Figure 3A). However, CoCl2 decreases H9C2 viability by 60% (Figure 3B) that is associated with a sustained stabilization of HIF-1____a (Figure 3C,D). Thus, we choose this in vitro model as it replicates cardiac cell death and HIF-1_a_overexpression or stabilization which we similarly observe in our in vivo model and in apneic patients (Moulin S, Can J Cardiol 2020).

Please see the figure on the dowloaded file

Figure 3 : (A-B) Cell viability measured by 3-(4,5-dimethylthiazol-2-yl)-2,5-diphenyl-2H- tetrazolium bromide (MTT) of H9c2 cells exposed to 6 hours (h) of repetitive cycles of Intermittent hypoxia (2 minutes (min) PO2 16% - 2 min PO2 2%) (n=3) (A) or treated with CoCl2 (1mM, 2h) (n=6) (B). (C-D), __quantification of __total ____HIF-1____𝛂 expression relative to tubulin (C) and representative image of Wetsern-blot (D) (n=2-3); *p****p*

Fig. 2K, change in BNIP3 expression is modest, but change in Parkin is very dramatic. BNIP3 is a HIF-1α target but Parkin is not, so it is plausible that mitophagy could be occurring through a HIF-1α independent mechanism.

Fig. 2K is a representative panel of 2-3 independent experiments. The quantification reported in Figures 2I and 2J demonstrated a significant decrease in BNIP3 and Parkin expressions in HIF-1a heterozygous mice exposed to Intermittent Hypoxia (IH) compared to HIF-1a+/+ mice exposed to IH. While we acknowledge that only BNIP3 is a direct target of HIF-1, the role of HIF-1 in IH-induced auto/mitophagy is demonstrated by our experiments performed in HIF-1____a____heterozygous mice. This shows an important role for HIF-1 without excluding any impact of HIF-1a independent mechanisms.

What are we meant to be looking at in Fig 2L?

Figure 2L aims at illustrating mitochondrial remodeling under IH. Stars indicate that mitochondria have abnormal fate in IH conditions and arrows point autophagosomal membrane and formation. This figure was magnified to be clearer (please see new Figure 2L).

Figure 3B-C, the reduction in pT172 on AMPK is modest. It would be good to include pACC as a downstream target for AMPK.

As recommended by the reviewer, we inserted in the manuscript the quantification of 79Ser-P-ACC/ACC western-blot as well as a representative image of the Western-blot (See new Figure 3). We also modified the legend of the figure. 79Ser-P-ACC is an important target of AMPK; however, in our experimental conditions, its phosphorylation is not associated to the decrease in AMPK phosphorylation. This could be explained by many points. First, Metformin was administered every day and hearts were harvested 24 hours later after the last administration. Most studies demonstrating a modification of AMPK and ACC phosphorylation are experiments performed in vitro or directly (less than 1 hour) after a single dose of Metformin administration. In the context of myocardial ischemia-reperfusion, Yin et al. showed an increase in P-AMPK/AMPK directly after Metformin treatment without showing any data on P-ACC/ACC (Yin M; Am J Physiol 2011); similar data were published in models of chronic cardiac diseases (Soraya H, Eur J Pharmacol, Gundewar S, Circ Res 2009). Second, in line with the previous explanation, the lack of effect of metformin on P-AMPK and/or P-ACC in rodent models could be explained by its rapid distribution (Sheleme T Clin Pharmacokinetics of Metformin 2021) and its short half-life that is around 3.7 hours in mice (Junien N, Arch Int Pharmacodyn Ther 1979).

To conclude, since we performed all our analysis 24h after the last treatment and exposure to hypoxia, we argue that the slight but significative decrease in AMPK phosphorylation that we observed in our study highlight a robust impact of chronic IH. However, this would be elegant to confirm this result by measuring AMPK through its phosphorylation capacity (Cool B, Cell Metab 2006, Ducommun S, Am J Physiol 2014). We already sent hearts from mice exposed to Normoxia or Intermittent Hypoxia to Luc Bertrand’s lab (IREC, Belgium) where they used to perform this assay.

Fig. E-G, show data for mice treated with vehicle.

In Figure 4 I-J­­, we demonstrated that Metformin significantly decreases infract size in IH condition only and this validates our main hypothesis regarding the specific beneficial effect of this drug in the context of chronic IH. __In order to show that the cardioprotective effect of Metformin is relative to AMPKa2 activation, we first showed that 79Ser-PACC/ACC, one of the main downstream targets of AMPKa2 was increased (Fig. E-G). We did not find it necessary to does not exhibit cardioprotective effects. However, as shown in Figure 3 below, __Metformin also increases 79Ser-PACC/ACC in Normoxic mice validating the treatment. Thus, in normoxic conditions, AMPK____a____2 activation does not exert any cardioprotective effect. We acknowledge that this reinforces our result about the specificity of AMPK____a____2 activation by Metformin under chronic IH condition. We could add this Figure in supplemental results.

Please, see the figure on the dowloaded file

Figure 4 : AMPK activation in Normoxic mice treated with vehicle (Vh, CmCNa 0.01%, 0,1ml.10g-1) or __ __metformin (Met, 300mg.kg-1.d-1 : __ __172Thr-P-AMPK/AMPK (A) and 79Ser-P-ACC/ACC (B) ratio and representative image of Western-blot (C) (n=3-6); *p

Fig. 3K - what cre is used for the a2 KO mice?

As written in the Materials and methods section, AMPKa2KO mice are not inducible Knock-out mice. Constitutive AMPKα2 knockout mice were kindly generated by Benoit Viollet (Viollet B, JCI, 2003).

Include normoxia data for the a2 KO mice studies.

The question of the reviewer concerning the cardioprotective effects of metformin is interesting but is not aligned with the objectives of the study. Indeed, we did not treat normoxic mice with Met for several reasons. First, the objective of the study was to find a cardioprotective strategy against IH-induced an increase in infarct size. Second, Fig. 3I shows that Met significantly reduced infarct size upon IH only; this suggests that AMPK____a____2 activation is specifically involved in IH-induced increase in infarct size but not in reducing infarct size in normoxic mice. Moreover, the beneficial impact of metformin in standard models of myocardial ischemia-reperfusion is controversial and has been extensively discussed (Foretz et al. Cell Metab. 2014). Overall, using AMPKa2 mice was legitimated in the context of IH only. We validated the involvement of AMPKa2 in the cardioprotective effect of metformin especially in IH conditions.

Figure 5G, what is the rationale for switching to CoCl2 in the mice to prove metformin reduced HIF-1α expression? Why not use reduced O2 tension in mice.

We respectfully disagree with the reviewer since mice were exposed to N and IH and treated or not with Metformin to demonstrate that this drug abolished IH-induced increase in HIF-1a nuclear expression (Figure 4 H, I). The same model was used in Figure 3 to demonstrate the impact of Metformin on infarct size. Fig. 5G was conducted to demonstrate the potential link between AMPKa2 and HIF-1a phosphorylation in basal conditions of AMPKa2 content or in absence of AMPKa2 (AMPKa2-/- mice). The single presence of AMPK____a____2 demonstrates an increase in HIF-1____a____ phosphorylation if its stabilization is increased by CoCl2; this was not observed in AMPK____a____2-/- mice highlighting that AMPK____a____2 plays an important role in HIF-1____a phosphorylation.

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Please find below the answer to the first question asked by the reviewer 2.

1) Why did authors choose the IH protocol illustrated in Fig. S1A

The choice of the hypoxic stimulus was based on literature and mainly on our recognized expertise in preclinical studies aiming at better understanding obstructive sleep apnea syndrome (OSA); a chronic pathology associated with several comorbidities such as diabetes, hypertension… We are conscious that the hypoxic stimulus used in this study is very severe, with a nadir arterial oxygen saturation (SaO2) around 60%. However, this experimental design is required to induce detrimental cardiovascular effects __in the absence of any confounding factors (i.e., obesity) or genetic susceptibility for complications (i. e. genetic susceptibility to hypertension) (Dematteis M, ILARJ 2008). Especially in the context of myocardial infarction, exposing rodents to 14 to 21 days of IH at 5% and subjected them to a myocardial ischemia-reperfusion protocol allows us to reproduce the increase in infarct size in rats (Belaidi E, J. Am. Coll. Cardiol., 2009; Bourdier G, Am J Physiol, 2016) and in mice (Belaidi E, Int J Cardiol 2016; Moulin S, Can J Cardiol 2020) similar to what has been observed in apneic patients (Buchner S, EHJ 2014). __Moreover, we recently conducted a meta-analysis based on 23 preclinical studies aiming at investigating the impact of the IH pattern (duration, FiO2, repetition of cycles…) on infarct size and cardiomyocyte death (Belaidi E, Eur. Resp. J 2022). We showed that IH significantly increases infarct size when IH is applied several days (especially 14 to 21 days) and when FiO2 is around 5%; whereas IH decreases infarct size when it is applied a single day at a FiO2 at 10%. This meta-analysis provided the confirmation that we need to apply a chronic and severe stimulus to reproduce an increase in infarct size that is observed in apneic patients which are exposed every day, during several days to a decrease in SaO2. If the reviewers and the editor consider that this point should be discussed in the discussion section, we will be happy to include it.

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Please find below the answers or the revisions that have already been incorporated in response to the comments of the reviewer 3. They appear in red in the new manuscript except the modifications performed in the “references” section which appear in black.

1 The authors used H9c2 rat cardiac cells in vitro experiments although they used mouse model in vivo experiments. Using mouse P19.CL6 cardiac cells instead of rat H9c2 cells may much clearer. Why the authors did not use P19.CL6 cells should be explained.

We thank the reviewer for his/her suggestion. P19CL6 cell line has been isolated from pluripotent P19 embryonal carcinoma (EC) cells after long term culture under conditions for mesodermal differentiation (Habara-Ohkubo A, Cell Struc Funct 1996). Therefore, these cells are mostly used to ____study the differentiation of cardiac muscle. Indeed, they were recognized to avoid large variations in the differentiation rates which were extensively reported (Mueller I, J Biomed Biotechnol 2010). To our knowledges no ventricular non-beating mice cell line. In this study, we used H9c2 which are extensively used and recognized as a gold standard cellular model to study the biology of cardiomyocytes including mechanisms involved in cardiac ischemia-reperfusion injury (Paillard M, Circulation, 2013; Zhang G Circulation 2021__), cardiac hypertrophy__ (Zhang N, Cell Death Diff 2020; Hu H, Cardiovasc Res 2020), intra-organites calcium exchanges (Moulin S, Antioxydants, 2022, Paillard M, Circulation, 2013) as drug testing (Beshay NM, J Pharm and Tox Methods, 2007). Recently, H9c2 and P19.CL6 were exposed to intermittent hypoxia (70 cycles of FiO2 1% (5 min) - FiO2 21% (10%)) in order to “mimic OSA” and investigate the transcription level of a pool of genes. The authors show some similiraties and differences of mRNA expression between the two cell lines that, indeed, could be attributed to variations in the cell origin (Takasawa S, IJMS 2022). However, in this study, there are no experiment allowing to assess the state of cardiac cells (apoptosis, life, metabolism, remodeling) questioning the pathophysiologic transposability of the model. Moreover, the number of experiments conducted on H9C2 (pubmed references : 7000 vs 100 for P19.CL6) to understand the mechanism involved in acute and chronic cardiac pathologies makes our choice confident and relevant.

2 The authors described, "The protocol was approved by the French minister (APAFIS#23725-2020012111137561.v2)." in Animals (page 16) without showing approval date, the authors should clearly show the approval date together with their approval numbers.

We added the approvement date in the materials and methods section. It was approved on February 20, 2020.

3 In Figure 2 L, scale bar(s) should be added because figures are magnified and/or reduced by printer.

We agree with the reviewer that scale bars were not visible; we highlighted them.

4 In Figure 3J and 3N, scale bar(s) should be added.

Scale bars have been now added on figures 3J and 3N. All pictures were acquired at the maximal zoom of a camera placed at an equal distance from the slices. Then, analyses were performed, slice per slice, with Image J with the same zoom (x5 to get an image at 100%). In this context, scale was added based on a photo of slice taken close to a ruler.

5 In introduction, "HIF-1" should be changed to "hypoxia-inducible factor 1 (HIF-1)".

Thank you, we replaced HIF-1 by Hypoxia Inducible Factor-1 (HIF-1) in the introduction section.

6 In Results, "Angpt1, Txnip, Nmrk2, Nuak1 or Pfkfb1" should be changed to "Angiopoietin 1 (Angpt1), Thioredoxin-interacting protein (Txnip), Nicotinamide riboside kinase 2 (Nmrk2), NUAK family SNF1-like kinase 1 (Nuak1) or 6-phosphofructo-2-kinase/fructose-2,6-biphosphatase 1 (Pfkb1)".

We did the modification and let the abbreviation in italic since it concerns genes name.

7 In Chronic intermittent hypoxia, "FiO2" should be changed to "FiO2".

Thank you, we changed it in the materials and methods section.

8 In Western-blot, "Bio-Rad, California, USA" should be changed to "Bio-Rad, Hercules, CA".

Thank you, we did it.

9 In Western-blot, what "tubulin" (α-tubulin or β-tubulin) should be clarified.

We agree with the reviewer that this point should be specified; α-tubulin was stained, we added the “α”.

As mentioned below, we have done all the modifications required by the reviewer in the references section.

10 In Ref. 8, "Antioxidants (Basel) 11 (2022)" should be changed to "Antioxidants (Basel) 11, 2326 (2022)".

Done

11 In Ref.10, "Pharmacol Ther (2016)" should be changed to "Pharmacol Ther 168, 1-11 (2016)".

Done

12 In Ref.13, "Antioxidants (Basel) 11 (2022)" should be changed to "Antioxidants (Basel) 11, 1462 (2022).

Done

13 In Ref. 21, "Diabetes (2017)" should be changed to "Diabetes 66, 2942-2951 (2017)".

Done

14 In Ref. 28, "Adv Biol (Weinh), e2300292 (2023)" should be changed to "Adv Biol (Weinh), 8, 2300292 (2023)".

Done

15 In Ref. 37, "J Am Heart Assoc 6 (2017)" should be changed to "J Am Heart Assoc 6, e006680 (2017)".

Done

16 In Ref. 41, "Eur Respir Rev 32 (2023)" should be changed to "Eur Respir Rev 32, 230083 (2023)".

Done

17 In Ref. 46, "Int J Mol Sci 22 (2020)" should be changed to "Int J Mol Sci 22, 268 (2021)".

Done

18 In Ref. 47, "Int J Mol Sci 21 (2020)" should be changed to "Int J Mol Sci 21, 2428 (2020)". Done

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

__Please find below the answers to the comment of the reviewer 3 that we cannot provide and that is not in the scope of the study. __

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Figure 5, multiple phosphorylation sites have been identified on HIF1a. What is the nature of the Thr/SerP-HIF1a antibody? It would be far more preferable (essential?) to identify the site(s) within HIF1a that are phosphorylated by AMPK.

The antibody was provided by Cell Signalling, ref. 9631. Phospho-(Ser/Thr) Phe Antibody detects phospho-serine or threonine in the context of tyrosine, tryptophan or phenylalanine.

The identification of the Phosphorylation sites will require a long-time consuming phosphoproteomic analysis and subsequent functional validation in vivo and in vitro (directed mutagenesis, knock-in mice, …) which are out of the scope of our paper.

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Referee #3

Evidence, reproducibility and clarity

Although the findings that metformin inhibits intermittent hypoxia (IH)-induced mitophagy in myocardium and decreases hypoxia-inducible factor 1-α (HIF-1α) nuclear expression in mice subjected to IH. In vitro demonstrated that metformin induces HIF-1α phosphorylation, decreases its nuclear localization and subsequently HIF-1 transcriptional activity are very much interesting, numbers of points need clarifying and certain statements require further justification. These are given below.

Point

1. The authors used H9c2 rat cardiac cells in vitro experiments although they used mouse model in vivo experiments. Using mouse P19.CL6 cardiac cells instead of rat H9c2 cells may much clearer. Why the authors did not use P19.CL6 cells should be explained.
2. The authors described, "The protocol was approved by the French minister (APAFIS#23725-2020012111137561.v2)." in Animals (page 16) without showing approval date, the authors should clearly show the approval date together with their approval numbers.
3. In Figure 2 L, scale bar(s) should be added because figures are magnified and/or reduced by printer.
4. In Figure 3J and 3N, scale bar(s) should be added.
5. In introduction, "HIF-1" should be changed to "hypoxia-inducible factor 1 (HIF-1)".
6. In Results, "Angpt1, Txnip, Nmrk2, Nuak1 or Pfkfb1" should be changed to "Angiopoietin 1 (Angpt1), Thioredoxin-interacting protein (Txnip), Nicotinamide riboside kinase 2 (Nmrk2), NUAK family SNF1-like kinase 1 (Nuak1) or 6-phosphofructo-2-kinase/fructose-2,6-biphosphatase 1 (Pfkb1)".
7. In Chronic intermittent hypoxia, "FiO2" should be changed to "FiO₂".
8. In Western-blot, "Bio-Rad, California, USA" should be changed to "Bio-Rad, Hercules, CA".
9. In Western-blot, what "tubulin" (α-tubulin or β-tubulin) should be clarified.
10. In Ref. 8, "Antioxidants (Basel) 11 (2022)" should be changed to "Antioxidants (Basel) 11, 2326 (2022)".
11. In Ref.10, "Pharmacol Ther (2016)" should be changed to "Pharmacol Ther 168, 1-11 (2016)".
12. In Ref.13, "Antioxidants (Basel) 11 (2022)" should be changed to "Antioxidants (Basel) 11, 1462 (2022).
13. In Ref. 21, "Diabetes (2017)" should be changed to "Diabetes 66, 2942-2951 (2017)".
14. In Ref. 28, "Adv Biol (Weinh), e2300292 (2023)" should be changed to "Adv Biol (Weinh), 8, 2300292 (2023)".
15. In Ref. 37, "J Am Heart Assoc 6 (2017)" should be changed to "J Am Heart Assoc 6, e006680 (2017)".
16. In Ref. 41, "Eur Respir Rev 32 (2023)" should be changed to "Eur Respir Rev 32, 230083 (2023)".
17. In Ref. 46, "Int J Mol Sci 22 (2020)" should be changed to "Int J Mol Sci 22, 268 (2021)".
18. In Ref. 47, "Int J Mol Sci 21 (2020)" should be changed to "Int J Mol Sci 21, 2428 (2020)".

Significance

the study is convincing

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Referee #2

Evidence, reproducibility and clarity

In the submitted paper by Moulin et al., the authors investigated the effect of metformin treatment (an oral anti-diabetic drug and AMPK activator) on cardiac response to ischemia-reperfusion in mice exposed to intermittent hypoxia (IH), a major component of obstructive sleep apnea (OSA). The data demonstrates that IH alters the expression profile of a subset of genes involved in myocardial mitochondrial dysfunction, such as Angpt1, Txnip, Nmrk2, Nuak1 or Pfkfb1, hallmark genes of hypoxia and glycolysis. In H9c2 cells treated with CoCl2 with or without chloroquine, the authors claim that IH induces mitophagy through HIF-1 activation, associated with an increase in autophagic flux. This effect is abolished in HIF-1𝛂+/- mice. Metformin treatment in mice reverses IH-increased in infarct size through AMPK activation, decreases IH-induced mitophagy and HIF-1𝛂 nuclear localization.

The paper is interesting but needs some clarifications:

1. Why did authors choose the IH protocol illustrated in Fig. S1A)
2. The WB images were cut and pasted. Please add the original images

Significance

This work opens new avenues for exploring the potential effects of metformin as a modulatory of HIF-1𝛂 activity in obstructive sleep apnea syndrome.

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Referee #1

Evidence, reproducibility and clarity

Summary: The manuscript by Moulin and colleagues begins by exploring changes in gene expression in mice subjected to intermittent hypoxia (IH). Based on these results, the authors postulate a link with HIF1a, and so use a cell-based model to examine this link. Next, the authors turn to AMPK showing that IH decreases Thr172 phosphorylation on AMPK. In view of this, the authors use metformin as a way to activate AMPK during IH and monitor necrosis in hearts following ischemia-reperfusion. Metformin treatment reduces necrosis in mice subjected to IH. Mechanistically, the authors link decreased HIF1a activity following AMPK activation in response to metformin and suggest that this is due to phosphorylation of HIF1a by AMPK. Overall, this reviewer found some of these connections to be quite weak and in some cases the evidence supporting the claims was equivocal. In some instances, the lack of appropriate controls or the use on non-specific reagents, undermined the findings. Adding to these issues, there was a lack of experimental detail both in the Figure legends and in the M&M section. Below I have listed some of the major concerns that if addressed satisfactorily would greatly strengthen the manuscript.

Major Comments

Major Points

1. Figure 1 - it would be helpful to list all of the DEGs (what genes are changed?). Including the expression of HIF-1α and PHD isoforms would be informative. If there is a robust HIF-1α signal, changes in the expression of HIF and PHD isoforms would be anticipated. Fig 1F - with regards to glycolysis and hypoxia pathway analysis, most of the DEGs are not canonical HIF-1α/hypoxia targets.
2. Was mitochondrial content in the hearts after IH experiment measured e.g. mtDNA measurements? IH results in mitochondrial dysfunction/reduced mitochondrial content. It would have been good to show mitochondrial dysfunction by doing basic functional experiments (e.g. TMRM/MitoROS imaging etc.) by isolating cardiomyocytes from the N and IH experiments.
3. Fig 2A-D - CoCl2 is not a good model to mimic hypoxia due its effect on disrupting iron homeostasis in cells, which can mean that some of the effects are due to changes in iron levels and not HIF stabilisation. Fig. 2K, change in BNIP3 expression is modest, but change in Parkin is very dramatic. BNIP3 is a HIF-1α target but Parkin is not, so it is plausible that mitophagy could be occurring through a HIF-1α independent mechanism. What are we meant to be looking at in Fig 2L?
4. Figure 3B-C, the reduction in pT172 on AMPK is modest. It would be good to include pACC as a downstream target for AMPK. Fig. E-G, show data for mice treated with vehicle. Fig. 3K - what cre is used for the a2 KO mice? Include normoxia data for the a2 KO mice studies. In these experiments, as well as subsequent studies, it would be very informative to use a specific AMPK activator e.g. MK-8772, to compare with metformin. It is well known that metformin has a number of other targets in addition to AMPK.
5. Figure 5G-I, show cytoplasmic HIF1a as well as nuclear. Alternatively, why not use IHC for subcellular localisation?
6. Figure 5, multiple phosphorylation sites have been identified on HIF1a. What is the nature of the Thr/SerP-HIF1a antibody? It would be far more preferable (essential?) to identify the site(s) within HIF1a that are phosphorylated by AMPK.
7. Figure 5F, it would be important to show the levels of expression of HIF1a in these experiments. Are there positive and negative controls that the authors could use for HIF21a activity in this experiment?
8. Figure 5G, what is the rationale for switching to CoCl2 in the mice to prove metformin reduced HIF-1α expression? Why not use reduced O2 tension in mice.

Minor Comments

Nothing at this stage of the process. The authors need to focus on the major points to improve the quality of the manuscript.

Significance

Overall, the lack of robust mechanistic studies makes it difficult to fully interpret the impact of the study.

This feels like a preliminary exploration of a potentially important biological system, but the manuscript seems incomplete and requires more attention to details.

Upon revision, I think the study would be of interest to basic and clinical researchers working in the filed of cardiac metabolism and hypoxia.

My expertise is in metabolism and cell signalling.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Here, Ahel et al characterize complex composiiton, chromatin binding, and respressive function of ADNP2. First they show that ADNP2 forms a complex with CHD4 and HP1b, very similar to, although biochemically distinct from, the ChAHP complex formed by ADNP. This complex is prevalently bound at repeats, and in particular at LTR retrotranspoons. Recruitment of ADNP2 is mostly mediated by HP1b binding to H3K9 and a PxVxL mutant that cannot bind to HP1 does not localize properly to chromatin. While ADNP has its own specific targets in SINE elements, it also binds some ADNP2 targets in an HP1-dependent manner. Depletion of ADNP or ADNP2 results in upregulation of some shared and some distinct transposons, indicating distinct roles but also partial redundancy.

This is a solid study that adds to our knowledge of these repressive complexes and their transposable element targets. I feel that the data could be analyzed a bit more in depth, especially in the comparisons of ChIP-seq vs. RNA-seq.

Major points

• Fig. 5: it would be interesting to analyze differences between repeats that are only under ADNP2 control vs. those that are sensitive to additional loss of ADNP. Presumably they both have K9me3 so why some are also repressed by ADNP?
• Fig. S5B, S7A: degrons are known to destabilize some proteins even before induction of degradation. These western blots should include a WT line to compare abundance of the endogenous protein with the tagged version.
• FIg. 5: it would be good to show a bit more overlap between RNA-seq and ChIP-seq. How many of the bound transposons are derepressed? Can co-occupancy by ADNP and ADNP2 explain which transposons will display synergistic effets from removal of both proteins?

Minor points

• Fig. 2B: Upset plot seems like a strange choice for visualization. I would show as stacked bar plot compared to genome distribution. I.e. are peaks enriched on repeats or is it just that a larger genomic space is occupied by repeats compared to TSSs?
• Fig. 3A: if ADNP2 only binds to a subset of K9me+ retrotransposons, why arent' there regions of K9me+ ADNP2- in this plot?
• Check figure calls for 3B and 3C, some of them seem off.
• Fig. S7B: the text says several dozen genes but I only see 21 up and 15 down upon ADNP with ADNP2 present.

Significance

This is a solid study that adds to our knowledge of these repressive complexes and their transposable element targets. I feel that the data could be analyzed a bit more in depth, especially in the comparisons of ChIP-seq vs. RNA-seq.

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Referee #2

Evidence, reproducibility and clarity

In this work, Ahel, Pandey and Schwaiger et al. examine the function of ChAHP complexes in transposon silencing in mouse embryonic stem cells. This works builds on a proteomics approach previously developed in the Buhler lab, which identified ADNP1-ChAHP as a repressor complex of SINE retrotransposons. In their previous work they also identified the zinc-finger protein ADNP2 as an interactor of the ChAHP component CHD4. Here, the authors test the hypothesis of whether ADNP2 is part of an alternative ChAHP, which they termed ChAHP2. They first establish, through proteomics/biochemistry experiments, that the ChAHP2 complex can form independently of ChAHP. By ChIP-sequencing they then show that the ChAHP2 member ADNP2 predominantly occupies retrotransposons of the LTR families (e.g., ERV elements). They further show that recognition of target transposable elements (TEs) is conferred by the ChAHP2 complex member HP1 and its affinity for H3K9me3. Using RNA-seq they then addressed the repressive activities of ChAHP and ChAHP2 on TEs through degradation of ADNP, ADNP2 or both. The experimental approach is very well thought out and experiments are done with extensive controls.

I have the following comments/suggestions:

• Regarding the ChIP-seq experiments, it is not entirely clear from the manuscript text and also not from the Material and Methods whether ChIP-seq was done with a tagged-version of ADNP2, which is what I assume, or an endogenous ADNP2 antibody. Could you please state this clearly?
• The authors map short read sequencing data to individual TE insertions and conclude that ADNP2 binds retrotransposons both internally and at their terminal sequences. Particularly for the internal parts, how sure can the authors be that their approach, mapping to repeat consensus sequences, is not confounded by e.g., genetic differences between their ESC lines and the references they map to, or simply by the limitations of short read data?
• Page 7, the first sentence starting with "Contrary to the expected behavior of a TF, ...". Could the authors please elaborate on what they mean with "the expected behavior of a TF"?
• In Figure S4B, could the authors please clarify if HP1, CHD4 and Tubulin are high/low exposure?
• SETDB1 is the H3K9me3 methyltransferase responsible for LTR/ERV silencing in mESCs and its disruption leads to a pronounced upregulation of TEs (Karimi et al., 2011). Could the authors comment on the effect of their degron-mediated SETDB1 depletion on de-repression of LTR/ERV elements? At least for the elements shown to lose H3K9me3 upon SETDB1 depletion (Figure S5D - strong depletion replicate)? Could you please also provide information about morphological/pluripotency characteristics of the 2HA-FKBPSETDB1 ESC lines before and after the 48h treatment with 500nM dTAG13?
• Maybe I missed this, but are H3K9me3 levels affected in the ADNP and/or ADNP2 degron lines where transcriptional dysregulation of TEs is observed (Figure 5)? If not H3K9me3, is TE de-repression accompanied by reduction in repressive histone marks in ADNP2 degraded lines?
• When looking at TE de-repression, the upregulation seems very modest (Figure 5) and Log2FoldChanges >0.9 (FDR<0.05) were considered as statistically significant. Is this the result of using mESCs that "approximate a constitutive KO situation through inducible ADNP2 degradation" and 14 days of treatment with 250nM dTAG13? As mention above, could you please also provide information about morphological/pluripotency characteristics?

Significance

The findings are interesting and expand on our understanding of how complexes of chromatin bound proteins control epigenetic silencing of individual retrotransposon classes/families in mouse embryonic stem cells. More specifically, this study adds a new player, ChAHP2, a ChAHP alternative that associates with ERV and LINE1 retrotransposons via HP1-mediated binding of H3K9me3 and is required for transcriptional repression of LTR class retrotransposons. Although, in my opinion, it remains somewhat uncertain how depletion of ADNP2 results in TE upregulation.

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Referee #1

Evidence, reproducibility and clarity

The Buhler group previously identified the ChAHP complex and showed it to be made up of the transcription factor ADNP, chromatin remodeler CHD4, and HP1 proteins. They found that genetic removal of ADNP leads to increased expression of SINE B2 elements in mouse ES cells (mESCs), and an increase in chromatin accessibility and CTCF binding.

In the current manuscript they describe a related protein complex they name ChAHP2. ChAHP2 has a vertebrate paralogue of ADNP, a transcription factor they call ADNP2 and the same chromatin remodeler CHD4, and HP1 proteins. By investigating chromatin occupancy they find that ChAHP2 chromatin binding specificity is distinct from ChAHP, and predominantly associates with ERV and LINE1 retrotransposons via HP1beta-mediated binding of H3K9 trimethylated histones. The ChAHP and ChAHP2 complexes control a wide variety of molecularly disparate retrotransposons, including SINEs, LINEs, and ERVs.

The findings are of significance as the ChAHP2 complex is novel - it has not previously been identified or characterized and its description is therefore worthy of publication. Overall this study was well-performed and nicely-presented. In general, the text is clear, the flow of experiments seemed logical, easy to follow and supported by the presented evidence without the findings being overstated.

The data is mainly descriptive and it was at times hard to identify what were the clear conclusions from their study. Having identified the new ChAHP2 complex they show that its chromatin binding characteristics are distinct from ChAHP, which predominantly binds SINE elements. In contrast, ChAHP2 binds different classes of retrotransposons and recruitment to H3K9me3 heterochromatin is dependent on HP1-Beta. This was all relatively clear. It became a little more confusing trying to unravel the functional consequences of the loss of ChAHP2 - either alone, or in combination with ChAHP.

Although they see changes - both up- and down-regulation of a large number of genes, they say that: 'None of the changing gene categories showed strong and significant patterns either in terms of GO term enrichment (FigureS7C), distance between the promoter and the nearest ADNP/ADNP2 peaks'- does this mean that none of the upregulated genes following ADNP1/2 deletion show ADNP/ADNP2 peaks over the specific gene in question - i.e. do they think that the majority of effects here are indirect?

When it came to the 'repeat' families of genes - the situation was also not entirely clear.

They say: All these differentially expressed repeats belonged to the LTR class of retrotransposons, including families identified as ADNP2-bound in ChIP sequencing - it would be helpful to know which familes are bound and maybe show snapshots of ADNP2 binding. Are these differentially expressed repeats directly regulated by ADNP2? - they seem like a fairly heterogenous group of repeat elements? - do they have any shared features? They say that expression of two LINE1 subclasses were significantly upregulated - do these L1s (L1Mdas) have common features - are they old or young - it would be helpful if these different issues could be clarified.

In the discussion they are upfront about their inability to identify any specific sequence motifs required for ADNP2 occupancy. Since the repression is not obviously H3K9Me3 dependent, then what is the role of H3K9me3 in repressing here? They surmise that repression is likely to be regulated through chromatin remodeling by CHD4 - would ATAC-seq help clarify this suggestion? - particularly as they suggest that having CHD4 as an integral component of the repressor complex is a unique feature of ChAHP1/2?

In this context, do they not consider MORC2 to be an essential component of HUSH-dependent silencing?

Other points

The language in the introduction somewhat confusing and could be improved: They jumble ZNFs/TRIM28/HUSH/HP1 as if there is no specificity here - there clearly is - needs a more balanced and informative description.

What is firstly referring to? Firstly, histone deacetylation and the removal of activating histone methylations disfavor transcription13,14. Secondly, the underlying DNA is extensively methylated, further repressing the locus

They state: Like ERVs, LINE1 retrotransposons are autonomous- would help if they could clarify exactly what is meant here.

Significance

The findings are of significance as the ChAHP2 complex is novel - it has not previously been identified or characterized and its description is therefore worthy of publication. Overall this study was well-performed and nicely-presented. In general, the text is clear, the flow of experiments seemed logical, easy to follow and supported by the presented evidence without the findings being overstated.

The findings will be of broad interest to chromatin biologists - particularly those interested in the regulation of retroelements and repeat regions

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Reply to the reviewers

We would like to thank the reviewers for carefully reviewing our manuscript submitted to Review Commons. Their constructive comments have led us to identify key additional experiments to perform (testing endothelial cells, investigating the role of CXCR4/Sdf1 axis in the asymmetric division). They have shed light on specific points of the manuscript that had to be amended (see below).

First, we are pleased that the reviewers acknowledged the quality of the experiments performed (Reviewer #1: “In general, is a well-done work” ; Reviewer #2: “the evidence is convincing, experiments are rigorously performed with adequate replicates and reproducibility”), as well as interest and large scope our study (Reviewer #1: * “it gives a few more details describing that when HSPCs divide asymmetrically it seems there is an association between centrosome and lysosome distribution”, Reviewer #2: “These results collectively contribute to a deeper understanding of how the hematopoietic niche and interactions with neighboring cells influence HSPC behavior and their commitment to distinct cell fates during division”, “The findings have significance in understanding how the microenvironment influences HSPC behavior. This is broadly significant for stem cell biology”. Reviewer #3 “The manuscript is likely to have broader interest to not only HSPC researchers, but stem cell biologists and even engineers due to the technologies used”).*

Our detailed answers to the reviewers’ concerns are listed below.

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Reviewer #1 (Evidence, reproducibility and clarity):

In this manuscript, Candelas and colleagues investigated asymmetric cell division of human hematopoietic stem and progenitor cells (HSPCs) upon heterotypic interactions with osteoblasts. They developed a new in vitro system to test this and found that upon interaction, HSPCs polarized in interphase with centrosome and the Golgi apparatus and lysosomes positioned close to the site of contact. In addition, during mitosis, HSPCs were found to orient their spindle perpendicular to the plane of contact. This division gave rise to siblings with unequal amounts of lysosomes and CD34. In general, is a well-done work and it gives a few more details describing that when HSPCs divide asymmetrically it seems there is an association between centrosome and lysosome distribution.

Authors: We thank the reviewer for this positive assessment of our work.

Reviewer #1 (Significance (Required)):

However, all of these features (described above) have already been independently described even in human HSPCs thus this work does not represent a major advancement in this field (e.g. on the potential molecular mechanism by which heterotypic interactions with osteoblasts promote such behaviours). Overall, this stage is descriptive in nature.

Authors: We respectfully disagree with the reviewer on this point. The main finding of our work does not simply concern the ability of HSPCs to undergo asymmetric division. This ability has indeed been previously shown in mouse and human models, and we refer to the princeps works in our introduction (page 2 “In vitro HSPCs can undergo asymmetric divisions 11 12 13 14 15 16 17 ”). Our main finding is about the instrumental role of heterotypic interactions with stromal cells of the niches. This had not been shown previously, mostly due to the limitations of classical co-culture systems and of in vivo tracking of HSPCs. We have engineered artificial niches in microwells specifically to overcome these limitations. We are confident that this finding is of interest for of hematopoietic niches biology and more globally for the field of stem cell biology. In that sense, the corresponding biorXiv preprint has just been quoted by the seminal review by Hans Clevers “Hallmarks of stemness in mammalian tissues” (doi: 10.1016/j.stem.2023.12.006).

One major caveat of this work is that CD34+ HSPCs represent a very heterogeneous population. Although the underlying features described in this work could be similar between different cell populations, the frequency of these events (e.g. % magnupodium; polarization index, % of asymmetric inheritance, etc) is likely to be different between stem and progenitor cells. This may also explain the wide spread of their data points. Experiments should also be conducted with different cell populations, in particular with HSCs (either with the CD34+CD38-CD45RA-CD90+ or CD34+CD38-CD45RA-CD90+CD49f+ HSC enriched fraction or the highly CD34+CD38-CD45RA-EPCR+ HSCs).

Authors: We agree that we are dealing with an heterogenous population of stem and progenitor cells; we cannot exclude that more pronounced effects could be obtained by analyzing separately stem cells, lymphoid and myeloid progenitors. The use of CD34+ heterogenous population has been a strategical choice. We are working with human primary cells, harvested from cord blood, a rare and precious material, who’s access has been in addition reduced during the COVID period and since. Working with the global CD34+ population was giving us the ability to work with a higher number of cells and avoid material limitations to perform experiments. Importantly, in our initial publication (Bessey et al doi:10.1083/jcb.202005085), we both used CD34+, or CD34+/CD38- versus CD38+/CD34+ subpopulations (see figure 4): the effects we described using global CD34+ population were significant, validating a posteriori this choice. Similarly, the effects observed in the present work with CD34+ population have always been validated by appropriate statistic tests. So, we are confident that the use of the CD34+ population, despite its heterogeneity, did not alleviate the validity and pertinence of our analyzes and conclusions.

Results shown in Figure 2 were obtained with a very limited number of cells; also data obtained for Figure 4; this should be substantiated;

Authors: We acknowledge that the analyses performed on fixed mitotic cells are based on relatively small samples. We have decided to fix and analyze the cells at 40h of culture which corresponds to the peak of mitosis, instead of synchronizing HSPCs in mitosis with available drugs, in order to avoid potential perturbations of these drugs. The consequence was the scarcity of the mitotic HSPCs in each experiment. This limitation has also been encountered by other laboratories working on HSPCs : our samples sizes are in fact within the range of the samples analyzed in other works (see Hinge et al., 2020, doi:10.1016/j.stem.2020.01.016: around 20 cells; Florian, et al., 2018: doi: 10.1371/journal.pbio.2003389. from 8 to 40 cells). However, in order to improve this limitation, few additional experiments and analyses have been performed to increase the number of mitotic cells (Figure 3: from 27 to 38 cells).

In addition, data from Figure 2 adds little and should be combined with Figures 3 and 4 to make a single stronger message.

Authors : We agree on this comment: Figures 2 and 3 have now been merged

It is/was unclear why the authors investigated the distribution of CD34 and CD33 and the major and important question remained to be answered: whether the symmetric cell divisions were/are differentiating or self-renewal in nature hence, the asymmetric cell divisions promoted by the osteoblasts may represent asymmetric self-renewal ones; this needs to be investigated further and potential molecular mechanisms for such promotion should be highlighted.

Authors: CD34 and CD33 were chosen as our “gold standards” according to the princeps work of Loeffler et al (Loeffler et al., 2019, and 2022). Our selection is based on the need for markers that encompass this diverse population. We focused on CD34 and CD33 as they are among the most prevalent CD markers on HSPCs, particularly when working with the CD34+ population, which is broad and necessitates widely expressed CD markers. Importantly, previous works have reported that CD34 anti-correlates with lysosome asymmetric inheritance after the first division, whereas CD33 does not (see Fig3E, Loeffler et al., 2022). So using these markers we can compare two markers: one that follows lysosome inheritance after the first division, and one which doesn’t. We found that osteoblasts inducing asymmetric lysosome inheritance in HSPC do increase asymmetric production of CD34 but not CD33, in concordance with the literature. This has been now explained in more detail in the text.

In addition, higher lysosome inheritance has been previously demonstrated to be associated with the most stem cell (Loeffler et al., 2019), implying a more stem-like profile for the proximal cell during division in our work. However, recent studies using single-cell sequencing approaches challenge the notion of discrete differentiation within this stem cell model (reviewed by Zhang et al., 2018; Laurenti and Gottgens, 2018; Cheng et al., 2020; Liggett and Sankaran, 2020). Our study contributes to this discussion by providing insights into the relationship between CD markers, lysosome inheritance, and the stem cell profile during asymmetric division, and presenting this heterogeneity observed in single-cell sequencing works.

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

The paper titled "Heterotypic Interaction Promotes Asymmetric Division of Human Hematopoietic Stem and Progenitor Cells" presents research on how interactions between Hematopoietic Stem and Progenitor Cells (HSPCs) and osteoblasts impact cell division symmetry. The use of polyacrylamide microwells to simulate the hematopoietic niche and study osteoblast interactions is a novel and valuable approach. The paper effectively explains the experimental design, making it easy for others to replicate and verify the results. The paper provides detailed insights into how interactions with osteoblasts influence HSPCs, particularly in terms of cell polarization, spindle orientation, and organelle distribution during cell division. The evidence is convincing, experiments are rigorously performed with adequate replicates and reproducibility.

Authors: We thank the reviewer for this positive evaluation of our work.

• The study acknowledges that not all HSPCs respond to heterotypic interaction, suggesting that individual variability in HSPC behavior plays a role. Future research could explore the factors that determine which HSPCs undergo asymmetric divisions. This raises questions about the heterogeneity in HSPC responses. The researcher starts culturing CD34+ which is a heterogeneous group with osteoblast. This heterogeneity by default will give different cells progeny which mimics the in vivo BM status. But, to minimize the invitro experiment variables examining a more pure HSC population such as isolated CD34+CD38-CD90+ cells would strengthen the findings?

Authors: We agree that we are dealing with an heterogenous population of stem and progenitor cells; we cannot exclude that more pronounced effects could be obtained by analyzing separately stem cells, lymphoid and myeloid progenitors. The use of CD34+ heterogenous population has been a strategical choice. We are working with human primary cells, harvested from cord blood, a rare and precious material, who’s access has been in addition reduced during the COVID period and since. Working with the global CD34+ population gave us the ability to work with a higher number of cells and avoid material limitations to perform experiments. Importantly, in our initial publication by Bessy et al (doi:10.1083/jcb.202005085), we used both CD34+, or in some cases CD34+/CD38- versus CD38+/CD34+ subpopulations (see figure 4), to investigate HSPC mode of polarization. The effects observed in the case of total CD34+ were significant, validating a posteriori this choice. Similarly, the effects observed in the present work with CD34+ population have always been validated by appropriate statistic tests. Our study indicates that the mechanism we described is conserved throughout the entire HSPC population.

In conclusion, we are confident that the use of the CD34+ population, despite its heterogeneity, did not alleviate the validity and pertinence of our analyzes and conclusions.

What was the Osteoblast/HSCs ratio used in the experimental setup? Does this ratio affect the results?

Authors: The loading of HSPC has been optimized to get one HPSC per microwell, as indicated in the result section (page 3 line 3). This has now been clarified in the material and methods section. However, we observe some wells with more than one HSPC on the stromal cell, but we did not notice any clear impact on cell division asymmetry and did not investigate further this parameter.

• The paper primarily focuses on lysosome inheritance and CD34 expression, leaving room to explore other lineage-specific markers and their correlation with asymmetric division. Do osteoblast/ HSCPs interactions have also an effect on mitochondrial inheritance?

Authors: We fully agree that other markers could have been analyzed to comfort our observations.

A far as mitochondria are concerned, recent publications suggest that lysosomes can be considered as a “inversed” readout of mitochondria inheritance: (1) mitophagy has been shown to take place in quiescent hematopoietic stem cells (Ito et al., 2016), suggesting that lysosomes do participate in the regulation mitochondria levels in HSPCs. (2) Loeffler et al. (2019) has shown an opposite pattern between mitochondria and lysosomes, lysosomes co-inheriting with mitophagosomes. Considering that this mutual or opposite inheritances were already described, we did not investigate them further. However we agree that it could be the focus for future works.

• While the study hints at the clinical implications of its findings, it does not show the practical applications in detail. How the knowledge gained from these interactions could be translated into clinical practices or therapies is not explicitly discussed. Bridging this gap is necessary for understanding the practical utility of these results.

Authors: we are confident that microwell technology could find, in the long term, more medical applications. However, we did not wish to speculate on this point in the present manuscript. The words “clinical” and “therapy” show no occurrence in our text. The potential implications of our findings in the field of leukemia are now mentioned in the discussion section with the corresponding references (page 6 line 10) “Such spatial control of the division is a conserved feature of asymmetric divisions in other stem cell niches 6. It may account for in vivo observations of organization into clusters of blood cell differentiation 44, and may play an important role in competition mechanisms at play within the hematopoietic niches in physiological 45 and pathological 46 contexts.”

__Reviewer #2 (Significance (Required)): __

• Investigating the process of HSPC asymmetric division is highly important to understand HSPC fate decisions and functions. The findings have significance in understanding how the microenvironment influences HSPC behavior. This is broadly significant for stem cell biology.
• The paper's observation of uneven lysosome distribution and its potential impact on differentiation markers, including CD34 and CD33, contribute to our understanding of HSPC division and lineage determination.
• Upon interaction with osteoblasts, HSPCs polarize during interphase, with centrosomes, the Golgi apparatus, and lysosomes positioned close to the site of contact. This reorganization of intracellular architecture plays a significant role in asymmetric division.
• These results collectively contribute to a deeper understanding of how the hematopoietic niche and interactions with neighboring cells influence HSPC behavior and their commitment to distinct cell fates during division.

Authors: We thank the reviewer for this quite positive evaluation of our work.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary: In this study, the authors systematically work to identify the contribution of hematopoietic niche stromal cells in the control of HSPC asymmetric divisions. Using live cell imaging techniques, the authors show that heterotypic interaction with osteoblasts promotes asymmetric division of human HSPCs. The authors find that HSPCs polarize in interphase with centrosome, the Golgi apparatus and lysosomes positioned close to the site of contact. Moreover, during mitosis, HSPCs orient their spindle perpendicular to the plane of osteoblast contact and the subsequent division gives rise to siblings with unequal amounts of lysosomes and differentiation markers such as CD34. Taken together, the authors suggest that this asymmetric inheritance generates heterogeneity in progeny, which is likely to contribute to plasticity during the early steps of hematopoiesis.

Major Comments:

1. The study that uses polyacrylamide microwells as minimalist niches to evaluate the role of heterotypic interactions in the asymmetric division of HSPCs. Using this model system, the data clearly indicate that osteoblasts promote HSPC polarization when compared to fibronectin or skin fibroblasts. However, osteoblasts weren't compared to other HSPC stromal niche components. For example, is the same polarization observed with endothelial cells? This would help to determine whether this observation is specific to only osteoblasts in the niche or if there's a broader role for heterotypic interactions, which is the claim made in the discussion.

Authors: We have now performed additional experiments using endothelial cells (see Figure 1 and 2, Page 3 and 4) and found that endothelial cells do also promote asymmetric division.

This is primarily a descriptive study that doesn't attempt to address or even postulate the type of receptors potentially responsible for the polarization-driving heterotypic interactions. Perhaps inhibitors to candidate receptors could be incorporated or at least candidate receptors could be mentioned and described in the discussion as future directions.

Authors: We have now performed additional experiments to address this point: We have analyzed the effect of the CXCR4 antagonist AMD3100 on HSPC division upon interaction with osteoblast and found that blocking these receptors reduce the asymmetry of daughter cells to the level of isolated HSPC (see Figure 3 E -G; Figure S3 H-J; page 4).

__Minor Comments: __

1. There is no reference to Figures 2C and D in the text. Authors : This oversight has been corrected.

Page 3: “HSPC cultured on fibronectin exhibited spindle oriented parallel to the well bottom, (Figure 2A-C and S3C and D)”.

Page 4: In contrast, both equal and unequal LysoBriteTM segregations could be observed (Figure 2D and S3E).

The different circle colors in Figure 4C and D are a bit difficult to distinguish.

Authors: The figure has been modified accordingly

It's difficult to identify where the sites of cell contact are in Figure 2. Perhaps contact sites could be indicated in the images.

Authors: The sites of contact have now been systematically indicated using dashed lines, in Figure 2 and 3.

It's not clear how spindle orientation is being identified in Figure 3.

Authors: We are aware of the fact that spindle orientation is not easy to visualize in the still images presented in Figure 3A and B. These images are extracted from the movies that were used to determine the cell division plane visually. This plane, following the long-axis rule, is perpendicular to the spindle orientation, which could therefore be determined. Movies 6 and 7 are shown to support these observations and illustrate how amenable these movies are to support spindle orientation analysis.

Some grammatical errors need to be addressed throughout the manuscript.

Authors: We thank the reviewer for drawing our attention on this point: the modified text has been carefully examined, and hopefully improved.

Reviewer #3 (Significance):

Significance: Overall, this is straightforward study that presents data illustrating the polarization driving capacity of osteoblast interactions with HPSC. The findings are important to the field, as little is known about asymmetric vs symmetric division in HSPCs. However, in its current form, the manuscript lacks clarity with respect to whether specifically osteoblasts promote HSPC polarization, or any stromal niche player has this capacity. Moreover, there is a lack of mechanistic data and/or discussion about how osteoblasts may be driving the observed polarization.

Authors: We have now added data showing the similar role of endothelial cells and the implication of CXCR4 receptors.

The manuscript is likely to have broader interest to not only HSPC researchers, but stem cell biologists and even engineers due to the technologies used.

Authors: We thank the reviewer for his/her enthusiasm for our work

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Referee #3

Evidence, reproducibility and clarity

Title: Heterotypic interaction promotes asymmetric division of human hematopoietic stem and progenitor cells

Authors: Adrian Candelas, Benoit Vianay, Matthieu Gelin, Lionel Faivre, Jerome Larghero, Laurent Blanchoin, Manuel Théry, Stephane Brunet

Summary: In this study, the authors systematically work to identify the contribution of hematopoietic niche stromal cells in the control of HSPC asymmetric divisions. Using live cell imaging techniques, the authors show that heterotypic interaction with osteoblasts promotes asymmetric division of human HSPCs. The authors find that HSPCs polarize in interphase with centrosome, the Golgi apparatus and lysosomes positioned close to the site of contact. Moreover, during mitosis, HSPCs orient their spindle perpendicular to the plane of osteoblast contact and the subsequent division gives rise to siblings with unequal amounts of lysosomes and differentiation markers such as CD34. Taken together, the authors suggest that this asymmetric inheritance generates heterogeneity in progeny, which is likely to contribute to plasticity during the early steps of hematopoiesis.

Major Comments:

1. The study that uses polyacrylamide microwells as minimalist niches to evaluate the role of heterotypic interactions in the asymmetric division of HSPCs. Using this model system, the data clearly indicate that osteoblasts promote HSPC polarization when compared to fibronectin or skin fibroblasts. However, osteoblasts weren't compared to other HSPC stromal niche components. For example, is the same polarization observed with endothelial cells? This would help to determine whether this observation is specific to only osteoblasts in the niche or if there's a broader role for heterotypic interactions, which is the claim made in the discussion.
2. This is primarily a descriptive study that doesn't attempt to address or even postulate the type of receptors potentially responsible for the polarization-driving heterotypic interactions. Perhaps inhibitors to candidate receptors could be incorporated or at least candidate receptors could be mentioned and described in the discussion as future directions.

Minor Comments:

1. There is no reference to Figures 2C and D in the text.
2. The different circle colors in Figure 4C and D are a bit difficult to distinguish.
3. It's difficult to identify where the sites of cell contact are in Figure 2. Perhaps contact sites could be indicated in the images.
4. It's not clear how spindle orientation is being identified in Figure 3.
5. Some grammatical errors need to be addressed throughout the manuscript.

Significance

Overall, this is straightforward study that presents data illustrating the polarization driving capacity of osteoblast interactions with HPSC. The findings are important to the field, as little is known about asymmetric vs symmetric division in HSPCs. However, in its current form, the manuscript lacks clarity with respect to whether specifically osteoblasts promote HSPC polarization, or any stromal niche player has this capacity. Moreover, there is a lack of mechanistic data and/or discussion about how osteoblasts may be driving the observed polarization.

The manuscript is likely to have broader interest to not only HSPC researchers, but stem cell biologists and even engineers due to the technologies used.

I have experience with questions of HSPC regulation.

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Referee #2

Evidence, reproducibility and clarity

The paper titled "Heterotypic Interaction Promotes Asymmetric Division of Human Hematopoietic Stem and Progenitor Cells" presents research on how interactions between Hematopoietic Stem and Progenitor Cells (HSPCs) and osteoblasts impact cell division symmetry. The use of polyacrylamide microwells to simulate the hematopoietic niche and study osteoblast interactions is a novel and valuable approach. The paper effectively explains the experimental design, making it easy for others to replicate and verify the results. The paper provides detailed insights into how interactions with osteoblasts influence HSPCs, particularly in terms of cell polarization, spindle orientation, and organelle distribution during cell division. The evidence is convincing, experiments are rigorously performed with adequate replicates and reproducibility.

• The study acknowledges that not all HSPCs respond to heterotypic interaction, suggesting that individual variability in HSPC behavior plays a role. Future research could explore the factors that determine which HSPCs undergo asymmetric divisions. This raises questions about the heterogeneity in HSPC responses. The researcher starts culturing CD34+ which is a heterogeneous group with osteoblast. This heterogeneity by default will give different cells progeny which mimics the in vivo BM status. But, to minimize the invitro experiment variables examining a more pure HSC population such as isolated CD34+CD38-CD90+ cells would strengthen the findings? What was the Osteoblast/HSCs ratio used in the experimental setup ? Does this ratio affect the results?
• The paper primarily focuses on lysosome inheritance and CD34 expression, leaving room to explore other lineage-specific markers and their correlation with asymmetric division. Do osteoblast/ HSCPs interactions have also an effect on mitochondrial inheritance ?
• While the study hints at the clinical implications of its findings, it does not show the practical applications in detail. How the knowledge gained from these interactions could be translated into clinical practices or therapies is not explicitly discusssed. Bridging this gap is necessary for understanding the practical utility of these results.

Significance

• Investigating the process of HSPC asymmetric division is highly important to understand HSPC fate decisions and functions. The findings have significance in understanding how the microenvironment influences HSPC behavior. This is broadly significant for stem cell biology.
• The paper's observation of uneven lysosome distribution and its potential impact on differentiation markers, including CD34 and CD33, contribute to our understanding of HSPC division and lineage determination.
• Upon interaction with osteoblasts, HSPCs polarize during interphase, with centrosomes, the Golgi apparatus, and lysosomes positioned close to the site of contact. This reorganization of intracellular architecture plays a significant role in asymmetric division.
• These results collectively contribute to a deeper understanding of how the hematopoietic niche and interactions with neighboring cells influence HSPC behavior and their commitment to distinct cell fates during division.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Candeleas and colleagues investigated asymmetric cell division of human hematopoietic stem and progenitor cells (HSPCs) upon heterotypic interactions with osteoblasts. They developed a new in vitro system to test this and found that upon interaction, HSPCs polarized in interphase with centrosome and the Golgi apparatus and lysosomes positioned close to the site of contact. In addition during mitosis, HSPCs were found to orient their spindle perpendicular to the plane of contact. This division gave rise to siblings with unequal amounts of lysosomes and CD34. In general, is a well-done work and it gives a few more details describing that when HSPCs divide asymmetrically it seems there is an association between centrosome and lysosome distribution.

Significance

However, all of these features (described above) have already been independently described even in human HSPCs thus this work does not represent a major advancement in this field (e.g. on the potential molecular mechanism by which heterotypic interactions with osteoblasts promote such behaviours). Overall, this stage is descriptive in nature.

One major caveat of this work is that CD34+ HSPCs represent a very heterogeneous population. Although the underlying features described in this work could be similar between different cell populations, the frequency of these events (e.g. % magnupodium; polarization index, % of asymmetric inheritance, etc) is likely to be different between stem and progenitor cells. This may also explain the wide spread of their data points. Experiments should also be conducted with different cell populations, in particular with HSCs (either with the CD34+CD38-CD45RA-CD90+ or CD34+CD38-CD45RA-CD90+CD49f+ HSC enriched fraction or the highly CD34+CD38-CD45RA-EPCR+ HSCs).

Results shown in Figure 2 were obtained with a very limited number of cells; also data obtained for Figure 4; this should be substantiated; in addition, data from Figure 2 adds little and should be combined with Figures 3 and 4 to make a single stronger message.

It is/was unclear why the authors investigated the distribution of CD34 and CD33 and the major and important question remained to be answered: whether the symmetric cell divisions were/are differentiating or self-renewal in nature hence, the asymmetric cell divisions promoted by the osteoblasts may represent asymmetric self-renewal ones; this needs to be investigated further and potential molecular mechanisms for such promotion should be highlighted.

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Reply to the reviewers

Reviewer #1

• Albeit the link between CSA and NE integrity the work is in my eyes too preliminary. Although the data presented are well done and carefully evaluated they mostly (except Fig 1A) rely on direct comparisons of one patient cell line (CS-A or CS-B) to the same cells expression the wildtype protein. It remains thus open whether the effects seen on LEM2 expression, LEM2-LaimA/C interaction, stress fibre formation, cGAS/STING signaling pathway activation in the CS-A cells are representative for a number of different CS patient derived cells. This is especially important given the small changes observed. Please note that there are alos clear differences between the CSA-wt and CSB-wt cells. Would the HPA CSA KO cells show in addition to NE irregularities (not even quantified) the same phenotypes and can they be reverted by re-expression of the wildtype CSA protein? We would like to thank the reviewer for this comment. Indeed we have previously observed nuclear circularity defects in CSA KO HAP1 cells but we haven’t investigated the other phenotypes in this cell line. One of the main reasons behind this is the technical difficulties associated with performing immunofluorescence with HAP1 cells who are very small and tend to grow in aggregates.

Proposed experimental plan: To address this reviewer’s comment, we will attempt again to use HAP1 cells (WT and CSA KO) and look at nuclear circularity (with quantification), stress fiber formation and cGas foci. If we don’t succeed, we will use an alternative isogenic cell model consisting of fibroblasts in which we will knock out CSA using CRISPR/Cas9. We will then repeat the same experiments as proposed above for the HAP1 cells.

• The link between CSA and SUN1 is not well worked out. What is the effect of SUN2 downregulation and that of nespirins? It remains unclear whether the observed effects are indeed LINC mediated. Proposed experimental plan: To address this point, we will downregulate SUN2 and nesprins using siRNAs in two different cell models (as described above) and assess nuclear shape as well as cGas/STING pathway activation.

Minor comments:

* Fig 1B: Why is HA-Tagged CSA not shown on the CSA western? This would be helpful to compare to the endogenous levels at least in CSB cells. A western showing an housekeeping marker would allow better comparison. Judging from the proteins markers HA-tagged CSA seems much larger as endogenous CSA (first versus second row). Again, less cropped western blots would help.*

We are sorry for the confusion and we have realised that the molecular weights on the western blots were incorrectly labeled on this figure. This will be modified, and the full, uncropped WB will be provided as a supplementary file.

Fig 3A: Is CSA FLAG or HA-tagged? Or both? If both are expressed the question raises of why the CSA-LEM 2 interaction is only seen in an overexpression situation.

• *

CSA is HA tagged. To address this reviewer’s comment we will try performing immunoprecipitation on endogenous proteins.

Fig 5: Inconsistency between figure and figure legend: 20 vs 25 nM Jasplakinolide. I assume Latrunculin A should read Cytochalasin D?

Thank you for pointing this out, and yes this is indeed a mistake on our labeling. We will rectify this on the figure legend.

Fig5B: Not clear why in "CSA-wT cells" Cytochalasin D and Jasplakinolide have the same effect on nuclear envelope shape yet only Jasplakinolide increases the number of blebs.

Cyt D inhibits actin polymerization while jasplakinolide increases polymerization. Likely actin polymerization increases blebs through extra force being put on the nucleus through actin cables/ actin based motility. Both drugs decrease nuclear roundness as they disrupt the normal actin network leading to worsening of nuclear shape through different mechanisms.

Page 10: Method for IF: 4% (v/v) paraformaldehyde and 2% /v/v) should likely read (w/v). Page 19: replace "withl" by "with".

We will rectify both these points.

Reviewer #2

The paper is well-written and for the most part, the data support the conclusions of the authors. Some minor caveats could be addressed to improve the quality of the manuscript.

We would like to thank the reviewer for their positive feedback on our manuscript.

• The phenotype of decreased LEMD2 incorporation into the NE in CS-A cells is minor. Only ~20% and thus, it is not clear whether this is causal of any of the NE abnormalities. It should be better explained how these data add to the story.

To address this point, we will overexpress LEMD2 in CS-A cells and assess whether the NE phenotype can be significantly rescued. This will add value to this part of story.

• Inducing actin polymerization and depolarization impact nuclear morphological abnormalities and nuclear blebbing. Do these treatments impact nuclear fragility and cGAS accumulation at NE break sites?* This is a good point indeed. To address this question, we will include cGas foci staining and quantification upon treatment with these chemicals.

• Depletion of SUN1 in CS-A cells increased nuclear circularity, decreased blebbing, and phosphorylation of TBK1. The impact of SUN1 depletion in cGAS foci formation at NE break sites and phosphorylation of STING is not shown. Such experiments will provide stronger evidence that CS-A activates the cGAS-STING pathway in a SUN1 (mechanical stress)-dependent manner.

* We will address this question by analysing cGas foci and cGas-STING pathway activation upon SUN1 depletion by siRNA.

Reviewer #3

• *

The data are generally clear, well performed and well interpreted with some exceptions:*

1) I appreciate the use of isogenic cell lines (a big plus when dealing with patient-derived cell lines). However, these lines were established 30 years ago and the reported phenotypes might be due to genetic drifts. To exclude this, I suggest to complement the HAP-1 ERCC8 KO cell line with exogenously expressed CSA and assess if this rescues the phenotypes reported. Validation of the KO in these lines, either by western blotting or sequencing is needed.*

This point has also been raised by the first reviewer, and will be addressed as described above (and pasted below):

We would like to thank the reviewer for this comment. Indeed we have previously observed nuclear circularity defects in CSA KO HAP1 cells but we haven’t investigated the other phenotypes in this cell line. One of the main reasons behind this is the technical difficulties associated with performing immunofluorescence with HAP1 cells who are very small and tend to grow in aggregates.

Proposed experimental plan: To address this reviewer’s comment, we will attempt again to use HAP1 cells (WT and CSA KO) and look at nuclear circularity (with quantification), stress fiber formation and cGas foci. If we don’t succeed, we will use an alternative isogenic cell model consisting of fibroblasts in which we will knock out CSA using CRISPR/Cas9. We will then repeat the same experiments as proposed above for the HAP1 cells.

2) Related to the complementation of patient cell lines, the exogenous HA-CSA is not recognised by the anti-CSA in the CSA-null patient cell lines (Fig 1B, second blot). Shouldn't you be able to see this exogenous protein? HA-GFP-CSB in the complemented CSB-null patient cell line runs at the same weight as endogenous CSB (Fig 1B, fourth blot). This is also unexpected. I think you need better characterisation of your cell lines and need to demonstrate the level of exogenous transgenes that have been used to complement the cells and that they localise appropriately, presumably to the nucleus. You should also make sure to cite the paper where they were isolated and describe that they were immortalised (Troelstra et al., 1992) and the paper in which transgenes were stably overexpressed (Qiang et al., 2021).*

*

As mentioned above, we have realised that we made some mistakes with the labeling of the molecular weight on this western blot. This will be corrected and the full uncropped western blot will be provided as a supplementary figure.

We will also cite the suggested papers accordingly.

3) Immunolocalisation of INM proteins is notoriously tricky and the permeabilisation steps include only 0.2% Tx100, which can be insufficient to permeabilise the INM. I appreciate the Emerin and Lamin immunostaining seems to have worked, but in many cases successful immunostaining can be antibody-specific. Can you try harsher permeabilisation to expose LEM2 epitopes? I'm somewhat uncomfortable with the suggestion that there is a cytosolic (ER?) pool of endogenous LEM2 as this runs counter to the literature and feel that your antibody or fixation conditions are illuminating a non-specific protein. The WB in Fig 2E shows that there is virtually no LEM2 in the "soluble" fraction. I would be more cautious on this cytoplasmic/nuclear pool interpretation. Biochemical nuclear and cytoplasmic fractionation would help clarify the signal in a NE vs a non-NE pool.*

*

As suggested by the reviewer, we will try harsher permeabilisation conditions to test the LEMD2 antibody. As we suggest in the manuscript however, we think that the “cytoplasmic” LEMD2 pool we observed by IF in the absence of pre-extraction is indeed unspecific. This is why we have performed the rest of the experiments with a pre-extraction step, that we have shown to give a specific LEMD2 signal that disappear upon depleting LEMD2 by siRNA.

4) Page 15: "Using a Proximity Ligation Assay (PLA), we showed a significant reduction in the number of PLA foci in CS-A cells compared to the WT(HA-CSA) cells, reflecting a reduced number of LEMD2-lamin A/C complexes (Figure 2G, 2H). This data suggests defects in the incorporation of LEMD2 into the NE and lamin protein complexes in CS-A cells". If you have less LEM2 in the NE, it is quite expected that you will have less "LEM2-laminA/C" complexes. To me the logic doesn't hold and this data does not suggest that there is an underlying defect in LEM2-lamin interaction. To ascertain whether there is such a defect one could perform an IP against LEM2 and quantify laminA/C, normalizing by the amount of LEM2 in the input.

We feel we may not have been clear in how we interpreted this data. What we mean is that in each individual cell, the number of Lamin-LEMD2 complexes is decreased, probably indeed due to the fact that there is less LEMD2 altogether within the nucleus in the absence of CSA. We will clarify this in the text.

5) "We overexpressed LEMD2-GFP and Flag-CSA constructs, followed by GFP pulldown in WT(HA-CSA) cells". Since the co-IP data are obtained in overexpression conditions (of both HA-CSA and Flag-CSA?), the authors should validate the interaction between LEM2 and CSA using an orthogonal approach. Perhaps anti-HA capture of the WT(HA-CSA) cells would allow you to immunoblot for endogenous LEM2?*

*

To address this point, we will try to immunoprecipitate HA-CSA and look at endogenous LEMD2.

6) Related to the CSA-LEM2 binding in the above experiment, the procedure involves combining a native detergent-extracted cytoplasmic pool with a denatured (RIPA-extracted) nuclear pool for performing the GFP-trap. From which pool was the tagged CSA bound to LEM2 in?*

*

We are sorry about the confusion. We didn’t try to run the IP from the different pools but instead from the combined pools, to ensure we were looking in the whole cell extract. We would expect however that the interaction occurs in the nuclear pool as both CSA and LEMD2 are nuclear proteins.

7) "The absence of CSA in CS-A patient cells does not affect the mobility of LEMD2 at the NE but instead decreases its interaction with A-type lamins". To me the fact that loss of CSA decreases LEM2-lamin interaction is not well supported (see point 3).

• *

See our response to point 4

8) "Here, we showed by immunoprecipitation that LEMD2 also interacts with CSA. This suggests that the recruitment and stabilization of LEMD2 to the NE is mediated by an interaction with CSA, although the mechanism remains unclear". I think this is an overstatement: there are no data suggesting that CSA recruits or stabilises LEM2 at the NE.

* *We will tone down this statement in the text

9) As the authors suggest in the discussion, it would be worth checking whether LEM2 overexpression is able to rescue some of the NE defects reported, strengthening the hypothesis that LEM2 levels are at least in part responsible for the phenotypes reported.

To address this point, we will perform LEMD2 overexpression in the CSA cells, and analyse the nuclear envelope defects and ruptures (shape and cGas foci quantification)

10) To me it is not clear how the reported phenotypes are interrelated. The first part of the manuscript shows that CSA interacts with LEM2, and that loss-of-function CSA impacts on LEM2 levels and LEM2-lamin interaction, suggesting a direct role for CSA at the nuclear envelope. The second part of the manuscript shows that cells with defective CSA have more actin stress fibres and releasing the cytoskeleton-nuclear tethering is able per se to rescue the nuclear membrane and cGAS phenotypes. How do the authors reconciliate these two parts? Is CSA directly involved in both inner nuclear membrane homeostasis and actin cytoskeleton modulation or is this latter role upstream and the NE defects a mere consequence of increased cytoskeleton rigidity?

At this point indeed we cannot draw definitive conclusions as to whether the two described phenotypes are inter-related. However, by addressing the other points raised by the reviewers, we hope this will help clarifying the mechanism.

11) It is not clear how or why actin stress fibres are elevated in the CS-A cells. Can the authors provide any insight based on their RNAseq analysis? Demonstrating a link to ROCK, LIMK or Rho signalling would be interesting and verifying ppMLC2 levels would help explain why contractility is enhanced. Additionally, is the increase in contractility dependent upon any of the genes identified as up- or downregulated in RNAseq? Presently, the manuscript is missing a link between its two halves.*

*

We would like to reiterate that the RNASeq analysis we performed was done on previously published data from another group (as described in the text). To address the point raised by the reviewer, we will look more specifically into our analysis to look at ROCK, LIMK or Rho signalling to see if any of these pathways appear to be modulated by the absence of CSA.

12) Related to point 1, the RNAseq comparison was performed on patient cells lacking CS-A and patient cells lacking CS-A and later over-expressing HA-CSA, and this comparison is used extensively for phenotype description in the manuscript. In isn't clear to me that this is the most insightful comparison to make; the rescue by overexpression is not as elegant as CRISPR reversion and the ko fibroblasts have presumably been surviving well in culture without CS-A before this protein was overexpressed. Can you validate the differential expression of any identified proteins in the acute HAP1 ko? Can you validate any of the differentially expressed proteins in comparison to normal fibroblasts (e.g., 13O6, as per Qiang et al., 2021)?

As we will validate our experiments in an additional cell model (as described above), we will also indeed validate the level of expression of cytoskeletal proteins upon CSA KO/rescue.

Minor comments

* - Page 14: "To characterize the NE phenotypes further, we obtained CS patient-derived cell lines carrying loss-of-function mutations in CSA (CS-A cells) or CSB (CS-B cells), and their respective isogenic control cell lines (WT(HACSA) and WT(HA-GFP-CSB))." What type of loss-of-function? Is the mutant protein still produced? In Fig 6A there seem to be a band in the CS-A blot (second lane), but in Fig 1B, there isn't. I think this is important to know to interpret the phenotype related to LEM2 interaction.*

We can clarify that in the text. Indeed, the loss of function mutation leads to the absence of CSA protein.

- Figure 1B is poorly annotated. What do - and + stand for? In general, I find a bit confusing how the WB are presented throughout the manuscript, specifically how the antibodies are reported (e.g., HA-CSA instead of HA). Please mark up all western blots with antisera used. Please make sure all expected bands are within the crops - e.g., Fig 3B, the anti-LEM2 blot should be expanded vertically to show the LEM2-GFP relative to endogenous LEM2.

We will correct these on the figures

- From the methods, it appears that you obtained a Please provide clarity on which construct was used in which figure, and verify that an N-terminally tagged LEM2 still localises to the NE.

We actually cloned LEMD2 into an empty pEGFP vector but still maintained LEM2-GFP. We will remove the C1plasmid from the methods to avoid confusion as we removed the MCS and GFP and just used the blank vector and inserted lem2-gfp as we obtained it.

- Fig 1I: there is some text on top of the upper panels (DAPI, cGAS, Merge).

• *

* - "Through gene ontology analysis, we found that genes involved in endoplasmic reticulum (ER) stress were differentially expressed (Figure 4B)". I don't think that the way data are shown in Fig 4B is effective. Since GO has been performed, I would replace the table with a GO enrichment analysis graph. Ensure to report all the data in a supplementary .xls so that others can see and reuse it. Is there a mandated repository that accepts RNAseq data?*

The RNAseq experiment and data was performed by another group and reported in a previous study, as referenced in the main text of the manuscript (Epanchintsev A, Costanzo F, Rauschendorf MA, Caputo M, Ye T, Donnio LM, et al. Cockayne’s Syndrome A and B Proteins Regulate Transcription Arrest after Genotoxic Stress by Promoting ATF3 Degradation. Mol Cell. 2017 Dec;68(6):1054-1066.e6.). Here, we only re-analysed their data using STRING pathway analysis, as detailed in the Material and Methods. However, as suggested by the reviewer, we will replace the table by a GO enrichment graph.

- The volcano plot looks weird with many values at the maximum log10 (P-value) - is the data processed appropriately?

As mentioned above, the RNA Seq analysis was performed and published in a different study. We think this is because the Y axis shows adjusted P values.

- Figure 5B: the legend says "Latrunculin A". Please correct.

We will correct this

- For a Wellcome funded researcher, I'm surprised that the mandated OA statement and RRS is absent from the acknowledgements.

We will of course comply with the open access policy of the Wellcome Trust. However, and based on the WT requirements detailed on their website, we believe the acknowledgement section complies with the funder’s policy: “All research publications must acknowledge Wellcome's support and list the grant reference number which funded the research reported.”

Maybe mention the changes in nuclear shape is not a causative of nuclear blebbing. But maybe not say that they are completely mutually exclusive phenotype to each other.

suggestion

Maybe say that we will overexpress LEMD2 in CS-A cells and show that the NE phenotype can be significantly rescued. This will add value to this part of story. I remember when I did the FRAP experiment, CS-A cells with expression of LEMD2-GFP (that doesn’t form aggregates) looks better in term of shape.

I think Anne, please check the plasmid map? According to the lab inventory (Plasmids Anne), it is LEMD2-GFP. So probably GFP is at C-terminus.

I think there was a part in discussion was LEMD2-GFP was mistakenly written as GFP-LEMD… But I am sure I used LEMD2-GFP throughout the work

We cloned it into an empty pEGFP vector but still maintained LEM2-GFP. Maybe remove the C1 in the methods to avoid confusion as we removed the MCS and GFP and just used the blank vector and inserted lem2-gfp as we obtained it.

Same construct was used for GFP pulldown and for FRAP. And we can see in FRAp that they localise to the NE. SO it should localise to the NE. Maybe mention that we will do a LEMD2-GFP over expression experiment in CS-A cells and show that they do localise to the NE.

I don’t remember fully if Denny did this and what came out. I thought he did and ER stress and cytoskeleton regulation came out as enriched terms?

Denny will have to check this but I think this is because the Y axis shows adjusted P values?? I have the same in my data and Jack told me this is an artefact of the analysis if you adjust for multiple comparisons and is something more often seen in mass spec data

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, Yang and colleagues report that the absence of CSA (a protein with a well-characterised role in DNA damage repair and whose mutations cause a premature ageing syndrome) leads to defects in nuclear envelope (NE) integrity. Using a Cockayne syndrome patient-derived cell line they show that CSA deficiency correlates with the presence of an aberrant nuclear morphology, nuclear blebbing and increased cGAS-signalling. Moreover, they suggest that this CSA defective cell line presents decreased LEM2 at the NE and a consequent reduction in LEM2-laminA/C interaction. They were able to observe interaction betweenCSA and LEM2, andsuggested that CSA might interfere with LEM2 functionality at the nuclear envelope. Starting from the analysis of an already published RNAseq dataset, the authors go on investigating the cytoskeleton status in the CSA mutant cell line and identify an increase in actin, which they suggest leads to an increase in actin stress fibres. By promoting general actin depolymerisation and by disanchoring the cytoskeleton from the nuclear envelope, Yang et al are able to rescue the dysfunctional phenotypes reported above, suggesting that increased mechanical forces transmitted from the actin cytoskeleton to the nuclear envelope might cause defects in nuclear envelope integrity. Finally, the authors report that alleviating the nuclear envelope defects in CSA mutant cells does not decrease their sensitivity to a UV mimetic, hinting that CSA role in maintaining nuclear integrity is independent from its DNA damage repair function.

Major comments

The key conclusions of the manuscript are convincing and supported by the data. However, there are some conceptual concerns that limit my enthusiasm.

Firstly, that the actin cytoskeleton can transmit forces to the NE via the LINC complex is established. That these forces that lead to NE deformation, and in some cases, rupture, is somewhat unsurprising. The interesting observation in this manuscript is that CSA mutant patient cells exhibit more stress fibres. This leads to more LINC-dependent transmission of forces to the NE, with consequential effects on NE morphology and rupture. However, the mechanism by which actomyosin contractility is elevated in CSA-mutant patient cells is unexplored.

Secondly, it is unclear whether CSA controls the quality, or simply the number, of LEM2/Lamin interactions. As such, a mechanistic link between elevated stress fibres and CSA-dependent NE/lamina interactions is not provided and the paper sits as two presently unconnected observations.

The data are generally clear, well performed and well interpreted with some exceptions:

1. I appreciate the use of isogenic cell lines (a big plus when dealing with patient-derived cell lines). However, these lines were established 30 years ago and the reported phenotypes might be due to genetic drifts. To exclude this, I suggest to complement the HAP-1 ERCC8 KO cell line with exogenously expressed CSA and assess if this rescues the phenotypes reported. Validation of the KO in these lines, either by western blotting or sequencing is needed.
2. Related to the complementation of patient cell lines, the exogenous HA-CSA is not recognised by the anti-CSA in the CSA-null patient cell lines (Fig 1B, second blot). Shouldn't you be able to see this exogenous protein? HA-GFP-CSB in the complemented CSB-null patient cell line runs at the same weight as endogenous CSB (Fig 1B, fourth blot). This is also unexpected. I think you need better characterisation of your cell lines and need to demonstrate the level of exogenous transgenes that have been used to complement the cells and that they localise appropriately, presumably to the nucleus. You should also make sure to cite the paper where they were isolated and describe that they were immortalised (Troelstra et al., 1992) and the paper in which transgenes were stably overexpressed (Qiang et al., 2021).
3. Immunolocalisation of INM proteins is notoriously tricky and the permeabilisation steps include only 0.2% Tx100, which can be insufficient to permeabilise the INM. I appreciate the Emerin and Lamin immunostaining seems to have worked, but in many cases successful immunostaining can be antibody-specific. Can you try harsher permeabilisation to expose LEM2 epitopes? I'm somewhat uncomfortable with the suggestion that there is a cytosolic (ER?) pool of endogenous LEM2 as this runs counter to the literature and feel that your antibody or fixation conditions are illuminating a non-specific protein. The WB in Fig 2E shows that there is virtually no LEM2 in the "soluble" fraction. I would be more cautious on this cytoplasmic/nuclear pool interpretation. Biochemical nuclear and cytoplasmic fractionation would help clarify the signal in a NE vs a non-NE pool.
4. Pag 15: "Using a Proximity Ligation Assay (PLA), we showed a significant reduction in the number of PLA foci in CS-A cells compared to the WT(HA-CSA) cells, reflecting a reduced number of LEMD2-lamin A/C complexes (Figure 2G, 2H). This data suggests defects in the incorporation of LEMD2 into the NE and lamin protein complexes in CS-A cells". If you have less LEM2 in the NE, it is quite expected that you will have less "LEM2-laminA/C" complexes. To me the logic doesn't hold and this data does not suggest that there is an underlying defect in LEM2-lamin interaction. To ascertain whether there is such a defect one could perform an IP against LEM2 and quantify laminA/C, normalizing by the amount of LEM2 in the input.
5. "We overexpressed LEMD2-GFP and Flag-CSA constructs, followed by GFP pulldown in WT(HA-CSA) cells". Since the co-IP data are obtained in overexpression conditions (of both HA-CSA and Flag-CSA?), the authors should validate the interaction between LEM2 and CSA using an orthogonal approach. Perhaps anti-HA capture of the WT(HA-CSA) cells would allow you to immunoblot for endogenous LEM2?
6. Related to the CSA-LEM2 binding in the above experiment, the procedure involves combining a native detergent-extracted cytoplasmic pool with a denatured (RIPA-extracted) nuclear pool for performing the GFP-trap. From which pool was the tagged CSA bound to LEM2 in?
7. "The absence of CSA in CS-A patient cells does not affect the mobility of LEMD2 at the NE but instead decreases its interaction with A-type lamins". To me the fact that loss of CSA decreases LEM2-lamin interaction is not well supported (see point 3).
8. "Here, we showed by immunoprecipitation that LEMD2 also interacts with CSA. This suggests that the recruitment and stabilization of LEMD2 to the NE is mediated by an interaction with CSA, although the mechanism remains unclear". I think this is an overstatement: there are no data suggesting that CSA recruits or stabilises LEM2 at the NE.
9. As the authors suggest in the discussion, it would be worth checking whether LEM2 overexpression is able to rescue some of the NE defects reported, strengthening the hypothesis that LEM2 levels are at least in part responsible for the phenotypes reported.
10. To me it is not clear how the reported phenotypes are interrelated. The first part of the manuscript shows that CSA interacts with LEM2, and that loss-of-function CSA impacts on LEM2 levels and LEM2-lamin interaction, suggesting a direct role for CSA at the nuclear envelope. The second part of the manuscript shows that cells with defective CSA have more actin stress fibres and releasing the cytoskeleton-nuclear tethering is able per se to rescue the nuclear membrane and cGAS phenotypes. How do the authors reconciliate these two parts? Is CSA directly involved in both inner nuclear membrane homeostasis and actin cytoskeleton modulation or is this latter role upstream and the NE defects a mere consequence of increased cytoskeleton rigidity?
11. It is not clear how or why actin stress fibres are elevated in the CS-A cells. Can the authors provide any insight based on their RNAseq analysis? Demonstrating a link to ROCK, LIMK or Rho signalling would be interesting and verifying ppMLC2 levels would help explain why contractility is enhanced. Additionally, is the increase in contractility dependent upon any of the genes identified as up- or downregulated in RNAseq? Presently, the manuscript is missing a link between its two halves.
12. Related to point 1, the RNAseq comparison was performed on patient cells lacking CS-A and patient cells lacking CS-A and later over-expressing HA-CSA, and this comparison is used extensively for phenotype description in the manuscript. In isn't clear to me that this is the most insightful comparison to make; the rescue by overexpression is not as elegant as CRISPR reversion and the ko fibroblasts have presumably been surviving well in culture without CS-A before this protein was overexpressed. Can you validate the differential expression of any identified proteins in the acute HAP1 ko? Can you validate any of the differentially expressed proteins in comparison to normal fibroblasts (e.g., 13O6, as per Qiang et al., 2021)?

Minor comments

• Pag 14: "To characterize the NE phenotypes further, we obtained CS patient-derived cell lines carrying loss-of-function mutations in CSA (CS-A cells) or CSB (CS-B cells), and their respective isogenic control cell lines (WT(HACSA) and WT(HA-GFP-CSB))." What type of loss-of-function? Is the mutant protein still produced? In Fig 6A there seem to be a band in the CS-A blot (second lane), but in Fig 1B, there isn't. I think this is important to know to interpret the phenotype related to LEM2 interaction.
• Figure 1B is poorly annotated. What do - and + stand for? In general, I find a bit confusing how the WB are presented throughout the manuscript, specifically how the antibodies are reported (e.g., HA-CSA instead of HA). Please mark up all western blots with antisera used. Please make sure all expected bands are within the crops - e.g., Fig 3B, the anti-LEM2 blot should be expanded vertically to show the LEM2-GFP relative to endogenous LEM2.
• From the methods, it appears that you obtained a LEM2-GFP, and cloned it into an expression vector (pEGFPC1) to make GFP-LEM2. Please provide clarity on which construct was used in which figure, and verify that an N-terminally tagged LEM2 still localises to the NE.
• Fig 1I: there is some text on top of the upper panels (DAPI, cGAS, Merge).
• "Through gene ontology analysis, we found that genes involved in endoplasmic reticulum (ER) stress were differentially expressed (Figure 4B)". I don't think that the way data are shown in Fig 4B is effective. Since GO has been performed, I would replace the table with a GO enrichment analysis graph. Ensure to report all the data in a supplementary .xls so that others can see and reuse it. Is there a mandated repository that accepts RNAseq data?
• The volcano plot looks weird with many values at the maximum log10 (P-value) - is the data processed appropriately?
• Figure 5B: the legend says "Latrunculin A". Please correct.
• For a Wellcome funded researcher, I'm surprised that the mandated OA statement and RRS is absent from the acknowledgements.

Referees cross-commenting

I think the other reviews are fair and accurate

Significance

This work provides interesting insights on a possible new moonlighting role of the CSA protein. This could enhance the pathophysiological comprehension of some clinical manifestations in CS patients. The nuclear envelope defects are well described and convincing; however, there is no clear understanding of how (or even if) the reported cytoskeleton and nuclear envelope defects depend on CSA. Better characterising mechanistic roles of CSA in both nuclear envelope integrity and in stress fibre formation will boost the overall impact of the manuscript. At this stage, the manuscript could be of interest for a specialised audience (premature ageing syndromes) but with more mechanistical dissection it could become of broader interest (basic research, nuclear architecture/integrity readership).

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Yang et al. shows that ERCC8 (Cockayne syndrome A protein) mutations/loss of function causes nuclear envelope (NE) abnormalities and fragility, in addition to the well described deficiencies in transcription-coupled nucleotide excision repair (TC-NER). Cells from CS-A patients show decreased LEMD2-lamin A/C complexes at the NE and increased actin stress fibers that cause mechanical stress in the NE, in addition to more blebbing and ruptures of NE. This is turn causes activation of the innate/immune cGAS/STING pathway. Importantly, disrupting the LINC complex rescued NE problems and activation of the cGAS/STING pathway. This effect of ERCC8 dysfunction on NE integrity and activation of the cGAS/STING pathway may be behind patients' phenotypes of neuroinflammation, but not UV sensitivity.

The paper is well-written and for the most part, the data support the conclusions of the authors. Some minor caveats could be addressed to improve the quality of the manuscript.

• The phenotype of decreased LEMD2 incorporation into the NE in CS-A cells is minor. Only ~20% and thus, it is not clear whether this is causal of any of the NE abnormalities. It should be better explained how these data add to the story.
• Inducing actin polymerization and depolarization impact nuclear morphological abnormalities and nuclear blebbing. Do these treatments impact nuclear fragility and cGAS accumulation at NE break sites?
• Depletion of SUN1 in CS-A cells increased nuclear circularity, decreased blebbing, and phosphorylation of TBK1. The impact of SUN1 depletion in cGAS foci formation at NE break sites and phosphorylation of STING is not shown. Such experiments will provide stronger evidence that CS-A activates the cGAS-STING pathway in a SUN1 (mechanical stress)-dependent manner.

Referees cross-commenting

I am more positive than the other reviewers. I agree with reviewer 1 that another patient line would be great, and that some of the westerns need improvement. However, I still find that the phenotypes found in this cell line, which are rescued by the wild-type protein, are interesting and worth reporting. I do not fully agree with technical recommendations from reviewer 3, or suggesting that that the authors address questions outside the focus of their study.

Significance

The significance of the study is that shows for the first time the nuclear envelop defects and fragility in cells from Cockayne Syndrome patients (mutations in ERCC8) are due to mechanical stress that is alleviated by depletion of the LINC complex. In addition, the study shows activation of the cGAS-STING pathway in these cells, although the evidence about this phenotype could be strengthen.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Cockayne syndrome (CS), an autosomal recessive premature ageing/progeria disease, is caused by mutations in the genes coding for CSA and CSB. These play a well-studied role in transcription-coupled nucleotide excision repair. In this manuscript, CSA but not CSB dysfunction is associated with nuclear envelope defects, a typical phenotype of cells from progeria diseases caused by mutations in NE proteins. HPA model cells lacking CSA show an irregular nuclear envelope not observed in cells lacking CSB. Patient cells with defective CSA, compared to isogenic cells expressing the wild-type CSA protein, show more severe nuclear envelope deformation and blebbing and activation of the cGAS/STING signaling pathway, indicating nuclear envelope damage, a slight reduction in the expression of LEM2, a protein of the inner nuclear membrane, and a reduced interaction of LEM2 with the lamina component lamin A/C. Patient cells with defective CSA show aberrant acThe proposed link between CSA and nuclear envelope integrity is interesting. CSA would in this case a factor involved in DNA repair as well as nuclear envelope integrity, two processes linked to progeria. However, the work relies on a single patient derived cell line which is compared to the same cell line expressing the wild type protein. To consolidate, more cells form different CSA patients need to be included. If worked out this idea will be interesting all cell biologists interested in DAN damage repair and nuclear envelope structure and function as well as researchers interested in the molecular mechanisms of progeria syndromes. My expertise: nuclear envelope structure and function, nuclear transport tin stress fiber and their nuclei show different effects toward actin polymerization inhibitors or stabilizers. Downregulation of SUN1, one of the nuclear envelope proteins linking to the cytoskeleton, improves nuclear envelope blebbing phenotypes in CSA patient cells

Major comments:

Albeit the link between CSA and NE integrity the work is in my eyes too preliminary. Although the data presented are well done and carefully evaluated they mostly (except Fig 1A) rely on direct comparisons of one patient cell line (CS-A or CS-B) to the same cells expression the wildtype protein. It remains thus open whether the effects seen on LEM2 expression, LEM2-LaimA/C interaction, stress fibre formation, cGAS/STING signaling pathway activation in the CS-A cells are representative for a number of different CS patient derived cells. This is especially important given the small changes observed. Please note that there are alos clear differences between the CSA-wt and CSB-wt cells. Would the HPA CSA KO cells show in addition to NE irregularities (not even quantified) the same phenotypes and can they be reverted by re-expression of the wildtype CSA protein? The link between CSA and SUN1 is not well worked out. What is the effect of SUN2 downregulation and that of nespirins? It remains unclear whether the observed effects are indeed LINC mediated.

Minor comments:

Fig 1B: Why is HA-Tagged CSA not shown on the CSA western? This would be helpful to compare to the endogenous levels at least in CSB cells. A western showing an housekeeping marker would allow better comparison. Judging from the proteins markers HA-tagged CSA seems much larger as endogenous CSA (first versus second row). Again, less cropped western blots would help.

Fig 3A: Is CSA FLAG or HA-tagged? Or both? If both are expressed the question raises of why the CSA-LEM 2 interaction is only seen in an overexpression situation.

Fig 5: Inconsistency between figure and figure legend: 20 vs 25 nM Jasplakinolide. I assume Latrunculin A should read Cytochalasin D?

Fig5B: Not clear why in "CSA-wT cells" Cytochalasin D and Jasplakinolide have the same effect on nuclear envelope shape yet only Jasplakinolide increases the number of blebs.

Page 10: Method for IF: 4% (v/v) paraformaldehyde and 2% /v/v) should likely read (w/v).

Page 19: replace "withl" by "with".

Significance

The proposed link between CSA and nuclear envelope integrity is interesting. CSA would in this case a factor involved in DNA repair as well as nuclear envelope integrity, two processes linked to progeria. However, the work relies on a single patient derived cell line which is compared to the same cell line expressing the wild type protein. To consolidate, more cells form different CSA patients need to be included. If worked out this idea will be interesting all cell biologists interested in DAN damage repair and nuclear envelope structure and function as well as researchers interested in the molecular mechanisms of progeria syndromes.

My expertise: nuclear envelope structure and function, nuclear transport

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

The authors conducted a comprehensive investigation into the spatial and temporal expression patterns of Pcdh10 during brain development and employed two deficient mouse models to delve into its neurobehavioral functions, with a specific emphasis on ultrasonic vocalizations (USV). Interestingly, the authors found that heterozygous cKO pups showed an exaggerated effect on USV as compared to the ubiquitous heterozygous KO pups. These observations in general agree with previous studies of Pcdh10's complicated function in ASD-related neurodevelopment, as well as USV, indicating its important function in neurodevelopment. However, several key concerns warrant attention:

Major comments:

1. The authors analyzed published scRNAseq adult mouse dataset and found that Pcdh10-expressing cells differentially expressed genes involved in vocalization behaviors, including Foxp2, Cntnap2, Nrxn1 and Nrxn3, as compared to cells that did not express Pcdh10. Given that the authors also performed bulk RNA-seq experiments using the sorted cKO cells, it would be interesting and important to include these data in the analysis and validate whether the above genes are differentially expressed in the animal model in the current study. This may provide additional molecular mechanisms of the behavioral abnormality observed in the animal models.
2. In Figure 1S, the synapse assembly is one of the most significant GO-terms. Does Pcdh10 deficiency affect neuromophology and synaptic density/assembly? Characterizing the neuroanatomy of the animal model will provide a neuronal explanation for the behavioral abnormalities observed in this study.
3. Could the authors explain why cHE mice display a stronger phenotype than cKO at P6? Also, why cHE and cKO show stronger phenotypes than whole-body KO? Does this data indicate that loss of Pcdh10 in the inhibitory neurons only resulted in E-I in-balance? The authors should at least discuss the possibilities of this result they observed.

Minor comments:

1. It would be interesting and important to know the level of PCDH10 at the adult stage after P7 to learn whether this gene also plays an important role beyond early development.
2. Besides USV, does Pchd10 deficiency in mice show other autistic phenotypes in adolescence and adulthood, such as social interaction and repetitive behavior?

Significance

The experiments are well designed and the detailed characterization of USV in the animal models would be informative for the audience who are interested in Pcdh10's function in neurodevelopment and Social Communication. However, because previous studies already showed the function of PCDH10 in multiple mouse models, the novelty of this study is limited. The observation that cKO/cHE mice show stronger phenotype than whole-body KO mice could be potentially interesting, it would be nice if the authors could provide some explanation of this result with additional experimental evidence.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this paper the authors present a new cKO mouse model for PCDH10-related ASD. This model consists of the ablation of PCDH10 specifically in interneurons of the basolateral complex. Interestingly, the use of this mouse model together with a complete KO adds evidence towards an excitatory/inhibitory imbalance causing the ASD phenotype, rather than the complete ablation of a protein (in this case PCDH10). Firstly, the developmental dynamics of PCDH10 are measured with diverse techniques. The presence of PCDH10 at embryonic stages in different areas of the basal forebrain. Here it is made clear why the specific downregulation of PCDH10 in Gsh2- lineage interneurons. The cKO mouse model is validated with bulk RNA sequencing fluorescence imaging of the eGFP reporter in the telencephalon. The KO mouse model is validated with WB assay showing the gradual decrease of PCDH10 in Het and Ho mice. Secondly, the USV emitted by isolated pups throughout development (P3, P6, P9 and P12) are analysed with different parameters in both mouse models.

Major Comments

1. The role of anxiety in the phenotype described in this work should be supported by behavioural experiments in adulthood (Open field/light/dark/Plus Maze test)2-3M for mice to reach the appropriate age + 2 weeks for performing the experiments and extracting results.
2. The WB in panel F1C&E should be done with non-pooled biological replicates to be informative 3 weeks
3. The statistical test used for F2B and F3D-I needs to be specified.
4. The reduced GABA input in the amygdala that is hypothesized to be causing the phenotype could be studied by iPSP analysis through LFP (OPTIONAL) 1M

Minor comments

1. The results section should be subdivided in sections corresponding to each figure
2. Detail the pinhole opening in M&M used for the imaging of the images in panel of Figure 1 M-R
3. The group size and the power calculation used to determine it should be detailed in M&M
4. The WB membrane image in Panel 1F has saturated pixels, the image needs to be changed
5. Instead of asterisks, writing the exact p-value is more informative in the graphs
6. Figure 1B & D: detail what the Pcdh10 levels are normalised to. In the legend there's a typo "no-way ANOVA"
7. Figure 1F: specify what it means P17.5 (norm)
8. Figures 3-4: choose higher contrast colours for an easier readability and more accessibility.
9. Figure 3B: the WB image needs to be at a higher resolution
10. Figure 3C: the colour coding for dBFS in the spectrogram needs to be specified in the maximum and minimum number.
11. Figure 3D-I & 6G: results would be more clear if shown as a ratio of the WT (would be also more evident the mouse model differences). Also the titles of the graphs are misleading, as the graphs are showing data from all the genotypes of the mouse models.
12. Figure 2B: specify what it is normalised to
13. Figure 4 E-H: it is not described what the dotted lines correspond to.
14. In all the figures, the panels are excessively subdivided, the following panels should be grouped in one:
    • a. Figure 1: i. C & E are showing the same data

ii. G-I are showing the same data

iii. J-L are showing the same data

iv. M-R are showing the same data - b. Figure 2: panel 2C-G are showing the same data - c. Figure 3: i. A-B are showing the same data

ii. D-I are showing the same data - d. Figure 4: i. A-C are showing the same data

ii. E-H are showing the same data - e. Figure 5: the frequency parameters (A-E) should be all 1 panel f. Figure 6: B-E are showing the same data

Significance

The detailed study of the socio-affective communication of these mouse models is accurate and quite informative. There is still a big body of work to do for classifying and using pup USV as biomarkers for mouse model phenotyping, and this thorough work is a step forward. This type of work will be of interest to neurodevelopmental neuroscientists interested in behaviour and mouse model phenotyping. However, the claim of an autistic-like phenotype would be much stronger with additional behavioural assessments in adulthood (as USV in mating behaviour, social novelty recognition and stereotypical behaviours). In addition, the hypothesis of an excitation/inhibition imbalance is interesting, but correlational in this work. Further experiments would need to be done to prove causality.

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Referee #1

Evidence, reproducibility and clarity

This paper provides evidence that Pcdh10 (associated with autism spectrum disorder) is involved in anxiety-like behavior and socio-affective communication in developing mouse pups. Using a specific Cre-driver line targeting Gsh2-lineage interneurons, the authors performed a series of behavioral analyses, including isolation-induced ultrasonic vocalization. Particularly, the authors provided detailed analyses to provide distinct clusters that might correspond to identified call types. This work is excellent and I do not have any further comments, except one minor comment: why did the authors use CD1 line to generate the mouse lines, instead of C57BL/6 substrains?

Significance

This is of paramount significance, such that Pcdh10 expressed in Gsh2-lineage interneurons (a subpopulation in the basolateral complex of the amygdala) is required for isolation-induced ultrasonic vocalization.

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General Statements

We thank the reviewers for their constructive feedback on our study. We have updated the manuscript according to their recommendations.

Two of the three reviewers raised concerns about the quality of some of our data, in particular of the DP population. Since most DP samples suffered from low coverage, introducing bias when being compared to the higher quality data, we moved all results involving DP to the Supplement. We mention this in the Discussion. The main text and its figures were updated to focus on the remaining three wild populations and two laboratory strains.

We rewrote parts of the Abstract, Introduction and Discussion to clarify the comparison between the NLR families of Arabidopsis thaliana and Danio rerio. In regard to this, we also added an extra panel to figure 3.

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

General comments:<br /> 1) Odd statement in abstract comparing plants to fishes - why not put in context of animals in general, or vertebrates in particular? Same in the introduction and discussion. Either a more broad comparative framework should be set - from plants, through invertebrates to vertebrates, or it should be shortened and perhaps discussed in the light of diversity present in e.g., fish or just vertebrates. A persistent focus on plants is peculiar and does not seem to provide adequate background/context._

We have made an effort to clarify the reason for mentioning NLRs from A. thaliana in the Abstract, Introduction and Discussion. We added a plot to figure 3, which is analogous to figure 3A from Van de Weyer et al., 2019 where the pan-NLRome of A. thaliana is analysed.

Furthermore, we added a paragraph discussing copy number variation of another immune gene family (MHC genes) in vertebrates.

2) Methods seem overall well described, and the analyses seem to have been performed diligently-although I am not an expert in the field. One aspect that would be important to evaluate methodology is the repeatability of NLR detection - If we perform the procedure twice on DNA sample from a single individual, how repeatable collection do we get?

It is possible that we might have failed to identify a few NLRs from some individuals. Unfortunately, sequencing could not be repeated due to the limited amount of raw tissue. The population DP in particular is problematic since we had low sequencing depths across all of its samples. We have now excluded it from the main results and moved it to the Supplement. Still, we are confident that the general feature of widespread copy number variation both within and between populations persists even if the experiments were repeated. One argument for this is that the non-linear functions describing pan-NLRome sizes are fairly consistent among wild populations. Also, sample sizes of about 20 individuals per (wild) population are large enough to compensate for poor data quality of one or two indviduals. Finally, we found a substantial fraction of NLRs to be present in all wild populations, including DP. It would be unlikely to detect so many shared genes if the amplified sequences were spurious or the NLR identification procedure faulty.

We have expanded the discussion of the caveats of our approach.

3) Discussion is quite speculative, and some claims seem exaggerated; in conclusions, eg: "This study advances our understanding of the evolutionary dynamics affecting very large gene families." - as the study is mostly descriptive documentation od CNV of gene (or, gene fragments) I am not convinces how it really advances "understanding of the evolutionary dynamics".

We toned down Discussion and Conclusions.

Minor points:

At this stage the journal and so the audience is unknown, so perhaps this will not be an issue - but for a broader audience, a better explanation of what PRY/SPRY/B30.2 are would be useful._

We added an explanation.

English could be smoothed, certain sentences sound odd: eg. lines 87-89; or 90-93 - Studies have shown that viral and bacterial infections can induce the expression of specific fish NLRs (reviewed in (24)). Some have PYD or CARD domains and can even form inflammasomes similar to mammalian NLRs (25, 26). - could be read as if infections had PYD or CARD domains, not NLRs. Lines 239-240 - not sure what does "presence/absence variation" mean here.

We made an effort to improve language style.

Sequence of baits used should be provided in some supplement or repository.

The sequences are now attached to the manuscript as a supplementary dataset.

Reviewer #1 (Significance):

The article tackles an overall interesting subject: an expansion of a relevant group of genes in one of the major model species of biomedical importance. The main strength of the study is putting in context variation found in the lab strains - via comparison to wild populations. A limited and "haphazard" genetic variation (especially of genes involved in immune processes) of laboratory models can have paramount implications for the interpretation of experimental studies._

We expand on this in the Discussion._

That being said, expansion of NLR family in teleosts in general, and in zebrafish in particular, has been previously described (eg, https://bmcecolevol.biomedcentral.com/articles/10.1186/1471-2148-8-42_), and this study mainly expands description of this phenomena.

The expansion of NLRs has indeed been described before and in great detail. The manuscript contains multiple references on this topic, including the one recommended by the reviewer (e.g. Stein et al., 2007, Laing et al., 2008, Howe et al., 2016). The previously reported expansion of NLRs in the reference genome was a description, but not an interpretation "in the light of evolution". We demonstrate that gene birth, death, and presence/absence variation are ongoing processes and active on a population-genetic time scale.

Given the methodology, little can be said about possible functions of the discovered diversity. In particular, a technical aspect imposing limitation of sequence length resulted in a collection of exons, but not full genes - precluding e.g., deepened analysis of domain architecture.

We agree that our study does not reveal much about the function of the NLR-C genes. The focus on function in the discussion was disproportionate to our findings and we have reduced it to avoid speculation.

Selection analysis is also quite limited in scope; there are several, more sophisticated tools to infer balancing or purifying selection, either pervasive or episodic (see eg. excellent tools of_ https://www.datamonkey.org__/_).

Yes. However, with our limited amount of data, we deliberately do not want to speculate too much about selection. As mentioned in the text, many genes are monomorphic in our sample. To reliably infer the action of selection, and more so to distinguish it from signatures of demographic history, a much broader basis of sequence data is needed.

Nonetheless, the study certainly highlights the possible importance of such an expanded group of genes in this species, with a potential to inspire further - more mechanistic/functional research in this area. The article will likely interest a few groups of rather specialized audience - e.g., those working in NLR genes in particular, or in immunity of zebrafish (or fish in general). Another, somewhat broader angle, able to attract a wider audience would be subjects of general evolution of multigenic families (birth-and-death models, trade-offs at different CNV etc.) and comparative analysis to other groups of animals - or genes - evolving in a similar way. My field of expertise is diversity and evolution of adaptive branch of the immune system in vertebrates, in particular non-model vertebrates.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:

The authors have examined the variation of the immune related gene family "Nucleotide-binding domain Leucine-rich Repeat containing" (NLR) in the zebrafish Danio rerio. These proteins, while highly divergent, are conserved across animal and plant species. In humans or rodents, the number of these genes is relatively small (20-30) but other species such as Arabidopsis appear to have >10,000 NLR genes.<br /> Schäfer et al. collected 67 wild-type zebrafish from 4 independent sites near the Bay of Bengal and added 8 fish each from the laboratory strains Tübingen (TU) and Cologne (CGN). Using DNA capture and sequencing technology, they identified 1,560 unique "FISNA-NACHT" domains representing different NLR genes and 574 NLR-associated B30.2 domains. A subset, 714 and 229 respectively, were identified in all of the fish populations representing a "core" set common NLR genes. A significant subset of the genes could not be aligned to the GRCz11 reference suggesting significant variation across subpopulations of zebrafish.

Major comments:<br /> None. The work is straight-forward, carefully done and conservatively interpreted.

Minor comments:<br /> GRCz11 is still a very fragmented assembly, particularly chr4 where heterochromatin repeats on the long arm were intractable to short read sequences. There is a more recent assembly generated by the Tree of Life initiative (GCA_944039275.1) from the SAT fish line that may allow a more robust alignment and placement of the NLR genes, perhaps even some phasing of unassembled fragments._

We have examined some of the existing long-read based zebrafish assemblies and found that even the length of chromosome 4 that contains most of the NLRs can significantly differ between different strains and different genome assemblies. This is also in agreement with the recent findings of McConnell et al., 2023 on large structural differences on this chromosome between three strains derived from the AB genetic background. We now mention this finding and the alternative existing zebrafish assemblies in the Discussion.

Reviewer #2 (Significance):

General assessment:<br /> Obtaining more data on the inherent variation within species of NLR genes as well as collecting more cross-species data for evolutionary comparisons is valuable for our understanding of this interesting but poorly understood class of immune response genes as well as the dynamics of gene duplication/deletion in complex, repeated arrays.<br /> -The major strength of the study is the efforts put into capturing wild-type zebrafish from multiple different locations to maximize the diversity of the NLR sequences.<br /> -The primary limitation is targeted capture is always contingent on having enough homology in the probes to capture all the desired genes in roughly even proportions. Some of the more interesting NLR genes might have diverged too much to be properly captured but could provide critical information on evolutionary functional adaptation. Similarly, while based on cost, it is understandable why sequence capture was chosen, but phasing information across clusters could help explain (or discover) very diverse haplotype sequences in the introns of many of these gene arrays. As sequencing costs drop, this is an important aspect to the evolution of zebrafish chromosome 4 (as well as the rest of the genome). "Pangenome" differences in the zebrafish genome might be quite radically different.

Yes, we are aware of this possibility and discussed it now in more detail._

Advance:<br /> The study represents an important characterization of a poorly understood but important class of immune genes. A very similar (but more detailed) characterization of Arabidopsis NLR genes by Van de Weyer et al., Cell 2019, is considered an important advance to the plant biology community and has been highly cited since its publication. The collected data is potentially quite useful for future studies that want to understand the complex dynamics of highly repetitive, yet functional regions of the genome and how it can result in the creation and extinction of new genes.

Audience:<br /> There are two main likely audiences, those interested in how NLR genes are involved immune protection and those interested in genomes and evolution. It probably doesn't reveal a fundamental biological principle that would be of broad, general interest to the research community.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:<br /> The authors performed exon capture sequencing of FISNACHT and B30.2 domains from individuals among various inbred and wild zebrafish populations. This study provides average numbers of domains per fish and thus a valuable estimate for the size of the pan-NLRome in zebrafish.

Major comments:<br /> - Are the key conclusions convincing?_ Yes, and overall their findings are also consistent with what has been found in other model systems, most notably Arabidopsis (Weyer 2019, https://www.cell.com/cell/fulltext/S0092-8674(19)30837-2).<br /> - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?<br /> 'Complex patterns of inheritance' is unclear from significance statement.

We have reformulated this sentence.

For mechanisms driving copy number differences, haplotypes/segregation need not be presented as a model opposed to birth and death gene evolution/tandem duplication. These may both operate at different scales.

Yes, we reformulated.

• Are the data and the methods presented in such a way that they can be reproduced?<br /> Yes, overall, though the authors could provide sequences for their adapters, similar to Weyer 2019. It seems that raw data for this study is not yet available in NCBI: https://www.ncbi.nlm.nih.gov/bioproject/966920

The data will be made available at the time of publication. The sequences for all baits used, including non-NLR-ones, have been added as a supplementary .fasta-formatted text file.

Minor comments:<br /> - Specific experimental issues that are easily addressable.<br /> Their targeted exon capture approach cannot ensure that all NLR genes will be sequenced. This method also does not sequence across other exons from NLR genes, providing only a partial view of NLR gene structure and evolution. This may miss for example additional integrated domain architectures or evidence of physical clustering in the genome (Thatcher 2023, https://bsppjournals.onlinelibrary.wiley.com/doi/10.1111/mpp.13319). Nevertheless, focusing on capturing and enumerating FISNACHT domains as the most conserved and characteristic domain for NLRs appears to be a reasonable approach for estimating rough copy numbers.

We agree with the reviewer and have now added explanatory text on this topic to the discussion.

Unfortunately, mapping these domains back to only a single reference genome also means that the accuracy of their predictions for these domains, including which belong to genes or pseudogenes, is likely to be more error-prone (Wang 2019,https://www.pnas.org/doi/10.1073/pnas.1910229116), particularly for more divergent sequences. This may lead to additional limitations for assigning one-to-one relationships between FISNACHT domains, which they measure, and genes, which they seek to enumerate.

Thank you for pointing out the above reference. This is a limitation that we realized early on in the study after which we decided to not rely on the reference genome at all, instead opting to assemble and cluster all data de novo. In the manuscript we only use the reference genome for checking which of our identified NLRs have a clear homologue to satisfy potential interest by the biomedical community. All the other analyses were conducted based on the de novo assemblies and orthologous clusters._

In addition, many of their samples appear to be of poor DNA quality, meaning that

modeling estimates of domain copy number for the population can appear erroneous, even perhaps off by as much as a factor of 10 for the DP strain. This may contribute to some curious 'artifact' in some of the figures, such as Figs S2B1, S3B, S4C2, particularly for the B30.2 sequences in DP. The authors mention 'low sequencing depths' and 'low coverage' as contributing factors for this 'artifact' but also invoke possible 'evolutionary factors' in the discussion. Additional discussion for the apparent experimentally-induced effects on underestimating B30.2 sequences (perhaps due to increased DNA fragmentation and smaller domain size?), rather than coincidence of low coverage and actual biological strain-specific loss of B30.2 domains, appears warranted.

As mentioned in the text, although samples from the population CHT were older than the others and slightly degraded, they were rescued by applying the PreCR Repair Mix from New England Biolabs. We incorporated incubation with the reagent to the standard protocol that we used for all samples. The other samples had no quality problem.

Furthermore, the reviewer raises concerns regarding data quality for the DP population samples. After careful consideration, we decided to exclude the DP data and its analysis from the main text and deferred it to the supplementary material with the necessary remarks of caution. The main text now focuses on the other three wild populations, which did not have those issues.

Additionally, as per the reviewer’s suggestion, we discuss the additional caveats of bait-based targeted sequencing, especially for B30.2 domains._

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?<br /> Statement in the abstract about fewer (not 'less') NLRs in lab strains vs wild: consider revising to average # NLRs per individual._

We changed the respective sentence in the abstract.

Revise Fig 3C legend: 'Totally discovered NLR genes', e.g., to 'total # NLR genes'.

The recommended change was made to the figure legend.

Reviewer #3 (Significance):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.<br /> This study elucidates the pan-NLRome of zebrafish via application of a somewhat new technique.

• Place the work in the context of the existing literature (provide references, where appropriate).<br /> The authors apply a targeted capture and long read technology previously used in plants (Weyer 2019) to fish, thereby elucidating the pan-NLRome of zebrafish, a vertebrate with a large # of NLR genes. Previous studies has shown NLR gene variation in zebrafish, but had not compared levels within and between strains, or estimated a total NLR # across populations._

• State what audience might be interested in and influenced by the reported findings.<br /> Those interested in immune function, genetic diversity and genome evolution.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.<br /> Immune genes and evolution. The specific statistical approach_

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors performed exon capture sequencing of FISNACHT and B30.2 domains from individuals among various inbred and wild zebrafish populations. This study provides average numbers of domains per fish and thus a valuable estimate for the size of the pan-NLRome in zebrafish.

Major comments:

• Are the key conclusions convincing?

Yes, and overall their findings are also consistent with what has been found in other model systems, most notably Arabidopsis (Weyer 2019, https://www.cell.com/cell/fulltext/S0092-8674(19)30837-2).<br /> - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

'Complex patterns of inheritance' is unclear from significance statement.

For mechanisms driving copy number differences, haplotypes/segregation need not be presented as a model opposed to birth and death gene evolution/tandem duplication. These may both operate at different scales.<br /> - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Not necessary<br /> - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

NA<br /> - Are the data and the methods presented in such a way that they can be reproduced?

Yes, overall, though the authors could provide sequences for their adapters, similar to Weyer 2019. It seems that raw data for this study is not yet available in NCBI: https://www.ncbi.nlm.nih.gov/bioproject/966920<br /> - Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

Their targeted exon capture approach cannot ensure that all NLR genes will be sequenced. This method also does not sequence across other exons from NLR genes, providing only a partial view of NLR gene structure and evolution. This may miss for example additional integrated domain architectures or evidence of physical clustering in the genome (Thatcher 2023, https://bsppjournals.onlinelibrary.wiley.com/doi/10.1111/mpp.13319). Nevertheless, focusing on capturing and enumerating FISNACHT domains as the most conserved and characteristic domain for NLRs appears to be a reasonable approach for estimating rough copy numbers.

Unfortunately, mapping these domains back to only a single reference genome also means that the accuracy of their predictions for these domains, including which belong to genes or pseudogenes, is likely to be more error-prone (Wang 2019, https://www.pnas.org/doi/10.1073/pnas.1910229116), particularly for more divergent sequences. This may lead to additional limitations for assigning one-to-one relationships between FISNACHT domains, which they measure, and genes, which they seek to enumerate.

In addition, many of their samples appear to be of poor DNA quality, meaning that modeling estimates of domain copy number for the population can appear erroneous, even perhaps off by as much as a factor of 10 for the DP strain. This may contribute to some curious 'artifact' in some of the figures, such as Figs S2B1, S3B, S4C2, particularly for the B30.2 sequences in DP. The authors mention 'low sequencing depths' and 'low coverage' as contributing factors for this 'artifact' but also invoke possible 'evolutionary factors' in the discussion. Additional discussion for the apparent experimentally-induced effects on underestimating B30.2 sequences (perhaps due to increased DNA fragmentation and smaller domain size?), rather than coincidence of low coverage and actual biological strain-specific loss of B30.2 domains, appears warranted.<br /> - Are prior studies referenced appropriately?

yes<br /> - Are the text and figures clear and accurate?

yes<br /> - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Statement in the abstract about fewer (not 'less') NLRs in lab strains vs wild: consider revising to average # NLRs per individual.

Revise Fig 3C legend: 'Totally discovered NLR genes', e.g., to 'total # NLR genes'.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This study elucidates the pan-NLRome of zebrafish via application of a somewhat new technique.<br /> - Place the work in the context of the existing literature (provide references, where appropriate).

The authors apply a targeted capture and long read technology previously used in plants (Weyer 2019) to fish, thereby elucidating the pan-NLRome of zebrafish, a vertebrate with a large # of NLR genes. Previous studies has shown NLR gene variation in zebrafish, but had not compared levels within and between strains, or estimated a total NLR # across populations.<br /> - State what audience might be interested in and influenced by the reported findings.

Those interested in immune function, genetic diversity and genome evolution.<br /> - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Immune genes and evolution. The specific statistical approach

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors have examined the variation of the immune related gene family "Nucleotide-binding domain Leucine-rich Repeat containing" (NLR) in the zebrafish Danio rerio. These proteins, while highly divergent, are conserved across animal and plant species. In humans or rodents, the number of these genes is relatively small (20-30) but other species such as Arabidopsis appear to have >10,000 NLR genes.<br /> Schäfer et al. collected 67 wild-type zebrafish from 4 independent sites near the Bay of Bengal and added 8 fish each from the laboratory strains Tübingen (TU) and Cologne (CGN). Using DNA capture and sequencing technology, they identified 1,560 unique "FISNA-NACHT" domains representing different NLR genes and 574 NLR-associated B30.2 domains. A subset, 714 and 229 respectively, were identified in all of the fish populations representing a "core" set common NLR genes. A significant subset of the genes could not be aligned to the GRCz11 reference suggesting significant variation across subpopulations of zebrafish.

Major comments:

None. The work is straight-forward, carefully done and conservatively interpreted.

Minor comments:

GRCz11 is still a very fragmented assembly, particularly chr4 where heterochromatin repeats on the long arm were intractable to short read sequences. There is a more recent assembly generated by the Tree of Life initiative (GCA_944039275.1) from the SAT fish line that may allow a more robust alignment and placement of the NLR genes, perhaps even some phasing of unassembled fragments.

Significance

General assessment:

Obtaining more data on the inherent variation within species of NLR genes as well as collecting more cross-species data for evolutionary comparisons is valuable for our understanding of this interesting but poorly understood class of immune response genes as well as the dynamics of gene duplication/deletion in complex, repeated arrays.

• The major strength of the study is the efforts put into capturing wild-type zebrafish from multiple different locations to maximize the diversity of the NLR sequences.
• The primary limitation is targeted capture is always contingent on having enough homology in the probes to capture all the desired genes in roughly even proportions. Some of the more interesting NLR genes might have diverged too much to be properly captured but could provide critical information on evolutionary functional adaptation. Similarly, while based on cost, it is understandable why sequence capture was chosen, but phasing information across clusters could help explain (or discover) very diverse haplotype sequences in the introns of many of these gene arrays. As sequencing costs drop, this is an important aspect to the evolution of zebrafish chromosome 4 (as well as the rest of the genome). "Pangenome" differences in the zebrafish genome might be quite radically different.

Advance:

The study represents an important characterization of a poorly understood but important class of immune genes. A very similar (but more detailed) characterization of Arabidopsis NLR genes by Van de Weyer et al., Cell 2019, is considered an important advance to the plant biology community and has been highly cited since its publication. The collected data is potentially quite useful for future studies that want to understand the complex dynamics of highly repetitive, yet functional regions of the genome and how it can result in the creation and extinction of new genes.

Audience:

There are two main likely audiences, those interested in how NLR genes are involved immune protection and those interested in genomes and evolution. It probably doesn't reveal a fundamental biological principle that would be of broad, general interest to the research community.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Study by Schäfer et al. investigates diversity of NLR family genes in zebrafish (Danio rerio). Genes belonging to this vast family are implicated in various defense/immune functions across studied domains of life, and form extensive families of often highly duplicated genes. Here, repertoire of NRL genes was studied in 93 individuals, coming from both laboratory strains and natural populations. Authors found a relevant, intra-specific copy number variation in the NLR genes in zebrafish, and a higher diversity of these genes in wild animals, compared to their laboratory counterparts.

General comments:

1. Odd statement in abstract comparing plants to fishes - why not put in context of animals in general, or vertebrates in particular? Same in the introduction and discussion. Either a more broad comparative framework should be set - from plants, through invertebrates to vertebrates, or it should be shortened and perhaps discussed in the light of diversity present in e.g., fish or just vertebrates. A persistent focus on plants is peculiar and does not seem to provide adequate background/context.
2. Methods seem overall well described, and the analyses seem to have been performed diligently-although I am not an expert in the field. One aspect that would be important to evaluate methodology is the repeatability of NLR detection - If we perform the procedure twice on DNA sample from a single individual, how repeatable collection do we get?
3. Discussion is quite speculative, and some claims seem exaggerated; in conclusions, eg: "This study advances our understanding of the evolutionary dynamics affecting very large gene families." - as the study is mostly descriptive documentation od CNV of gene (or, gene fragments) I am not convinces how it really advances "understanding of the evolutionary dynamics".

Minor points:

At this stage the journal and so the audience is unknown, so perhaps this will not be an issue - but for a broader audience, a better explanation of what PRY/SPRY/B30.2 are would be useful.

English could be smoothed, certain sentences sound odd: eg. lines 87-89; or 90-93 - Studies have shown that viral and bacterial infections can induce the expression of specific fish NLRs (reviewed in (24)). Some have PYD or CARD domains and can even form inflammasomes similar to mammalian NLRs (25, 26). - could be read as if infections had PYD or CARD domains, not NLRs. Lines 239-240 - not sure what does "presence/absence variation" mean here.

Sequence of baits used should be provided in some supplement or repository.

Significance

The article tackles an overall interesting subject: an expansion of a relevant group of genes in one of the major model species of biomedical importance. The main strength of the study is putting in context variation found in the lab strains - via comparison to wild populations. A limited and "haphazard" genetic variation (especially of genes involved in immune processes) of laboratory models can have paramount implications for the interpretation of experimental studies.

That being said, expansion of NLR family in teleosts in general, and in zebrafish in particular, has been previously described (eg, https://bmcecolevol.biomedcentral.com/articles/10.1186/1471-2148-8-42), and this study mainly expands description of this phenomena. Given the methodology, little can be said about possible functions of the discovered diversity. In particular, a technical aspect imposing limitation of sequence length resulted in a collection of exons, but not full genes - precluding e.g., deepened analysis of domain architecture. Selection analysis is also quite limited in scope; there are several, more sophisticated tools to infer balancing or purifying selection, either pervasive or episodic (see eg. excellent tools of https://www.datamonkey.org/). Nonetheless, the study certainly highlights the possible importance of such an expanded group of genes in this species, with a potential to inspire further - more mechanistic/functional research in this area.

The article will likely interest a few groups of rather specialized audience - e.g., those working in NLR genes in particular, or in immunity of zebrafish (or fish in general). Another, somewhat broader angle, able to attract a wider audience would be subjects of general evolution of multigenic families (birth-and-death models, trade-offs at different CNV etc.) and comparative analysis to other groups of animals - or genes - evolving in a similar way.

My field of expertise is diversity and evolution of adaptive branch of the immune system in vertebrates, in particular non-model vertebrates.

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Reply to the reviewers

My response to the reviewers appears in the uploaded "Revision Plan" PDF file

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Referee #3

Evidence, reproducibility and clarity

This study by Chourasia et al determined the effects of MTCH2 deletion on the total metabolite content (polar and lipid metabolites) per total protein of HeLa cells, analyzed at different consecutive times after adding fresh and complete media (high glucose, 10%FBS). They also analyzed the effects of nutrient depletion (no FBS In addition, authors assessed the effects of MTCH2 deletion on mitochondrial morphology, lipid droplet number and size in HeLa cells, as well as in the differentiation of mouse fibroblasts to adipocytes. From the metabolite snaphots under htese differents times and conditions, authors conclude that MTCH2 deletion increases mitochondrial oxidative function to induce a catabolic state, which impedes lipid synthesis and, as a result, adipocyte differentiation. The major concerns are that it is unclear whether the metabolic phenotype observed is a consequence of MTCH2 deletion inducing a decrease in proliferation of HeLa, as well as of fibroblasts that need to reach confluence to differentiate. In this regard, it is also unclear whether MTCH2 deletion increases ATP demand and/or promotes a catabolic program, as metabolic flux analyses are missing. A minor concern is the use of computer (processing system), antenna and wifi analogies to describe the role of MTCH2 in mitochondrial function, which is confusing.

Significance

This study represents a thorough characterization of the metabolite content in proliferating HeLa cells in the absence of MTCH2 expression. The changes observed in polar and lipidic metabolites are novel, interesting and contribute to our understanding on the role of MTCH2 function in cellular metabolism. The main limitation of the study is that the levels of most metabolites are normalized by protein content, comparing conditions in which cell number and protein synthesis have changed. Thus, it is unclear whether some of the effects observed are a consequence of the reported role of MTCH2 supporting the proliferation of different tumors and cell lines, or whether it is a direct effect of MTCH2 increasing ATP demand and/or being a direct activator of mitochondrial catabolism. Related to this point, it is unclear whether the defect in adipocyte differentiation induced by MTCH2 KO in NIH3T3 fibroblasts might be caused by an inability of MTCH2 KO to reach confluency at day 0, needed for differentiation.Finally, respirometry and mitochondrial ROS content analyses would be needed to confirm that the changes in the metabolite levels induced by MTCH2 are caused by an increase in mitochondrial oxidation leading to nutrient depletion, as authors conclude. For example, an increase in the ADP/ATP ratio could also be caused by an inhibition of mitochondrial ATP synthase in the mitochondria, concurrent to an increase in ROS production, which would decrease NADH and NADPH content.

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Referee #2

Evidence, reproducibility and clarity

Mitochondrial carrier homolog 2 (MTCH2, SLC25A50) loss induces alterations in mitochondrial dynamics and energy utilization. However, the molecular mechanisms underlying these changes are still unknown. The study employs temporal metabolomic and lipidomic analyses, uncovering heightened catabolism, increased lipid storage, and disrupted adipogenesis in MTCH2 KO cells. The manuscript provides a comprehensive metabolic profile, revealing ATP demand increase, oxidized cellular environment, and adaptive changes in MTCH2 KO cells. Notably, in line with the fundamental role of fatty acid biosynthesis and anabolism in adipogenesis, the authors demonstrates that MTCH2 loss inhibits adipocyte differentiation. This work offers novel insights into the broader metabolic consequences of MTCH2 depletion.

Major comments:

• The key conclusions of the paper align with the conducted experiments, but a few additional experiments are necessary to state some claims and provide more robust conclusions.

• The paper could benefit from the inclusion of specific experiments, particularly those that address the following aspects:

• Validate MTCH2 ablation in HeLa and NIH3T3L1 through sequencing of clonal lines, Western blot analysis to confirm the absence of the protein, and real-time PCR to assess whether the mechanism involves mRNA decay.

• Provide a more detailed rationale for their temporal metabolomics approach, elucidating the choice of the media and the timepoints of cell collection. The method involves an initial culture of the cells in DMEM medium, followed by a switch to complete medium (CM) for overnight cell growth, and subsequent refreshment with CM for different timepoints before the metabolomics analyses. Authors should articulate the reasoning for opting for CM. Furthermore, authors should explicitly explain the rationale behind selecting specific timepoints for cell collection after the addition of the fresh medium.
• In Figure 1, authors conclude that MTCH2 ablation stimulates oxidative metabolism and ATP production to fulfill increased cellular ATP demands. However, this conclusion is based only on metabolomic analyses of the ADP/ATP ratio. To comprehensively assess the impact on cellular respiration, the authors should monitor the Oxygen Consumption Rate (OCR) and report the Respiratory Control Ratio (RCR).
• NAD+/NADH ratio: authors should measure NADH levels in both mitochondria and cytosol. This can be accomplished through NADH autofluorescence (recommended) or commercially available kits. This additional analysis would contribute to a more comprehensive interpretation of the observed changes in oxidative metabolism. They should also include measurement of mitochondrial membrane potential using TMRM. Suggested experiment: measuring NADH autofluorescence. The autofluorescence of mitochondrial NADH can be distinguished from cytosolic NADH by optimizing substrate consumption followed by the complete inhibition of electron feeding to the ETC. The redox state of NADH reflects the equilibrium between mitochondrial ETC activity and the rate of substrate supply. After acquiring basal autofluorescence levels through live imaging, max signal is obtained by stimulating maximal respiration (FCCP), and min signal is obtained by inhibiting respiration (NaCN or Rot+AA). Subsequently, "NADH redox indexes" are generated by expressing the basal NADH levels as a percentage of the difference between the oxidized and reduced signals. Furthermore, by examining the fluorescence signal increase after NaCN addition, the rate of NADH production can be monitored. This rate serves as a proxy of TCA efficiency.
• Authors observe a reduction in the levels of various amino acids and TCA cycle intermediates, indicative of an increased flux through the TCA cycle. This proposition could be further supported by measuring the kinetics of NADH autofluorescence. Additionally, a decrease in metabolites associated with the urea cycle, such as citrulline and ornithine, is observed, yet this observation remains uncommented and warrants discussion. Intriguingly, an elevation in Branched-Chain Amino Acids (BCAAs) and unsaturated acyl carnitines is noted, leading to the hypothesis of an increased transport and breakdown of fatty acids in the mitochondria to meet the heightened cellular demand for ATP in MTCH2 KO cells. To substantiate this, and to quantitatively measure mitochondrial fuel utilization in live cells, authors shall perform a Mitofuel Flex Test by measuring the Oxygen Consumption Rate (OCR) in cells treated with inhibitors of each mitochondrial oxidative pathway including etomoxir. This approach would enable the measurement of the dependency, capacity, and flexibility of cells concerning the pathway of interest in meeting ATP demand. It is also recommended to perform MitoStress test in cells supplemented with only one of the carbon sources (such as Glucose, Glutamine, Long chain and Short Chain Fatty acids).
• In Fig 3, a reduction in membrane lipids, free fatty acids, and non-esterified fatty acids is observed, while there is an increase in esterified fatty acids, storage lipids like Triacylglycerols (TAG) and Cholesterol Esters (CE), and lipid droplet number and size. Notably, these lipid droplets are positioned closer to mitochondria in MKO cells. The authors propose that MKO results in enhanced transfer and metabolism of lipid moieties at the mitochondria to generate ATP. To provide insights into the molecular mechanisms underlying the observed lipid changes in MTCH2 KO cells, the following experiments are recommended: Employ Western blot and real-time PCR to measure the levels of enzymes crucial in TAG and CE formation and accumulation (e.g., Long-chain acyl-CoA synthetase (Acsl), Stearoyl-CoA desaturase (SCD) or others). Evaluate the enzymatic activity of these identified enzymes to understand their functional role in lipid metabolism in MTCH2 KO cells.
• The suggested experiments are realistic in terms of time and resources, ensuring practical feasibility.
• The data and methods are presented in a clear and reproducible manner.
• The experiments appear adequately replicated, and the statistical analysis seems OK.

Minor comments:

• There are no specific experimental issues that require addressing.
• Prior studies are appropriately referenced
• In general, both the text and figures are clear and accurate. The significant alteration of metabolites found in their metabolomic dataset should be plotted using the online tool MetaboAnalyst to analyze metabolic pathways and generate better visualizations.
• Overall, the presentation is satisfactory with only minor language adjustments recommended. A minor suggestion for improvement involves refining the language used in the text. Instead of consistently using the term "produce energy," please use "conversion of energy".

Significance

General Assessment: The study, through the integration of metabolomic and lipidomic data in MTCH2 KO cells, provide a comprehensive overview of the metabolic rewiring of these cells. This metabolic change is particularly interesting in the context of adipogenesis, offering valuable insights into the interconnectedness of a mitochondrial solute carrier, cellular metabolism and adipogenesis.

Comparison and Advance: The current study significantly advances our understanding of the mitochondrial carrier homolog 2 (MTCH2) by uncovering its intricate roles in metabolism, and adipogenesis. While prior research identified MTCH2 as a regulator of apoptosis and mitochondrial dynamics, the present study expands our knowledge by elucidating its involvement in cellular metabolism and adipocyte differentiation. The major advance lies in the detailed exploration of MTCH2's impact on cellular metabolism through temporal metabolomic and lipidomic analyses. The study reveals that MTCH2 deletion leads to heightened ATP demand, an oxidized cellular environment, and alterations in lipid, amino acid, and carbohydrate metabolism. Additionally, the adaptive response in MTCH2 knockout cells involves a strategic decrease in membrane lipids and an increase in storage lipids. Furthermore, the study unveils a novel connection between the imbalance in energy metabolism triggered by MTCH2 deletion and the inhibition of adipocyte differentiation-a process that demands substantial energy and reductive biosynthetic activities. This mechanistic insight provides a conceptual advance, indicating how MTCH2, beyond its known role in apoptosis and mitochondrial dynamics, plays a pivotal role in orchestrating cellular metabolism and adipogenesis. Importantly, this work aligns with prior observations that hinted at MTCH2's involvement in fatty acid synthesis, storage, and use through his identified interactome. In summary, the study advances our knowledge of MTCH2 by providing a more comprehensive understanding of its roles in cellular metabolism and adipocyte differentiation, shedding new light on its multifaceted functions beyond its originally identified roles.

Audience: This research will appeal to a broad audience, ranging from specialists in cellular metabolism to those with a general interest in mitochondrial dynamics and biochemistry.

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Referee #1

Evidence, reproducibility and clarity

In the present study, Chourasia et al. describe the effects of MTCH2 deficiency on various metabolic parameters. Using temporal metabolomics in HeLa cells, they show an increase in ATP demand in cells lacking MTCH2. They also show altered lipid metabolism in NIH3T3L1 preadipocytes lacking MTCH2, associated with impaired maturation.

This study is mainly descriptive, containing large amount of information that would be of interest to the understanding of the role of MTCH2 in cell metabolism. The manuscript would benefit from thorough editing to make it more focused and accurate. This is challenging since there is a very large amount of data. Below are some suggestions, along with a couple of experiments that I suggest to add in order to clarify the mechanism through which MTCH2 acts.

Major Comments:

1. The ratio ADP/ATP as well as AMP/ATP as well as the decrease in TCA metabolites are indications of ATP demand. Nevertheless, these are not fluxes. It would therefore be worthy to complement these results with respirometry.
2. The dramatic increase in AMP/ATP ratio suggests an increase in AMPK activity. Testing it (by measuring AMPK phosphorylation or ACC phosphorylation) could further strengthen the results but it is not a must-have.
3. The cause of the increase in AMP in the NIH3T3L1 is not addressed. The involvement of acyl-CoA synthetase is worth discussing or investigating.
4. Fig. 2F shows MKO and WT, but it doesn't show MKO-R. This is an important control since lactate doesn't seem to be affected in the MKO-R.

Minor comments:

In the intro there are a few instances that could benefit from some more accuracy:

1. In the abstract there is no mention of the cells that are used.
2. Line 56: "...(OXPHOS) converts nutrients into adenosine triphosphate (ATP)". It would be more accurate to write that OXPHOS converts the chemical energy that is stored in nutrients into ATP.
3. Line 58: "The mitochondrial NAD+/NADH pool are substrates for OXPHOS". It would be more accurate to write that NADH is the substrate. (NAD+ is after all the product of oxidation)
4. Line 59-60: "Along with ADP, NAD+ also plays an important role in the regulation of the Krebs cycle". Instead of "regulation" I think it is more specific to write "stimulates" (otherwise add ATP and NADH which are also involved in regulation. 5. Line 65: "...changing metabolic states. In addition, mitochondria..." A link between the two sentences seems to be missing.
5. Figure 1 is a heavy figure. Some results are significant and some show only a tendency. The description (Lines 119-125) is too general. It addresses only the "trends". A bit more specificity as to the metabolites or ratios of metabolites and the time points that are significant would be in place.
6. Lines 136-139 "The metabolomics analyses revealed additional important changes in many more nutrient substrates, which included a decrease in most amino acids (Fig. 2A and Fig. S2A). Notably, the most significant change was seen in glutamine (Fig. 2A, left top graph), one of the major amino acid-nutrient sources" Glutamine is indeed an important amino acid and the effect is strong, but in this case it's increased. From the first sentence one would think it's decreased. Again, be more specific in your sentencing.
7. Lines 157-159: "Thus, the acyl carnitine profile suggests that 1- to 12-hrs post media change the MKO cells use BCAAs as a nutrient source, and later shift to unsaturated acyl carnitines, specifically to the C16:1 and C18:1 forms". This conclusion does not derive from the description by the result - address the difference between the different carnitines that occurs at different times.
8. Lines 167-168: "These results suggest that there is higher metabolism of acetyl CoA in the MKO cells leading to a bell-shape dynamics (low-high-low levels)." The interpretation is unclear. I understand that you mean that there is fluctuation within the group, however the acetyl-CoA levels remain lower MKO than in the control at all time points. This further suggests a decrease in TCA cycle.
9. Lines 172-173 addresses the bell shape of lactate, yet the most prominent result is the 3-fold increase in lactate levels compared to WT which is not mentioned. Unfortunately, the MKO-R shows a similar increase. Still, this should be addressed in the text.
10. 182-184: "Taken together, the results presented above are consistent with the idea that the increased amino acid/lipid/carbohydrate metabolism and substantial decrease of many metabolites in MKO cells is most likely due to their increased utilization to meet themincreased cellular energy demand." I'm not sure how this conclusion is reached. From metabolite levels alone, it's difficult to conclude about fluxes. Also, in a previous conclusion the authors wrote that the TCA cycle is probably reduced; this contradicts the above conclusion. If the authors mean that the FFAs and amino acids are used for anabolism and glucose for meeting energy demand, they should state so more clearly.
11. Figure 3A can be split into 2 or 3 subfigures. I think it would make it more comprehensible.
12. Line 210-211: "Notably, we also found that MTCH2 knockout cells showed accelerated mitochondria elongation (Fig. S3D, top panels), which was further pronounced when cells were grown in HBSS". The increase in mitochondrial elongation comes after fragmentation in MTCH2 KO. Although this is a known phenotype, it is good to address it shortly in the text.
13. Line 208-209: "LDs from dispersed to a highly clustered distribution that was often observed in close proximity to mitochondria..." The proximity of mitochondria to LD suggests the possibility that there is an increase in peridroplet-mitochondria, which have been shown to be involved in biogenesis LD. It might be interesting to investigate this path as an explanation to the observed phenotype.
14. Lines 244-245: "These results suggest that the MTCH2 knockout preadipocytes face a cellular energy crisis that is similar to the one seen in the MTCH2 knockout HeLa cells presented earlier" It's true that NAD+ and AMP (as well as AMP/ATP ratio) are increased but in view of the high ATP and NADH, it's difficult reach the conclusion that there's an energy crisis.
15. In the discussion- Lines 267-269: "Thus, MTCH2 might act like a "relay station" by sensing and connecting between metabolic intermediates/pathways and dynamic changes in mitochondria morphology/energy production by receiving and sending Wi-Fi signals." It's difficult to raise such specific hypothesis from the results. Use milder terms.

Significance

Great study

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Reply to the reviewers

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

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Referee #2

Evidence, reproducibility and clarity

Summary

This study highlights the role of the septin cytoskeleton in plasma membrane repair in HeLa cells perforated by the pore-forming toxin listeriolysin O (LLO). The authors performed a silencing RNA screen targeting protein-coding genes involved in endocytosis, exocytosis and intracellular trafficking. Besides the recovery of proteins that were previously identified to be part of the membrane repair machinery, they uncovered novel plasma membrane repair candidates, including septin 7 (SEPT7).

They found that upon LLO treatment, septins redistribute from actin stress fibers to the cell surface where they form knobs and loops together with F-actin, Myosin-IIA and Annexin A2 (ANXA2). Using super resolution microscopy and 3D reconstruction, they showed that these structures often protruding from the cell surface are formed by septins and F-actin that are organized in intertwined filaments associated with Annexin A2, and that they are functionally correlated with plasma membrane repair efficiency. Silencing SEPT7 further revealed that the remodeling of the repair protein ANXA2 at the cell surface is greatly decreased in LLO-injured cells, whereas the down regulation of ANXA2 had no impact on the arrangement of septins and F-actin into knobs and loops. Altogether, their results evidenced that the septin cytoskeleton triggers the organization of membrane domains containing the actomyosin cytoskeleton and ANXA2, that are essential for the repair to occur.

Major comments:

• The authors show that silencing SEPT6 or SEPT7, but not SEPT2 or SEPT9, perturbed plasma membrane repair of LLO-injured cells. The authors explain this result by indicating that the reduced expression of SEPT7 and SEPT6 (according to the siRNA), but not that of SEPT2 results in a reduced expression of septins from other groups. This could have been an explanation but, in Fig. S2B, downregulating SEPT2 clearly seem to impact the expression of SEPT6 and SEPT7 (except for siRNA#3) once normalized with the loading control tubulin. Moreover, it is well accepted in the literature and has been observed in many cell types, including HeLa cells, that knocking down a septin from one group (with sometimes the exception of septins of Group 3) induces the downregulation of septins of the other groups, and that it consistently results in the loss of septin filaments. Therefore, the fact that silencing SEPT2 does not perturb plasma membrane repair is quite surprising. This could suggest that SEPT6 and SEPT7, independently of their filament organization, play a role in membrane repair after LLO treatment. Nevertheless, the SEPT2 staining to study the fate of septin filaments following LLO exposure indicated that it is the redistribution of septin filaments that is crucial in this repair process. Interestingly, BORG proteins which are involved in the association of septin filaments to the actin cytoskeleton in interphase cells bind to the SEPT6/SEPT7 coiled-coil region of septin polymers. Could these proteins be involved, knowing that they are Cdc42 effector proteins, and that links exist between Cdc42 activation and Ca2+ entry? OPTIONAL: silencing BORG proteins (BORG2 for example) and studying septin and F-actin remodeling following LLO exposure could help the authors to understand the reason of such a redistribution.
• What about the terms "knob" and "loop": Are they structurally related to the "specks" described in other papers? Or are they new structures that no one observed before? Nobody has never looked at septins in this repair process before, but actin has long been described to be involved.
• It seems that knobs are formed before loops take over. This would deserve further investigation. Is that a reality? Or are they two independent structures? OPTIONAL: it would be interesting to do time-lapse video microscopy to follow the fate of a knob. Related to the previous point: why to show 3 sets of images in the LLO condition in Fig. 2A? Does the top b-panel represent the knob stage? Where there are still many stress fibers indicating that septins have not yet fully redistributed? And when septins are fully dissociated from actin cables, which are then lost, loops are forming (middle c-panel) and then increase in size (bottom d-panel)?
• Even though, some information is given in the discussion section, it would be helpful to mention in the introduction section the different pathways that cells activate to repair plasma membrane defects, and to precise which one(s) has(ve) already been described in the literature to be switched on in response to the LLO toxin.
• Some experiments are not rigorous enough: Sometimes, they have not been repeated, as exemplified in Fig. 7B. Count less cells but repeat the experiment at least three times. Sometimes, one condition is missing, as in Fig. 6C. Where is the DMSO condition? What about the statistics? Fig. 6A: In the calcium free condition, it seems that the two cells that are illustrated depict a telophase. The subcellular organization is obviously different at the end of cell division. Show only one interphase cell as in the top panels. Fig. 6B and C: It is mentioned in the figure legend: "Cells were treated as indicated in (A) and (D)". But the "C" condition is not mentioned anywhere: Does "C" stand for no DMSO or FCF treatment, in the presence of calcium, but under LLO treatment? Likewise, it would be very helpful to indicate in each figure panel whether cells have been treated with LLO or FCF. Please help the reader. Fig. 7A: Whatever SEPT7 is expressed or downregulated, the actin stress fibers are still present. If these cells were not well transfected, replace the images.
• Concerning the FCF experiments: The FCF cytokinin has been used by many authors to perturb septin dynamics. It induces the stabilization of septin polymers, thus promoting the formation of thick ectopic fibers. It is a potent inducer of septin polymerization and acts as a stabilizer. Fig. 6D: In the Ctr condition, a DMSO condition is needed to visualize the impact of FCF on septin filaments. Does FCF stabilize septins and induce the formation of thick filaments? The SEPT2 image in the FCF condition without LLO is of bad quality (see above remark). Also in Fig. 6D (FCF condition without LLO), the F-actin staining revealed that there are no stress fibers!!??? Usually, the more septins are associated with actin, the thicker stress fibers you get, since septins stabilize actin cables. FCF treatment often induces thick ectopic septin filaments that are not associated with stress fibers (which are therefore lost). Was it the case in all FCF-treated cells? Does FCF treatment really mimic what happens physiologically in the cell? Many off-target effects have been observed with this molecule in non-plant cells.
• The image quality in Figs 3A and B, and 6A and D needs to be improved regarding the septin staining. In control conditions, septin filaments cannot be clearly distinguished.
• Fig. 3B: It seems that ANXA2 is overexpressed in LLO-injured cells. Its accumulation level between both conditions should be compared by immunoblot. ANXA2 is indeed recovered on loops, but it is difficult to consider whether it is a redistribution.
• Fig. 7D: Compared to the control condition (we have to refer to Fig. S5D), ANXA2 again seems to be overexpressed under LLO treatment. To affirm that ANXA2 remodeling in LLO-injured cells requires the formation of septin/F-actin knobs and loops, data in Fig. 7D must be quantified.
• Fig. 6 (B-D): In panel B, there is a significant difference between the "C" and "FCF" conditions regarding the number of knobs + loops per cell. Where are the images corresponding to the "C" condition?

Minor comments:

• Fig. 2A: Report the white squares (selected enlarged areas) in all panels (SEPT2 and overlay). In panels b, do not place an arrowhead where we are supposed to observe an enlarged area. Also, from panels b, it would be worth showing an enlarged area including a knob. Show enlarged areas also from panels d.
• Fig. 3B'i: Septins are not on stress fibers. Select a transfected cell where septins still coalign with actin fibers, not a cell that was impaired by the transfection.
• Fig. 3C: Add the time point "0min". What was the % of colocalization before LLO treatment? and in DMSO condition? What about ALIX at 5 and 10min? Again, it's only one experiment.
• Figs 4 and 5: Very nice images but obtained following FCF exposure. Hopefully FCF would not have induced an aberrant organization!
• The "Ctr" abbreviation is often used, in different conditions, and may be confusing. Precise in the figure (not in the figure legend) whether it is siRNA ("Ctr siRNA"). Mention "DMSO" for the controls of your drugs (like in Figs S4 and S5).
• Fig. S4C: How is this figure different or does it provide additional information compared to Fig. 2C?
• Fig. S5D: It is hard to know that the ANXA2 siRNA worked, since no difference of staining between the Ctr and the transfected cells can be observed. Were these cells really transfected? It would have been helpful to use fluorescent siRNAs. The same applies to Fig. S5C: Silencing SEPT7 supposedly greatly reduces the level of expression of all septins. The SEPT2 staining is still high, and many actin stress fibers are still observable (whereas the loss of septin filaments results in the loss of actin stress fibers, as observed by many authors, including in HeLa cells). Same remark for Fig. S6, regarding the SEPT7 silencing in the Ctr condition (no LLO). No impact on stress fibers! Are these cells transfected? The authors themselves mention that sometimes cells are less effectively silenced (like in Fig. 7A, B). Why not to show cells effectively silenced!!
• In the abstract, it is specified that SEPT7 also plays a role in membrane repair after mechanical wounding. Based only on one type of experiment (SEPT7 silencing, Fig. 1H), this statement should only be mentioned in the text or used to discuss the putative repair mechanisms that septins are involved in, but not stated in the abstract as a main conclusion.

Significance

Strengths:

Despite septins have been involved in endocytosis, exocytosis, membrane protrusions, cell junction integrity or actomyosin constriction at cytokinesis, the involvement of the septin cytoskeleton in the plasma membrane repair machinery has, to my knowledge, never been reported before. The authors not only showed that septins are present in specific membrane protrusions (knobs and loops) but also evidenced that septin filaments trigger the formation of these plasma membrane repair domains by recruiting F-actin and ANXA2, essential for the repair to occur. The novelty of this study has therefore to be acknowledged, and these data will benefit the scientific community, and the septin community in particular.

This is a descriptive paper that nevertheless clearly shows, by different means, the reorganization of the septin cytoskeleton in LLO-injured cells. The use of high-resolution microscopy coupled to 3D reconstruction which enables to easily appreciate the organization of septins, F-actin and ANXA2 in the knobs and loops is a true strength of the paper.

Limitations:

The authors mention in the abstract that septins act as scaffolds to recruit contractile actin fibers and ANXA2. Biochemical experiments such as co-immunoprecipitations could strengthen this notion. The molecular mechanism by which septins are involved in this repair process has not been addressed at all in the paper. Even though the silencing RNA screen highlighted several proteins involved in known membrane repair mechanisms, the authors just presented a few data concerning ALIX, a component of the ESCRT-III machinery. A % of colocalization of SEPT2 and SEPT7 with ALIX is reported in Fig. 3C but this experiment has only been done once (n=1) and only following 15-min exposure to LLO. Is that too late? Immunofluorescence images of SEPT2 and ALIX with or without LLO (15min) are also provided in Fig. S5A but no quantification is reported. Is it sufficient to say that the ESCRT machinery is not involved?

My field of expertise:

Cytoskeleton, Septin, Actin, Microtubule, Signaling pathways

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Referee #1

Evidence, reproducibility and clarity

Review of "The septin cytoskeleton is required for plasma membrane repair" by Prislusky et al.

Eukaryotic cells rapidly repair damage to their plasma membrane and underlying cortical cytoskeleton. Such repair is increasingly recognized as being of major importance to human health (PMID: 33849525). Two broadly conserved cell damage responses have been described: a very rapid membrane resealing response which commences within a second or so following damage, and a cortical cytoskeletal response which commences within ~15-30s and which is based on activation of the Rho GTPases. However, our understanding of either of these responses is extremely limited, a situation which has engendered considerable debate about not only the mechanistic bases of these responses but also their relative roles and the extent to which they may be interdependent.

In the current study, the authors use an siRNA screen to identify Septin7 (hereinafter SEPT7) as a critical participant in the cell repair response. They further demonstrate that cell damage, as induced either by bacterial pore-forming proteins or by mechanical abrasion results in accumumulation of septins (including SEPT7) in curious ring-like structures associated at the plasma membranes; these structures are often associated with plasma membrane protrusions, which are a common feature of damaged cells. Additionally, the authors show that the septins colocalize with F-actin, myosin-2 (an F-actin-based motor protein) and annexin-2A, a protein previously implicated in cell repair. Lastly, the authors show that depletion of septins reduces the recruitment of annexin-2A to the plasma membrane in wounded cells, implying that the septins are upstream of the annexin in the wound response.

This is an exciting study that is also very well-documented. The excitement is provided by the following observations: first, septins have not previously been implicated in cell repair; second, the association of the septins with F-actin and myosin-2 in ring-like structures at the plasma membrane is suggestive of the possibility that local contraction may promote healing, a long-standing idea derived from studies of frog oocyte healing (PMID: 10359696; PMID: 11502762) which has proven controversial for healing of other cell types (see below); third, a link between septins and annexins in cell repair or, for that matter, any other process, is novel. With respect to the support for their claims, the authors go above and beyond to make their case-every point is supported by multiple approaches-for example the importance of septins is shown via siRNA, shRNA, and inducible depletion-and the imaging is very, very nice.

The potential role for actomyosin-powered contraction in healing of wounds made in cultured mammalian cells has been largely discounted because of studies wherein cells are wounded after pharmacological treatment with actin poisons have shown that healing is actually improved. The problem with such studies, is that depolymerization of actin prior to cell damage will dramatically alter the response to damage due to loss of cortical tension (PMID: 19846787). Thus, besides being important in its own right, the current study opens new doors for experimental assessment of the possible roles for cortical actomyosin in cell repair.

I have only minor concerns or questions:

1. What is the spatial relationship between the septin rings and actual damage sites? This could be addressed by wounding in the presence of a lysine fixable dextran.
2. The information in table 1 could be made more reader-friendly. In particular, it is not clear how the authors are getting their gene/protein names for their hits and what they correspond to. This was most noticeable for IQSEC1, ABI1, and GBF1 which the authors describe in the text as "genes that control the actin cytoskeleton" but in the table are listed as "Signaling proteins". I may have the abbreviations wrong (which is more reason for additional clarity) but GBF1 is the abbreviation for a protein involved in intracellular trafficking; IQSEC1 is a GEF for Arf proteins, and ABI1 is best known as a subunit of the WAVE complex.
3. The statement that begins the abstract "Mammalian cells are frequently exposted to mechanical and biochemical stresses..." could just as easily be "Eukaryotic cells..." or even "Cells..." as the membrane repair response is apparently universal and, indeed, was first described in nonmammalian cells. Similarly, the introduction begins "The plasma membrane of mammalian cells forms a biophysical barrier that separates the cell from its external environment". As far as I know, this is not a specific feature of mammalian plasma membranes but rather all plasma membranes. I don't know if it is the author's intention to imply their work is only relevant to mammals, but that is certainly not the case and they end up reducing the impact of their work by making it sound like cell repair is a phenomenon specific to mammalian cells.
4. The word "subplasmalemmal" is likely to be confusing for those who are not aware that plasmalemma is an antiquated term for the plasma membrane. It might be easier for the reader if the authors refer to "subdomains of the plasma membrane".

Significance

This is an exciting study that is also very well-documented. The excitement is provided by the following observations: first, septins have not previously been implicated in cell repair; second, the association of the septins with F-actin and myosin-2 in ring-like structures at the plasma membrane is suggestive of the possibility that local contraction may promote healing, a long-standing idea derived from studies of frog oocyte healing (PMID: 10359696; PMID: 11502762) which has proven controversial for healing of other cell types (see below); third, a link between septins and annexins in cell repair or, for that matter, any other process, is novel. With respect to the support for their claims, the authors go above and beyond to make their case-every point is supported by multiple approaches-for example the importance of septins is shown via siRNA, shRNA, and inducible depletion-and the imaging is very, very nice.

The potential role for actomyosin-powered contraction in healing of wounds made in cultured mammalian cells has been largely discounted because of studies wherein cells are wounded after pharmacological treatment with actin poisons have shown that healing is actually improved. The problem with such studies, is that depolymerization of actin prior to cell damage will dramatically alter the response to damage due to loss of cortical tension (PMID: 19846787). Thus, besides being important in its own right, the current study opens new doors for experimental assessment of the possible roles for cortical actomyosin in cell repair.

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Reply to the reviewers

General Statements

We are grateful to the reviewers for reviewing our manuscript. In general, the reviewers agree that our method presents a new approach of Nanopore direct RNA-seq that is not limited to the standard use of only the adenylated fraction of RNAs within a sample but they have also requested more evidence about the effectiveness and usefulness of this approach. Reviewer 1 notes that NERD-seq "extends nanopore direct RNA-Sequencing to beyond the poly(A) fraction." Reviewer 2 notes that "This manuscript has the potential of having major significance to researchers in the field of transcriptomics". At the same time Reviewer 1 remarks that, "the authors need to expand more on why this is useful, and what scenarios this would be used in" and need "to demonstrate that NERD-Seq is more than an incremental improvement to existing approaches". Reviewer 2 notes that "This technique has great potential, as ONT direct RNA sequencing can be used to detect RNA modifications... There are however some issues that need to be addressed before the manuscript is suitable to publication" and agrees with Reviewer 1 that the authors need to demonstrate "that their newly sequencing techniques could indeed improve RNA detection beyond the current techniques." We are grateful to the reviewers for these comments, and we fully agree that the manuscript in its initially submitted form falls "short from providing strong arguments supporting the fidelity, accuracy and coverage of the new technique." and that more "proof of the increased accuracy or utility of the new technique" was needed.

We attach a substantially revised and expanded version of the manuscript that includes additional data needed to ensure the methodology is replicable and further supports the rationale why NERD-seq is a useful addition to the current direct RNA sequencing methodology repertoire. We now provide:

• the repetition of all performed NERD-seq runs with a new enzyme (commercially available), as the one used in our initial study (Omniamp polymerase) is not anymore commercially available

• 6 revised main figure panels based on the new sequencing runs and a new main figure (Fig.7),

• 20 new supplementary figures, and

• 1 new supplementary table (Suppl. Tables 1),

that correspond to the points raised by the reviewers. We have also revised the main text accordingly.

Please find below the reviewers 'comments and a detailed point by point response to these comments. A document with the changes from the initially submitted manuscript being highlighted is attached at the end of this response.

Point-by-point description of the revisions

Reviewer 1

*------------------------------------------------------------------------------ *

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

• *

***Summary:** *

• *

This reviewer generally remarks that: "Saville et al detail a new method, NERD-Seq, which extends nanopore direct RNA-Sequencing to beyond the poly(A) fraction. In principle, this allows the capture of additional RNA types in a single sequencing reaction, albeit at the expense of sequencing depth. However, the authors need to expand more on why this is useful, and what scenarios this would be used in. The rationale for many of their experimental choices are not explained/contextualized appropriately. The manuscript also suffers from excessive jargon and grammatical errors."

• *

We appreciate these comments made by the reviewer. We now expand more on why and how NERD-seq is useful, and what scenarios this could be used in. In particular:

In the introduction, we now denote that a significant number of the most well described RNA modification positions are located in classes of RNAs such as tRNAs, snoRNAs and other ncRNAs like 7SK RNA. In the results section, we build on the second reviewer's suggestion that "This technique has great potential, as ONT direct RNA sequencing can be used to detect RNA modifications...", and we first show in revised Figures 3-5 that the standard approach misses the above classes of RNAs. Subsequently, in two new figures (Fig. 7 and Suppl.Fig. S23) we present an example of the ability of NERD-seq to decipher known RNA modifications in a well-studied ncRNA, 7SK, compared with the inability of the standard approach to do so. Widely studied RNAs such as 7SK have the potential and thus often serve as controls for known positions of certain RNA modifications when validating them for novel positions in other RNAs. This however means that the application of the standard approach, which is not able to detect RNAs and thus their modifications for RNAs such as 7SK, makes it difficult to use them as controls. In other words, the ability to perform genome wide studies of RNA modifications using the direct RNA-seq approach relies on the ability to be able to confirm at the same time these findings in already known control positions located in the above classes of RNAs. If these known controls such as short ncRNAs are missing, as we show that it is the case with standard RNA-seq, it is difficult to perform such genome wide epitranscriptome studies. Thus, the usefulness of our approach is not only that it can sequence certain classes of shorter RNAs beyond mRNAs, but that it can do this without affecting the ability to study mRNAs simultaneously or use targeted sequencing adapters. This is now discussed in the text. We have also tried to avoid the excessive use of jargon language and correct any grammatical errors.

*------------------------------------------------------------------------------ *

***Major comments:** *

• *

Point 1. The reviewer mentions:* "To my understanding, the primary purpose of NERD-Seq is to allow the sequencing of the non-adenylated fraction of RNAs within sample with a size filter step designed to exclude ncRNAs larger than ~200 nt. While this allow for subsequent polyadenylation of the small fraction, it remains quite likely that larger non-adenylated non-rRNAs are being missed by the protocol. It is also not clear why NERD-Seq should be considered the optimal strategy. The authors should show that they have considered/evaluated other strategies such as: *

*- Depletion/Seperation of the poly(A) fraction prior to size selection performed on non-adenylated fraction. *

- Targeted degradation of the rRNA fraction using rRNA depletion kits."

• *

We thank the reviewer for this comment. The primary purpose of NERD-seq is not only to allow the sequencing of the non-adenylated fraction of shorter RNAs but to do this while maintaining the ability to sequence longer polyadenylated RNAs. In particular, we are not sequencing only the short RNA fraction but also the longer RNA fraction of naturally polyadenylated RNAs. This includes both mRNAs and ncRNAs that are polyadenylated. We apologize that this may have not be presented clearly in our initial text, and we have now revised the respective results part (page 8, lines 13-14 and 30-31). As mentioned below, we now also provide evidence that our approach does not affect the ability to efficiently sequence mRNAs and decipher effectively their isoforms (new Suppl. Fig. S19). Only large non poly-A ncRNAs still evade our detection. Now, we discuss this limitation in the last paragraph of the discussion section (page 19, lines 12-20). We have now also evaluated other strategies such as those mentioned by the reviewer (depletion of rRNA, size selection using magnetic beads, different enzymes) and in the new Suppl. Figure S5 we show that they were suboptimal in providing sufficient reads that pass the quality thresholds in base calling compared to our NERD-seq approach.

• *

To sum up, we certainly don't claim to be able to capture longer ncRNAs, due to their lack of polyadenylated tails. We show though that while the ability to capture simultaneously all reads under the current Nanopore sequencing protocols may be unattainable, the NERD-seq methodology demonstrates a useful addition to the Nanopore sequencing repertoire due to its ability, in addition to polyadenylated transcripts, to simultaneously capture multiple classes of short ncRNAs, hitherto until now only achievable one transcript at a time with custom adaptor ligation.

Point 2. The reviewer mentions that "Related to this, the authors note that NERD-Seq is designed to allow the sequencing of both adenylated and (short) non-adenylated fractions of RNAs within a study. What is the actual value of this versus, say, simply targeting the short non-adenylated fraction directly? "

Please see our response to the general comment by this reviewer and the new figures Fig. 7 and Suppl. Fig. S23 and the completely new results section at pages 15 and 16 about examples on how NERD-seq expands the study of epitranscriptomic signatures to additional RNA classes while maintaining the ability to efficiently assess the protein coding transcriptome (new Suppl. Fig. S19).

Point 3. The reviewer notes that "The manuscript in general is written in a somewhat subversive style, seemingly focused on highlighting the 'failings' of the standard ONT protocol. This is somewhat disingenuous as these are not 'failings' per se given the design objective of the standard DRS protocol (i.e. to capture and sequence the poly(A) fraction of RNAs) works well. The authors would be better off highlighting the situations (i.e. study questions) where NERD-Seq would provide a measurable benefit over the standard DRS strategy. "

• *

We apologize if this was indicated in our initial submission, as this was not our intention. We now focus on highlighting what NERD-seq can do, and this is reflected in the changes we have made in the introduction and discussion section.

Point 4. The reviewer asks "The authors state that 1.5ug total RNA is used as input for NERD-Seq but how much input (poly-A RNA) actually goes into the short- and long-fraction parts of the DRS protocol? This is important to know. "

We have now included data in the manuscript for polyadenylation signals in the reads themselves (new Suppl. Fig S5F) and view it as a useful addition to the manuscript as it seems to show there is little difference in the relationship of length of transcript and polyadenylation tail length between the two methods.

RNA RIN values differ across samples so within different samples the portions of poly-A RNA, non poly-A RNA and former poly-A RNA that has lost the poly-A due to degradation may also vary. This however has not been shown to affect the reproducibility of the standard direct RNA-seq methodology, so it should not affect also that of NERD-seq. Nevertheless, we searched the literature for a well characterized methodology for quantifying this further and found little on poly(A) specific quantification approaches that we could use. In fact, poly(A) selection has also been shown to have variable efficiency and could thus produce inaccurate measurements that would make it difficult for us to assess explicitly the exact portions of poly-A vs non poly-A portions. Thus, we feel that in the absence of a well characterized methodology to make these quantifications, developing a new one may have been beyond the scope of this manuscript.

Point 5. The reviewer recommends: "The authors show that NERD-Seq performs well on a tissue that is generally enriched in non-coding RNA activity but without the inclusion of biology replicates or tissue samples from other sources, it is impossible to assess (1) the reproducibility/robustness of the methodology and (2) whether NERD-Seq would produce useable data from other tissues with lower non-coding RNA activity. These experiments are required. "

• *

We thank the reviewer for this suggestion and we have now included an additional biological replicate for the mouse tissue and data from another tissue in a separate organism (5-person pool source human cerebral cortex RNA).

Point 6. The reviewer notes: "Several figures are poorly explained. For instance, Does Figure 2A show data only from the short RNA fraction? If not then this suggests incredibly high levels of mRNA degradation in the 'standard' ONT fraction - far beyond what is seen in other studies. The legends for all figures should be far more specific and detailed."

• *

We have now replaced figure 2A with a different mapping strategy and a whole sample assessment of mapped reads lengths. We have also edited the figure legends to include more information.

The reviewer made also the following comments:

Minor comments:

• *

": Please refrain from using 'next-generation' in a sequencing context (abstract, introduction). Having a 'new' next-generation sequencing is confusing in regard to the old 'next generation' sequencing. "

• *

The instances mentioned have been removed as per the reviewer's suggestion.

"Introduction should acknowledge that targeted sequencing of (individual) non-adenylated RNAs is possible (i.e. there is an ONT protocol for this)."

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We now include mention of this in the introduction, results and discussion.

"Several figure elements not referenced in the text appropriately (e.g. red bars in Figure 2A). "

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We have now addressed this and thank the reviewer for making us aware of this.

"The authors mention profiling of the epitranscriptome several times in the introduction and discussion but do not include any work geared toward looking for RNA modifications. Indeed it is entirely unclear whether NERD-Seq produces the depth of sequencing (on non-adenylated RNAs) required for current RNA modification detection tools. "

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We have now included a new main figure (Fig. 7) and a new supplementary figure (Suppl. Fig. S23) which profile elements of the epitranscriptome and show that indeed NERD-seq produces the depth of sequencing necessary for RNA modification detection.

Reviewer 1's summary:

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"NERD-Seq presents a modified method for DRS of both short non-adenylated and the standard adenylated fraction of RNAs within a sample. This utility of this approach appears rather niche and it is hard to determine situations in which this approach would be generally useful versus many of the existing (Illumina-based) approaches. The burden to demonstrate that NERD-Seq is more than an incremental improvement to existing approaches lies with the authors. "

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We appreciate the reviewer's comments. While we agree with them that for various applications (such as differential gene expression, quantification of lowly expressed genes) "the existing (Illumina-based) approaches" Illumina RNA-seq or short-RNA-seq would be more appropriate due to higher sequence yields, the main advantage of nanopore direct RNA-seq is the ability to identify RNA modifications directly at the same time (see new Figs 7 and S23). While we also agree that the field of high throughput sequencing epitranscriptomics is quite nascent, it is quickly gaining interest. Based on the reviewer's suggestions we believe that we have now modified the manuscript substantially to provide justification for NERD-seq's feasibility as a methodology to capture multiple classes of ncRNAs for the study of their sequence, quantity and their epitranscriptomic signatures.

We would also like to note that even as a BioRxiv preprint, our manuscript has received already a number of citations, including from an article published in Nature Biotechnology and feel this demonstrates interest in NERD-seq from the scientific community.

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Reviewer 2

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

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This reviewer generally remarks that "In this manuscript Saville et al. present NERD-seq, a novel method to enrich and directly sequence non-coding RNA using the Oxford Nanopore Technology (ONT). The technique is based on the addition of a poly-A tail to small non-coding RNAs which enables their sequencing by a conventional ONT direct RNA-seq protocol using a poly(T)-tethering adaptor. This technique has great potential, as ONT direct RNA sequencing can be used to detect RNA modifications. Furthermore, non-coding RNAs are known to harbor a lot of these modifications and that they are important to their function. In addition, non-coding RNAs aren't generally poly-adenylated and therefore are underrepresented when using standard ONT direct RNA-seq. The authors have shown that using NERD-seq, they are able to significantly improve the number of reads on several subsets of non-coding RNAs : tRNAs, snoRNAs, snRNAs, scRNAs and rRFs. There are however some issues that need to be addressed before the manuscript is suitable to publication."

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We thank the reviewer for their encouraging comments.

Major comments:

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Point 1. The reviewer recommends that "Data on RNA modifications present in the sequenced non-coding RNA would greatly improve the impact of the manuscript, as the method is presented as read tool to study RNA modifications. If the authors can't include these data, they should at least explain why in the discussion section."

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We have now included a new main figure (Fig.7) and a supplemental figure (Suppl. Fig. S23) which show the ability of NERD-seq to identify previously described RNA modifications and its superiority in the case of non-coding RNAs such as 7SK. We thank the reviewer for this recommendation that significantly improved our manuscript better revealing the rationale and impact of our approach.

Point 2. The reviewer remarks that "The authors did not discuss possible biases of their method. For example, is the poly-A tail ligation efficiency affected by sequence and or structural differences between RNA? Is there detectable differences in the efficiency of sequencing small RNA with structured 3'end when compared to mRNA? Are the proportions of reads obtained per non-coding RNA sub-category and RNA rank supported by other biochemical data (e.g. Northern blots, primer extension, RT-qPCR? "

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We have included commentary in the discussion on these biases (page 19, lines 7-11). We also include a new supplementary figure (Suppl. Fig. S5F) regarding polyadenylation in which we see similar transcript length to polyadenylation tail length dynamics between the two methodologies.

Point 3. The reviewer notes that "It is essential to include external size and sequence markers spike-in to directly evaluate the quality and fidelity of the newly develop sequencing technique. "

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We have now repeated the sequencing, including sequencing with the well described RNA sequins mix B. We include a new supplementary figure with this data (Suppl. Fig. S10) that shows that NERD-seq does not differ from the standard approach regarding its ability to effectively evaluate the quantity and complexity of the transcripts present.

Point 4. The reviewer mentions that "The author compared NERD-seq to ONT standard direct RNA-seq but did not compare it with other methods that are currently used for non-coding RNA sequencing (e.g. Illumina based sequencing, TGIRTseq). There is a need for side by side comparison at least by using data available in the literature if not experimentally. "

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We now include a comparison with Illumina sequencing data for both long and short fractions from each biological replicate (Suppl.Figs S12-15,17,19 and 21). This data shows that NERD-seq combines the advantages of both standard and short RNA-seq with Illumina, enriching both long and short RNAs, while simultaneously as mentioned above, offering the benefits of direct RNA-seq. We feel this also demonstrates the utility of the unique chemistry of Nanopore sequencing where fragmenting of long RNAs is not required for sequencing, allowing the combination of long RNAs and short RNAs in the same library to reproduce what is essentially enriched in short RNA libraries as well as poly(A) sequencing libraries. Since the enzyme included in our initial submission is not anymore widely accessible, we also tested a series of other enzymes, including the commercial replacement for omniamp (the originally used enzyme), lavalamp, and other small tweaks to the library methodology, until finding the GSP SSD2.0 enzyme to be the most suitable for our research goals. The summary of our findings is in Figure S5. Initially, we considered TGIRT as a potential enzyme for the sequencing reaction because of its use for sequencing snoRNAs and other highly structured RNAs but because of its strand switching properties, we felt it would be poorly suited for a nanopore direct RNA sequencing approach.

The reviewer made also the following comments/suggestions:

Minor comments

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"Page 5 line 3, NERD-seq is misspelled. "

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This is now fixed.

"Throughout this section µL and µg are written as uL and ug."

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This is now fixed.

"Several temperatures are missing the o symbol between the number and C."

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This is now fixed.

Final comments:

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"This manuscript has the potential of having major significance to researchers in the field of transcriptomics if the author demonstrated that their newly sequencing techniques could indeed improve RNA detection beyond the current techniques. Unfortunately, the manuscript only show the capacity of the technique to detect non-coding RNA but fall short from providing strong arguments supporting the fidelity, accuracy and coverage of the new technique. The use of Nanopore sequencing is not unique and was used in the past for sequencing non-coding RNA. What is needed now is a proof of the increased accuracy or utility of the new technique to justify yet another publication about Nanopore sequencing paper. The manuscript would potentially be of interest to researcher working on different type of non-coding RNA and transcriptomics.* *

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I am in the field of non-coding RNA sequencing and functional analysis and very familiar with this approach."

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We thank the reviewer again for their encouraging comments and valid concerns. We agree that the initial manuscript fell short of providing evidence of its utility as an addition to the Nanopore sequencing repertoire. We hope the additional data we provide (rerunning with an additional enzyme, use of replicates, use of standard spike in controls, testing an additional organism and tissue, testing and comparing different enzymes and other sequencing platforms) provide the necessary assurances about reproducibility and accuracy, while the new data concerning identification of RNA modifications and detection of important RNA classes missed by the standard protocol provides the necessary assurances about the utility of our approach.