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Referee #3

Evidence, reproducibility and clarity

Summary:

In this paper, Hama et al look to address ongoing questions regarding the recruitment of core autophagy factors to protein aggregates during aggrephagy. Using cells that lack all known aggrephagy receptors (PentaKO HeLa cells) provides the authors with a 'blank canvas' with which to cleanly dissect a process otherwise fraught with mechanistic redundancy. By this approach, the authors isolate a previously unidentified mechanism by which TAX1BP1 recruits ATG9A vesicles to ubiquitin-positive aggregates. Using mass spectrometry, the authors identify SCAMP3 as a component of ATG9 vesicles that is responsible for recruiting the vesicles to cargo. Moreover, they provide additional mechanistic insight through the subsequent identification and mutagenesis of a putative interaction interface between TAX1BP1 and SCAMP3.

Major comments:

1. Statistics:
   • a) The description of the statistical methods is sparse. In the methods section, the authors' state that statistical methods are described in each figure legend. However, for most figures they were excluded.
   • b) Where statistics are discussed, Mann-Whitney was used. However, this appears to be the incorrect test in many cases. Per GraphPad (the author's preferred statistical package) "Use Mann-Whitney test only to compare two groups. To compare three or more groups, use the Kruskal-Wallis test followed by post tests. It is not appropriate to perform several Mann-Whitney (or t) tests, comparing two groups at a time."
2. Rigor and reproducibility - The authors report n=~30 cells in most experiments. However, it's unclear if these 30 cells represent more than a single experimental replicate. While the trends in the data are quite convincing, this a significant limitation of this study.
3. Puncta identification - it's unclear how the authors called puncta. The quantification of these images (i.e. the box and whiskers plots) makes compelling points that support the authors' interpretation. However, in many cases the authors are calling puncta amidst a fairly speckled image. How were puncta distinguished from speckles? When did something rise to the level of a puntum? If it was computationally called, please provide the methods and pipeline. If data were manually scored, then the lack of replicates rises to a more significant concern - would other investigators have scored the data similarly? Is it possible that the data were scored with implicit bias based on expected outcomes of the investigator? Where data scored in a blinded fashion?
4. Do the findings presented here have functional implications? While the data on recruitment of ATG9A to TAX1BP1 is clear, it's unclear whether the SCAMP3/TAX1BP1 interaction is functionally important for lysosomal delivery of cargo. In part, this is because the authors must work in autophagy-deficient cells (ATG9AKO or FIP200KO) to observed many of their effects. One way to address function might be to ask whether lysosomal delivery of TAX1BP1 is affected upon SCAMP3KO (e.g. in PentaKO cells to remove the effects of other receptors).

Minor comments:

1. The authors IP TAX1BP1CC1 and SCAMP3, but an IP between full length TAX1BP1 (WT and K248E) and SCAMP3 would more fully demonstrate the sufficiency of this binding site.
2. Optional: Is the TAX1BP1 and SCAMP3 interaction direct?. The data are suggestive, but this question is not fully resolved due to the in vivo nature of the assays. Formally, there could be an adapter that facilitates TAX1BP1/SCAMP3 interaction. This could be formalized by testing binding between purified soluble domains of SCAMP3 and TAX1BP1CC1.
3. Figure 4F - the y axis has a typographical error

Significance

This is a crisply written manuscript with a generally clean experimental approach. While there are many directions the authors could take this work in the future, the data largely stand on their own as a short, concise advance. The work adds to our current understanding of the regulation of ATG9A recruitment during selective autophagy, which is under-explored in comparison to starvation-induced autophagy. Mechanistic insights are provided in the form of a new interacting protein SCAMP3, which is present in ATG9A vesicles and is required for the recruitment of ATG9A vesicles to TAX1BP1. The data are predominantly convincing, albeit with significant caveats. Limited sample sizes and lack of functional effects (see 'major concerns') limit the impact of this work. However, the data have merit on their own. This is a specialized study that will be appreciated by those interested in selective autophagy and the mechanism of autophagosome formation.

Reviewer expertise: selective autophagy and autophagosome formation

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Referee #2

Evidence, reproducibility and clarity

Ubiquitin-binding adaptors are a group of autophagy adaptor proteins that facilitates the formation of isolating membrane around a specific substrate during selective autophagy. At least two ubiquitin-binding adaptors, NBR1 and OPTN, have previously been demonstrated to recruit ATG9-positive vesicles to ubiquitin-positive biomolecular condensates. It is postulated that this recruitment mediates the formation of the isolating membrane around the ubiquitinated biomolecular condensates. In this manuscript, the authors utilized the HeLa cells deficient in the expression of five ubiquitin-binding adaptors, p62, NBR1, OPTN, NDP52 and TAX1BP1, to show that expressing TAX1BP1 colocalizes with ATG9A. The authors interpreted this observation to suggest that TAX1BP1 can recruit ATG9A vesicles independent of other adaptors. Interestingly, the TAX1BP1 positive structures differ from that of OPTN and NBR1 because they do not contain ubiquitin, suggesting a difference in substrate specificity. They further show that TAX1BP1 differs from OPTN and NBR1 because ATG9 recruitment required SCAMP3 to recruit ATG9A. Based on these observations, the authors propose that TAX1BP1 recruits ATG9A via SCAMP3.

Major comments

• The work presented in this manuscript is of high quality, however, the reliance on a single experimental assay (colocalization microscopy studies) limits the relevance of its findings. The conclusions are based on colocalization studies in wild-type and CRISPR/cas9 knockout HeLa cell lines. Therefore, it is not certain that their findings are restricted to these PentaKO cell lines. Given that these adaptors are required for selective autophagy, the pentaKO cells may have adapted. Unfortunately, the current study lacks additional systems physiologically relevant models or systems. Such experiments are needed to validate their findings in the HeLa pentaKO cell. (Optional) Alternatively, identify the substrate(s) specific to the TAX1BP1-SCAMP3-ATG9A mediated autophagosome vs. that of NBR1 and/or OPTN in these cell lines.
• There are several issues with the immunofluorescence data throughout the manuscript. For example, in Figure 1C, the authors quantify 30 cells per condition and perform a Mann-Whitney test, presumably using each cell as a data point, as this is not specified in the legend. There are two problems with this approach, the first being there is only one indicated independent trial performed, and the second that treating each cell as a data point for statistical analysis overinflates the power. These experiments should instead be performed across at least 3 independent trials (especially given the wide range of values seen in some conditions such as Fig. 2b) with 30 cells counted per trial, and statistical analysis should be performed using the means from each trial. See Lord, S.J. et al. (JCB 2020, PMID: 32346721) for a detailed explanation. Further, how each statistical test is performed (using means vs. all points) and the number of independent trials conducted should be communicated in the figure captions. Finally, beyond Fig. 1, the statistical test used is not reported. If a Mann-Whitney test was used for all statistical analyses, this should be revisited as with two or more variables (cell type, treatment, etc.), this is not the appropriate test.

Minor Points

• The experimental design rationale is not clear throughout the manuscript. For example, why FIP200 KO cells are used in Fig. 3c and Fig. 4 is not apparent, and only in Fig. 6 (Lines 211-213) is it clearly stated. The authors should revisit the results section and ensure the experimental rationale is clearly explained.
• It is curious that condensates formed in muGFP-NDP52 and muGFP-TAX1BP1 cells lack ubiquitin (Fig. 3c). Is this image representative of most cells? if so it should be discussed.
• The authors are missing some relevant citations:
  • Lines 57-58, the authors may consider citing more recent literature (Olivas, T.J. et al., JCB 2023; Broadbent, D.G. et al., JCB 2023; Nguyen, A. et al., Mol Cell 2023) investigating ATG9 vesicles in autophagosome biogenesis.
  • In lines 58-66, the authors do not mention that NBR1 was also shown to bind FIP200 (Turco, E. et al., Nat Communications 2021, PMID: 34471133).
• Some minor changes are recommended for clarity:
  • In lines 106-110, the authors may consider explaining that "growing" conditions are cells grown in regular culture conditions, as it is a bit unclear whether these cells are treated with a drug, etc., to induce p62-condensate formation. Something as simple as "...p62-double-positive structures under normal culture conditions, hereafter referred to as growing conditions," would help the reader.
  • The general axis labelling of "Ubiquitin-positive rate of FIP200 puncta (%)" (Fig 1D) is confusing wording. The authors may consider changing to "% of ubiquitin-positive FIP200 puncta" for readability.
  • The axis title in Fig. 4F has a typo.
• Several figure legends include data interpretation, which should generally be excluded from figure legends. For example, the first line of Fig. 4B should be removed.
• The authors may consider how ATG9A is recruited to ubiquitin-independent selective autophagy cargoes that are degraded independently of NBR1, p62, OPTN, NDP52, and TAX1BP1 in their discussion.
• Supplementary figure S2-right side blot. For best practice in publications, I encourage the authors to provide a single blot of FIP200, ATG13, and ATG9A immunoblot for Penta KO and its KO derivatives. Presently, the blot appears to have been spliced together

Significance

Although different ubiquitin-binding adaptor proteins have been shown to have some substrate specificity, how they mediate the selective degradation of a substrate remains unclear. This manuscript provides evidence that TAX1BP1, like NBR1 and OPTN, can also recruit ATG9A positive structures independent of the autophagosome initiation complex ULK1-complex. However, they do show that the mechanism of ATG9A vesicles differs from the other two adaptors in that it requires SCAMP3, a membrane protein found in endosomes. The data provided by the authors are of high quality. However, the study relies on only one experimental system/assay, which limits the relevance of its findings and could benefit from testing these findings using additional systems and/or physiologically relevant models, as well as increasing the rigor of the quantitative analysis.

Besides these two major shortcomings, the finding is novel and adds to our current understanding of autophagy adaptor proteins. The difference in the mechanism of ATG9 vesicles compared to NBR1 and OPTN may contribute to the selective nature of these autophagy adaptors.

This manuscript is most appropriate for specialized basic researchers in the field of selective autophagy.

Our expertise is in selective autophagy regulation and substrate selectivity of selective autophagy.

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Referee #1

Evidence, reproducibility and clarity

Macroautophagy is a catabolic pathway for various intracellular components mediated by the formation of autophagosomes followed by lysosomal degradation. ATG9 vesicles provide the initial autophagosomal membrane source and thereby recruitment of ATG9 vesicles to the autophagosome formation sites serves as a critical step for autophagy induction. However, the precise molecular mechanism of the ATG9A recruitment is not fully understood. In this study, Hama et al. report two distinct pathways; ULK complex-dependent ATG9 vesicle recruitment during starvation-induced autophagy, and selective autophagy receptor TAX1BP1-dependent ATG9 vesicle trafficking through the binding to SCAMP3, which was identified as an ATG9 vesicle component by the authors. Unfortunately, the authors were unable to demonstrate the impact of the TAX1BP1-SCAMP3-ATG9 vesicle axis on cellular physiology, presumably due to the existence of compensatory mechanisms mediated by other selective autophagy receptors and ULK complex, which limits the impact of the findings presented. Having said that, the study is technically well executed and provides a new insight into the regulation of cargo/receptor-mediated ATG9 vesicle recruitment. This reviewer has a few comments that should be addressed to strengthen the authors' conclusions.

1. In the Co-IP experiments (Fig 5A-C), binding of TAX1BP1 to SCAMP3 is assessed by using the CC1 domain fraction of TAX1BP1, which may yield an artificial binding to SCAMP3. Could the authors confirm binding of full length TAX1BP1 wild-type and K248E mutant to SCAMP3?
2. In Fig 5D, the authors showed that SCAMP3 localises to immuno-isolated ATG9A-positive vesicles. Is it a direct interaction between the two proteins? Could the authors provide the evidence that the interaction is retained in the presence of a detergent by immunoprecipitation? If the interaction is indirect, can the authors discuss candidate proteins that mediate binding of SCAMP3 to ATG9 vesicles?
3. Related to the comment #2, it is interesting that the knockout of ATG9A does not affect SCAMP3-positive "ATG9 vesicle" formation. What is the nature of "ATG9 vesicles" lacking ATG9A?
4. Could the authors confirm that K284E mutation in TAX1BP1 abrogates the localisation of SCAMP3 to the TAX1BP1 condensates as in Fig 6E? This will reinforce the claim that TAX1BP1 binding to SCAMP3 facilitates ATG9 vesicle recruitment.
5. Could the authors discuss the potential reasons differentiating TAX1BP1 from other CC-domain containing autophagy receptor proteins (NDP52, OPTN and NBR1), which enables it to bind to SCAMP3. For instance, does TAX1BP1 have charged residues facing outwards in its CC domain that could be responsible for this specificity?
6. In Fig 3C and 6E, no colocalisation of TAX1BP1 and ubiquitin was observed in TAX1BP1 condensates. In the context of "cargo-driven recruitment" of ATG9 vesicles, what cellular component(s) could trigger TAX1BP1-mediated SCAMP3/ATG9 vesicle recruitment? In the Discussion, authors mentioned that ferritin-NCOA4 was not the target of the TAX1BP1-SCAMP3 axis. Could the authors test if any of the other known TAX1BP1 cargo proteins localise to TAX1BP1 condensates in Penta KO/FIP200 KO/muGFP-TAX1BP1 cells?

Minor:

1. Fig 4F: Typo in y axis.

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

The main finding of the study is a new pathway of ATG9 vesicle recruitment through the interaction of TAX1BP1 with SCAMP3, which provides a novel insight into molecular mechanisms of autophagosome biogenesis. However, the axis is implied to be redundant for functional autophagy in wild-type cells, and lack of data providing a biological function of the axis in cellular physiology will limit impact attracting broader readers outside of molecular mechanism of autophagy.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

Interaction between ATG9A and selective autophagy receptors OPTN and NBR1 has been reported (doi: 10.1083/jcb.201912144; 10.15252/embr.201948902). This study provides an additional mechanistic insight into the regulation of ATG9 vesicle recruitment through another autophagy receptor TAX1BP1 interacting with SCAMP3 which was newly identified as an ATG9 vesicle component in this study. Given the predominant functions of ATG9A in TNF cytotoxicity and plasma membrane integrity as well as TAX1BP1 in neuronal proteostasis and iron homeostasis (doi: 10.1126/science.add6967; 10.1038/s41556-021-00706-w; 10.1016/j.molcel.2020.10.041; 10.15252/embr.202154278), the interaction between TAX1BP1 and ATG9A would potentially have uncovered but important role in mammals. Autophagy-independent lysosomal degradation regulated via ULK component, ATG9 and TAX1BP1 might be related in this context (10.1016/j.celrep.2017.08.034).

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This study will be of interest to the basic researchers working on molecular and structural mechanisms of bulk and selective macroautophagy. Unfortunately, the lack of data demonstrating the relevance of the findings for cellular physiology will limit the impact on researchers in broader fields such as pathology and drug discovery.

Please 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.

Molecular cell biology of autophagy; neurodegenerative and lysosomal storage disorders.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The article describes a study on two effector nucleases, V2c and V2a, encoded by the T6SS cluster in Agrobacterium tumefaciens 1D1609. The study shows that V2c is a DNase belonging to the Tox-SHH clade of His-Me finger superfamily, exhibiting DNase activity in vivo and in vitro. The SHH and HNH motif of V2c were found to be involved in DNase activity. The study also demonstrates that V2c induces DNA degradation and cell elongation, which can be neutralized by its cognate immunity protein V3c. Furthermore, V2a, also exhibits DNase activity-dependent cell elongation phenotype. Both V2a and V2c nucleases function synergistically for antibacterial activity against Dickeya dadantii, resulting in elongated and lysed cells. The study suggests that 1D1609 uses V2a and V2c DNase effectors with synergistic antibacterial activity against Dickeya dadantii.

Major issues:

1. The cell elongation phenotype was an important focus of the paper and the authors did a solid job quantifying this phenotype. However, cell elongation does not seem to be associated with the mechanism of toxicity. Just a small part of the cells are elongated while you have more than one log of killing (Figure 5C and 5D).<br /> Many stresses can result in cell elongation, such as cell-wall targeting antibiotics. The signal narrows down to the very well-known mechanism of SulA activated by SOS response. There is no evidence "cell elongation independent of nuclease activity may represent a new mechanism of stress response #339". I strongly suggest the authors to use an SOS like pPrecA-gfp from ref 17 if they want to invest in the cell elongation phenotype. As it is, cell elongation is a distraction from the most exciting things in the manuscript. One potential hypothesis is that the catalytic mutants may bind DNA without cleaving, and while bound to the DNA, the mutants may interfere with DNA metabolism, replications, transcription, etc... This interference could create breaks in the DNA and cause cell wall elongation.
2. The manuscript does not have biological replicates in many experiments. At first glance, the tiny error bars in many graphs raised a red flag. It is very difficult, if not impossible, to have the date so tight when working with bacterial cultures. Many of these graphs have "independent experiments", but in Fig 5 the authors mention " 6 repeats from three independent experiments". My understanding is that the independent experiments are from the same cultures, which makes them technical and not biological replicates. The authors need to have replicates from independent cultures. I ask the authors to explain better what they mean by replicates and their rationale.

Minor issues:

1. Many figures have all the data with conditions with and without arabinose. This makes the figure very polluted and difficult to follow. I suggest the authors keep only the data from induced cultures and move the figures with all the data to supplement. This is a big issue with Fig 3
2. The entire "V2c V2a nucleases function synergistically for antibacterial activity against the soft rot phytopathogen, Dickeya dadantii" #212 section is difficult to follow because the name of the toxins are not in the name of the strains. The reader should be able to associate the toxin with the strain.
3. The in vitro essay #427 should have information about the amount of enzyme used.
4. The competition essay #474 method does not have enough information to allow reproducibility and must be expanded.
5. Figure 2B Y-axis needs one log increase between marks, and not two.

6. 256 is difficult to understand and not very scientific. DNses are potent because they target essential molecules, the same for lipases and muramidases. This is not related to the origin of life.

Significance

Strengths:

Data is clear about the toxicity and DNA degradation phenotypes The synergy of toxins is a very exciting topic; it helps to explain why some strains have redundant toxins

Weakness:

Cell elongation claims are not supported Replicates are inadequate Methods needs to be more specific

The manuscript provides incremental data about bacteria-to-bacteria toxins. The major finding of predicted nuclease acting as nuclease toxins is not particularly innovative. This work will benefit a smaller audience in the field of toxins.

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Referee #2

Evidence, reproducibility and clarity

Santos et al demonstrate the activity and confirm predictions of the mechanism of action of SHH nuclease toxin encoded in auxiliary T6SS cluster of Agrobacterium tumefaciens. Study includes demonstration of nuclease activity in vitro and its manifestation in vivo, mutational analysis of the predicted catalytic site, and assessment of its role in inter-bacterial competition using strains deleted for the T6SS effector(s).

Major comments: major issues affecting the conclusions

Lines 159 and further - I am not sure that large deletion as an entire region between residues 380-409 is a very healthy approach. Without showing that such protein can be produced and fold, it can be very risky to draw any conclusions. While expression of other mutants are shown in Figure 2D, this construct is not included. Also, it is not clear (starting from line 160) what is the utility of double catalytic mutant if single mutants are already inactive. Was there residual activity of single mutants after all?

Line 187 and Figure 3 - cell elongation of CR mutant and HAHA mutant seems to be independent of expression of the construct. It is therefore incorrect to write that "E. coli expressing ...", since theoretically it should not express anything in the absence of arabinose. Also, how do would authors interpret these findings? Again, at Line 211 - in the same paragraph authors say "V2c shows DNase activity-independent cell elongation" and then conclude "cell elongation phenotype may be specific to toxicity of nuclease effectors". These two phrases seem to contradict each other.

Line 272 on - authors speculate about dependency on the metals, which is a hallmark of the his-me finger nucleases. A simple test could have been adding the EDTA control to chelate the metal in the in vitro experiment such as one presented in figure 2D. (OPTIONAL)

Minor comments

Figure 1 - Auxiliary cluster with accession numbers, in addition to the domain composition of the toxin could be demonstrated. This would help the readers to identify which effector is studied and link it to other studies.

Line 127 and Figure 1 C and line 303 - the last option, named "FIX RhsA AHH HNH-like" seems to be a mix of multiple things, First, FIX domain is already included as a first option; AHH HNH-like corresponds to toxic domain (although it often ends up in annotation of the entire protein). All His-Me finger nucleases at some point were annotated as HNH-like and thus HNH, AHH, SHH, ... all belong to the same clade of nuclease domains; RhsA is probably a correct domain/protein detected here and to be represented here as a separate option. I would call it "Rhs", not RhsA, since RhsA,B,C,... is part of an historical systematics from E.coli, but is probably true for one strain only, since Rhs ends (C-terminal toxic domains) are highly variable between species and even strains. To my knowledge, Rhs do encode AHH-like domains and quite often. In conclusion, this is just a mess of protein naming that was picked up from databases, I would correct this name for "Rhs".

Line 181-182 - text is speaking about v2c H383A v2c H384A, but in figure 3, it is v2c HAHA. It might be just naming differences, but it should be consistent.

Line 246 - expression "detoxify D. dadantii" is unclear and a little confusing here, did authors mean kill or eliminate?

Line 263 - "that consisting of" should be "that comprise" or "that possess"

Referees cross-commenting

I agree with the reviewer #1 that the text could be improved by better explaining the nomenclature, and reasoning behind certain experiments such as choice of prey cells. Regarding the novelty, to my opinion it is a choice of authors - either limit their study as it is now and it does not stand out by neither approach nor subject, or as suggested by the reviewers explore the mode of action, specificity and the reason behind the cell filamentation.

I agree with the reviewer #3 that the cell elongation seems to be central interest but it is not investigated properly. I do think, that the SOS reporter would strengthen the study and would help to support (or not) some of the statements. I appreciate the scrutiny of reviewer #3 and I agree that the replicates seem to have extremely low variation and authors should provide precise explication on the reproducibility.

Overall, I agree with the two other reviewers that the weakness of this manuscript is lack of innovation and to some extent lack of support for certain claims. The study could be improved by making it more profound, but a lot of additional work will be needed to bring it to another level.

Significance

Overall, this study is rather detailed, but not very novel - SHH and other HNH nucleases have been already assessed in literature using very similar methods, even by the same authors (Santos et al., Front Microbiol 2020). On the other hand, the study presents in depth investigation of auxiliary toxin, but shows that it is fully functional and has a role in killing, which is important and interesting for the field of Agrobacterium.

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Referee #1

Evidence, reproducibility and clarity

This study characterised one of the four previously identified T6SS effectors of Agrobacterium tumefaciens strain 1D1609. The effector, named V2c, is a His-Me finger nuclease likewise the previously characterised V2a, although V2c has a distinct SHH motif. V2c was found to induce growth inhibition, plasmid degradation, and cell elongation in E. coli. The cognate immunity protein V3c can neutralise the DNase activity of V2c. V2a and V2c are found to function synergistically to exhibit stronger antibacterial activity against a phytopathogen, Dickeya dadantii.

Although the manuscript provides a decent characterisation of the T6SS effector V2c of strain 1D1609 of A. tumefaciens, there are several areas where the authors could make significant improvements to their work.

• The introduction section of the manuscript would benefit from a more detailed background of the research to situate the reader in the appropriate context for a better understanding of the results of this study. Specifically, the authors could provide more information regarding the four effectors of A. tumefaciens 1D1609, their domains, their genetic context, and their immunity proteins. In fact, three of the effectors are, to a different extent, named in the manuscript, whereas the fourth one is not mentioned at all. The authors should also aim to provide more context and explanation of the nomenclature of the effectors. This will make the paper more understandable for readers unfamiliar with the terminology of Agrobacterium effectors. In addition, the authors should consider giving more attention to the phenotype of previously described nucleases, such as cell elongation, so that the reader would better understand the result section when encountering this phenotype. The authors only explain this in the discussion, and it would be helpful to have more clarification in the Introduction as well. The authors should also explain the reasoning behind using that prey cell (Dickeya) and not E. coli or another organism for the antibacterial activity experiments.
• The novelty of the study could be improved by providing a better explanation of the specific mechanism or mode of action through which V2c works. For example, the authors could study more deeply the puzzling fact that the elongation phenotype is independent of the nuclease activity for this effector but not for V2a. Another interesting approach would be to study the putative specificity of these nuclease effectors, as not all of them are effective against bacterial targets. This is an unexplored area of great interest for a more innovative study because nucleases do not seem to be specific, they all degrade nucleic acids, and somehow they have different capacities to kill different prey cells.
• In Figure 1B, it would be convenient to include in the alignment the two nucleases of the same family as V2c that have been already described in the literature and are named in the main text (Tke4 and Txe4) to better illustrate their similarities and differences. In Figure 1C, it would be convenient to add the PAAR-RHS domain to the list of N-terminal domains found with Tox-SHH nucleases.
• When it comes to the microscopy experiments (Figure 5), the authors should work to improve the relevance and quantification of the data they present. This could involve using more rigorous analysis techniques, such as statistical analysis, to support their findings more convincingly. In fact, the authors could enhance the rigour of their analysis (Dickeya cell lysis) by gathering more supporting evidence before drawing their conclusions. The authors should explain why they are using two identical strains (attackers) in the competition assays (Fig 5C) d3EIbcd 1 and 2.
• Regarding the inter-bacterial competition settings between Agrobacterium and Dickeya, the authors should explain why they used TssB-GFP prey cells when this is not necessary for the assays they performed. Furthermore, the authors should clarify the statement in the discussion (lane 353-355) regarding the absence of antibacterial activity of V2c against E. coli, while the results of this work show inhibition of E. coli cells (Fig. 2). The authors should rethink whether the video is necessary for this section, as it does not provide additional relevant information.
• To ensure that the paper is easily comprehensible and effectively conveys its message, the authors should meticulously examine all aspects of their writing, including language usage, grammatical accuracy, and syntax structure. The authors should also ensure consistency in their writing style and language usage throughout the paper. As one example of writing style inconsistency, the authors used both Gram-negative and gram-negative in the manuscript.

Significance

The study expands the knowledge in the specific field of SHH nucleases and T6SS effectors. This could be of interest to T6SS researchers and more broadly to researchers in the field of bacterial toxins.

The novelty of the study is very limited since the authors functionally characterised a T6SS effector with a well-described function, a DNAse (DNA degradation) and a recognised structure (SHH domain). As expected for a nuclease, it degrades DNA and provokes cell elongation, which has also been described before.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors provide insight into the gaps within BRAFi research in an effort to further understand how elements such as mechanisms of resistance and clinically observed adverse events in melanoma patients occur. This manuscript more specifically highlights the effects of BRAFi treatment on endothelial cells in the context of vasculature. The authors begin to explore how traditional BRAFi therapies may lend to such adverse events due to the role they play alongside that of targeting melanoma cells such as off-target effects, paradoxical endothelial signaling, and inducing a pro-tumorigenic microenvironment. The conducted studies demonstrate simple and effective methodology, focusing on proteomic and phosphoproteomic analysis, to elucidate the endothelial consequences of BRAFi treatment. The authors provide sound conclusions from the presented data and validate their in vitro findings with clinical observations using patient tissue. The analysis within this manuscript is just scratching the surface and leaves the authors with much to explore in future manuscripts.

Major comments:

The authors provide a solid story outlining the pitfalls in BRAFi therapy research and the consequences on endothelial vasculature in the treatment of BRAF mutant melanoma. The manuscript details clinical relevance of the research, functional impact to the field, and a thorough discussion on the scope of this work and where it may be lacking, which allows for the opportunity for future directions.

Minor comments:

The authors may consider revising minor errors within the Discussion as indicated below. Discussion - Paradoxical MAPK activation Missing comma between cells and the; "For endothelial cells, the concentration of BRAFi measured in the patient circulation is critical." Discussion - Off targets in endothelial cells Missing comma between range and it; "At concentrations in the low µM range, it inhibits numerous other kinases." Missing commas around apart from MAPK; "This suggests that, apart from MAPK, other signaling pathways would also be affected by BRAFi treatment"

Significance

This manuscript poses a key discussion in the importance of expanding research of molecular targeted therapies on more than just the target cells as the consequences to surrounding cell types can give vital insight into potential adverse effects in the clinic. The authors note that while this is not a novel concept, there are still gaps that prove vital in understanding clinical impact, which they hope to fill with this manuscript. They provide support to their conclusions using primarily proteomic approaches with the addition of some comparative analysis of a publicly available dataset, and patient tissue samples in order to validate their findings. Whether in the context of treating melanoma or any other disease. this manuscript serves as a helpful reminder to pre-clinical and clinical researchers alike in how important it is to factor in the patient as a whole, not just the disease when identifying effective treatment options.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The author Bromberger and colleagues have submitted a MS # RC-2023-02152 entitled "Off-targets of BRAF inhibitors disrupt endothelial signaling and differentially affect vascular barrier function" for review via Review Commons. In the MS they have investigated four BRAF inhibitors with different pharmacodynamics; Vemurafenib, Dabrafenib, Encorafenib and PLX8394 and their specific effect on vascular endothelial cells but also on melanoma cells. The study is composed of in vitro studies using in-house isolated human dermal endothelial cells. Also, melanoma cells and skin biopsies from 5 melanoma patients were analysed. The authors conclude that the BRAF inhibitor Vemurafenib caused strong effect on the endothelial cells' barrier function in comparison to the other three BRAF inhibitors.

Major comments: major issues affecting the conclusions:

In general; a major issue that is affecting the whole story is the rather high concentration of Vemurafenib (100 uM) used in the study. The authors do not provide any data describing the viability and function of the endothelial cells after exposure to 100 uM of Vemurafenib. Instead they have chosen two concentrations with a large (10X) difference. Where the cells viable at 100 uM of Vemurafenib? If the endothelial cells were suffering from 100 uM Vemurafenib, they will immediately loose the cell-cell contacts/junctions and thereby any performed permeability assay would be pointless. Furthermore, isolation of skin endothelial cells is at risk to be accompanied with lymphatic endothelial cell contamination. The authors should provide data ensuring that the cells are of >90% endothelial cell purity by checking for PROX1-positive cells together with endothelia cells markers (CD31, VE-cadherin, uptake of AcLDL etc).

The work is of importance in understanding consequences for endothelial cells exposed to BRAF inhibitors used in the clinic using clinically relevant concentrations of the drugs investigated in vitro. If the authors provide with a major revision, the work could be acceptable for publication.

1. The Western blots in this manuscript are in general overexposed (saturated) and therefore differences between treatment conditions are not possible to be clearly defined. Therefore, quantifications of the experiments should be done and combined with representative Western blots.
2. Figure 1A-C n=?, notice no standard deviations in 1C. Does this mean that in 1C n=1?
3. Figure 1D, no significant differences? If there is no significant difference, then there is no difference between the treatments.
4. Regarding concentrations of Vemurafenib; it is needed that the authors define endothelial cell viability (proliferation, Caspase-9 staining or LIVE/DEAD fixative stains) at this high concentration. Then 10 uM is probably a too low concentration (see data in figure 2 where 10 uM gives no data of relevance). Cell toxic effects could be the reason of increased passage of N-Fluorescein upon 100 uM Vemurafenib treatment or the cause of cell-cell gaps (Figure 5). If 100 uM truly shows that the cells are viable without any signs of toxicity, the paper would be more clear if main figures contain only 100 uM Vemurafenib. It is recommended that cell cytotoxicity is tested for all compounds in this short- and long-term treatments
5. Figure 5; the authors should demonstrate the effect of BRAF inhibitors using a different approach. Trans-endothelial migration (trans-well), or similar methods would enforce the main message. Furthermore, migration defects could be evaluated by scratch-wound assay. Comment: the imaging in figure 5A is not clear enough to truly show the cell morphology and to define the cell status (see point 4 related to cell viability). We also advice that figure 5A also contains stainings for all other treatment conditions (or included in a supplement figure). What´s the mechanism behind junctional rearrangement? Internalization, degradation or actin cytoskeleton-dependent mechanisms? Figure 5A, stainings should be quantified. Figure 5C; with three asterisks in the figure, what is the actual significance and is it compared to DMSO? With the large SD the significance can hardly fit with three asterisks (<0.001).
6. Valuable skin biopsies of patients before and after treatment have been used for figure 6. The authors should pay more careful attention to what vasculature they are investigating in the biopsy material. The authors mainly focus on large arteries (large vascular lumens with a thick layer of ASMA-positive cells). We recommend that they investigate capillaries (5-10 um in diameter) which are more plastic and susceptible towards treatment. Claudin-5 is a vascular marker but the antibody chosen clearly provides with high autofluorescence stains detecting blood cells in the vascular lumen and not only the endothelial cells. We therefore recommend to use another claudin-5 antibody that will stain dermal vasculature better. Which patient is imaged in figure 6? Please prepare a supplement figure with patient 1-4 to show representative images of the main differences. Do the authors expect that Vemurafenib 100µM will also decrease VE-cadherin and claudin-5 total protein levels?
7. Table 2: The quantification is not clear. The authors should describe the data in a more descriptive way. For example, what does it means to have more than 100% (181.41% of claudin-5 for patient 5) of the vascular markers? Also, it is not realistic to describe percentage data with 2 decimals. The authors should also classify their quantification based on vessel type (large caliber vessels vs capillaries), cancer and pseudo-normal tissue. As a way to validate their in vitro findings (permeability and junctional disruption in these patient tissue biopsies), the authors should check for leakage by staining for serum proteins like IgG, fibrinogen or serum albumin.

Minor comments: important issues that can confidently be addressed:

1. The authors want to fill a gap in knowledge related to BRAF inhibitors effect on endothelial cells, which a limited number of publications are available.
2. Why are the authors using CellTracker for visualize cell morphology. It would be better if cells were stained for VE-cadherin and beta-actin including nuclear stain with DAPI. This would far better define the cell morphology after treatments.
3. Please in Material & Methods describe KinSwing activity predictions index to help the reader to follow the results better.
4. Table 1 could be reformatted to be more easily to read.
5. Figure 1, is ERK= ERK1/2?
6. The discussion text should be shortened and more focused towards their findings and with conclusions of performed experiments. How is the paradoxical effect of Vemurafenib (figure 1) related to their later findings (Figure 2 and 3)? In other words, what is the relation between figure 1 and figure 2 and 3?
7. For the discussion; is the result in figure 5C supported by data that patients on Vemurafenib treatment would be exposed to a higher risk of metastasis?
8. Figure 3B, resolution of text needs to be improved and the full compound names could be written in figure 3A.
9. Figure 4A are any of the results statistically significant? If not, then there is no difference.
10. The authors should elaborate a hypothesis based on their phosphoproteomics data. Which of the off-targeted molecule(s) could impact endothelial barrier?

Referees cross-commenting

With our deep knowledge in endothelial cell biology, we would like to emphasize the need of Bromberger et al to reply to our comments. Additional experiments and verifications will improve the impact of the performed research. With reviewer 2 demanding far less additional work to be done there is a discrepancy between the two reviewers of the estimated time needed for performing a revision (1-3 months for reviewer 1 versus 1 month for reviewer 2). I (reviewer 1) believe that at least three (3) moths will be needed to collect additional data to reply to the questions.

Significance

This manuscript addresses an important question; how is the vasculature affected by cancer treatments? It is not unusual that the vascular status is neglected in clinical treatment studies. The manuscript provides valuable phosphoproteomics data of great interest related to this topic. The major weakness of the work is the lack of data verifying the chosen concentrations for the BRAF inhibitors used in the study. There is a great risk that several results based on the 100 uM Vemurafenib treatment (of high impact for the story) are based on cell toxicity due to a high concentration treatment in vitro. Also, the link between the strategy of performed in vitro experiments isn't clear and there is a lack of connecting the in vitro data to the validation performed on melanoma patient tissue biopsies. It is a great strategy to investigate skin biopsies before and after treatment. The precious biopsy material should be more carefully investigated and evaluated.

Audience: after improvement of the manuscript by better presentation of existing data and by additional experiments the work presented would be of interest to a pre-clinical and clinical audience investigating cancer treatments.

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Reply to the reviewers

Please see below for the detailed description of the changes made in response to the reviewers’ comments.

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

The manuscript investigated the composition of the plastid proteomes of seven distantly-related kareniacean dinoflagellates, including newly-sequenced members of three genera (Karenia, Karlodinium, and Takayama). Using a custom plastid-targeting predictor, automatic single-gene tree building and phylogenetic sorting of plastid-targeted proteins for plastid proteome construction, the authors suggest that the haptophyte order Chrysochromulinales is the closest living relative of the fucoxanthin plastid donor. Interestingly, the N-terminal targeting sequences of kareniacean plastid signal peptides, reveal a high sequence conservation. Moreover, ecological and mechanistic factors are suggested that may have driven the endosymbiotic acquisition of the fucoxanthin plastid. Overall, this is a comprehensive and interesting analysis.

Other comments.

1. For analyses of N-terminal targeting sequences, why did the authors not consider to employ Predalgo as an additional tool? Author response: We thank the reviewer for their suggestion. To our understanding, PredAlgo is a targeting predictor trained on primary green algae, which have two-membrane bound plastids and purely hydrophilic N-terminal plastid targeting sequences. It thus would be expected to perform poorly for the prediction of N-terminal targeting sequences in complex plastids such as those of the Kareniaceae bound by three or more membranes, who are located within endomembrane-derived compartments and which utilise plastid-targeting sequences based on an N-terminal hydrophobic signal peptide for ER import.

We considered the application of PredAlgo for the identification of downstream hydrophilic transit peptide regions in Kareniacean presequences, but note that the specific residue positioned after the signal peptidase cleavage site is typically a much better predictor than transit peptide hydrophobicity for identifying plastid-targeting sequences (Gruber et al., Plant J 2015, and citing references). We found that other targeting prediction tools based primarily on hydrophobicity (e.g., HECTAR) performed poorly in identifying probable plastid-targeting sequences in our control Kareniacean dataset, and therefore chose to prioritise a modified version of ASAFind that takes into account the residue context of Kareniacean signal peptidase cleavage site for our targeting predictor, which works with high sensitivity and specificity on our control dataset. We summarise these observations in Fig. S15.

Given the fact that peridinin or fucoxanthin pigment binding is in the focus of the paper, a more detailed introduction of the peridinin and fucoxanthin light-harvesting systems should be given.

Author response: A brief introduction to the pigment-binding proteins in dinoflagellates was added, “These include a unique carotenoid pigment… massively paralogized and synthesized as polyproteins” (lines 86-89).

The authors state "It is also possible that there has been a direct niche competition between the peridinin and fucoxanthin plastid that may have coexisted in the same host for a period of time with possibly different selective pressure on retention of their respective proteins based on their interaction with plastid-encoded components, e.g., extrinsic photosystem subunits not assembling correctly with their intrinsic haptophyte-like counterparts." It is tempting to ask, whether peridinin light-harvesting systems have left traces in the fucoxanthin plastid, possibly due to mistargeting of peridinin light-harvesting systems into the fucoxanthin plastid? Are some photosynthetic subunits "in-between" peridinin and fucoxanthin plastids?

Author response: We did not identify any other peridinin-like photosystem subunits than the ones visualized in the map schematic (i.e., ferredoxin/PetF in both Karenia and Karlodinium and PsaD of Karlodinium micrum) and discussed in the supplementary text. PetF is the only consistently retained peridinin-like photosystem protein, likely due to the fact that it is not strictly linked to photosynthesis: it is expressed in plant leucoplasts, and plastid-encoded in some non-photosynthetic chrysophytes. We have added a sentence in Supporting Text 6.4 that “we detect no possible homologues of peridinin-chlorophyll binding proteins (PCP) in any kareniacean transcriptome” (line 91).

Figure 3 is difficult to understand, e.g. for PSI and PSII which subunits are shown, why has PSI "more" contribution from dinoflagellates as compared to PSII?

Author response: The photosystem subunits are ordered numerically in the schematic, and detailed information on each protein and the corresponding sequences with their origin are included in the supplementary table S3. A single subunit of photosystem I (PsaD) was determined to be of plastid-early (peridinin-like) origin in Karlodinium (while the same protein is plastid-encoded in Karenia and undetermined in Takayama). We believe this may be simply due to an evolutionarily neutral differential loss / non-adaptive retention of photosynthesis-related proteins in a secondarily non-photosynthetic host before the acquisition of a replacement plastid. We note that there are only two (incomplete) kareniacean plastid genomes available so we cannot rule out the possibility of this subunit being plastid-encoded in Karlodinium as well (which would mean that both plastid-late and plastid-early homologs co-occur in this genus).

Fig. 3 is necessarily complex due to the size and multiplicity of the dataset considered. To facilitate reader navigation, we have added the following text to the figure legend (lines 1128-1140) text “Plastid proteins are arranged by major metabolic pathway or biological process, with each protein shown as rosettes … Proteins of plastid-late (haptophyte) origin, such as are concentrated in photosystem and ribosomal processes, are coloured red; and proteins of plastid-early (dinoflagellate) origin, such as are concentrated in carbon and amino acid metabolism are coloured blue. … In certain cases (shown as rosettes with multiple colours), homologues from different species have different evolutionary origins, e.g. Karenia possessing plastid-late and Karlodinium/ Takayama plastid-early”.

Data shown in figure 4, is there experimental evidence for signal peptide cleavage site(s). Could these data been used to predict mature plastid targeted protein sequence?

Author response: We were able to determine the conserved motives in signal peptide, including its cleavage site (GRR) which we exploited in the design of kareniaceae-specific matrix for ASAFind. We show these residues in Fig. 4. We note that these motifs were identified based on homology to known signal processing peptidase recognition sites, as opposed to experimentally determined protein N-termini.

Consistent with previous studies (e.g. Yokoyama et al., J Phycol 2011) we see limited evidence for consensus plastid transit peptide cleavage motifs in kareniacean presequences, and do not discuss this further as a result.

The authors state "Partial Least Square (PLS) analysis shows a set of environmental variables (salinity, silicate, iron) positively correlated with abundances of both Karenia and Takayma and also haptophytes as a whole, but at the same time negatively correlated to Karlodinium (Figure S8), further illustrating that the latter genus is quite distant from the rest in its biogeographical pattern." How could this be interpreted in the light of the plastid proteomes

Author response: We believe that this may be due to the more cosmopolitan distribution of Karlodinium, and possibly also a result of bias stemming from our strategy of grouping the organisms at the genus level (as not enough data was available at species level) which may obscure the potential outlier status of only some species/ subpopulations. This is particularly true for the haptophytes, where in the absence of specific ancestry for individual kareniacean plastids we are only able to consider distributions at the levels of entire orders. We now acknowledge this in the Discussion: “specific ecological interactions between the progenitors … via ancestral niche reconstruction for each lineage” (lines 473-475).

Please note, that the results might have changed slightly from the previous version due to the re-calculation following additional normalization of the data (see below).

Reviewer #1 (Significance (Required)):

The current manuscript gives insights into the endosymbiotic acquisition of the fucoxanthin plastids.

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

This is a well done, detailed bioinformatic analysis of genomic and transcriptomic data from an important lineage of dinoflagellates that have undergone serial substitution of their plastid. On the whole I am enthusiastic about the paper; it presents valuable new insights, and is rigorously performed. However, I have to object to the way the term "proteome" is used in the paper; the manuscript is talking about the predicted proteome, not a measured proteome. This is something of a technical distinction, but it is an important one because the transcriptome and the proteome don't necessarily track each other, and there is little or no actual proteomic data available from dinoflagellates. We assume that transcript abundance has something to do with proteome abundance, but this is often violated. What this paper is really addressing is the potential proteome, because if a given gene is completely absent from the genome and the transcriptome we can be confident it will not be present in the proteome. The converse is not true. For this reason I feel it is important to be clear on the distinction. I would be satisfied in this regard by minor modifications, using the term "predicted proteome" in the title, and being more direct in the introduction about the distinction.

Author response: We agree that the usage of the word proteome for in silico predictions is not entirely correct, and have used the term “predicted proteome” where possible in the text to clarify this.

We have also, as described in our response to Reviewer 1 above, included a statement in the Discussion that our largely bioinformatic results will be transformed by an experimentally realised kareniacean plastid proteome, which we nonetheless feel goes beyond the scope of our manuscript.

Overall the analyses are impressive. I do have to squirm a little when I see automated analyses generating alignments where the threshold is less than 75% gaps and at least 100 nucleotides aligned. I looked at the supplementary data and the figshare files and could not find the alignments themselves, so I don't know what fraction of the sequences are in that territory. Because phylogenetic analysis (as performed here) treats the alignments as an observation, and because the alignments include sequences with more than 50% gaps, it is entirely possible that some taxa, or even whole segments of the tree, are based on non-overlapping data.

Author response: We thank the reviewer for their comment and have added in three new supplementary figures (S16-S18) providing statistics on alignment size, length, and average gap percentage distribution. We report that most of the alignments contained relatively little gaps: 90% of the alignments contained between 1.1 and 24.5% of gaps with median value of 6.6%.

Mind you, we have done similar analyses, and I don't think this invalidates the results, but it does open up the possibility of some dramatic artifacts. Consequently, I would recommend a) making the alignments available (or more obvious where to find them), and b) providing more detail on the alignments, including, if possible, to add a figure (probably in the supplementary data) that visualizes them. It is not given in the text itself, but according to the figure 2 caption there are 22 sequences thought to be "plastid late", and 241 in the pan-eukaryotic dataset. This is a scale that is feasible to put in a figure showing, for example, each aligned residue as a color and indels as grey. Such a figure is readable even when the individual residues are only a few pixels in size (less than a millimeter when printed). I also recommend describing the final alignments more fully in the text. Most of the summary statistics are presented in normalized form, and that can obscure patterns that come from poorly sampled taxa. Better clarify on the characteristics of the alignments will make it easier to interpret the findings overall. Although this is critical to interpreting the results, gappy alignments are not uncommon in analyses of this sort, and setting that aside the analyses presented are comprehensive and thorough. The discussion does a good job of addressing the significance of the work, and potential causes of error are addressed adequately (aside from the matter of the alignments).

Author response: We thank the reviewer for their comment and have provided alignments for all single-gene trees, in a dedicated online supporting repository (https://figshare.com/articles/dataset/all-automatically-generated-alignments_rar/24347032). The datasets and alignments used for PhyloFisher and plastid-encoded gene trees are included directly in the supplementary files (phylofisher_files.tar, plastid_genome_phylogeny_files.tar and plastid_protein_phylogeny_files.tar).

We have additionally included three new supporting figures (S16-S18) showing the distributions of lengths, gaps and homologues in each single-gene tree. These data project largely completion of individual alignments, with only 5% containing > 20% gapped positions (see Fig. S18), for example. We have additionally clarified in the Methods that “The trimmed alignments were then filtered by a custom python script that discarded sequences comprising of more than 75% gaps and then rejected alignments shorter than 100 positions or containing fewer than 10 taxa.” (lines 571-573).

For the two concatenated trees presented, we have clarified in the Methods the alignment lengths (PhyloFisher: 72, 162 positions; plastid genes: 2,404 positions), and that we removed sequences containing >66% of gaps from the final alignment. Reflecting on the congruency assumptions required to concatenated alignments, we have chosen to replace the plastid-late concatenated tree (which may group proteins with multiple phylogenetic signals) with a new main text figure 2 providing an overview of the plastid signals we observe across the entire dataset (see comments below to Reviewer 3).

Reviewer #2 (Significance (Required)):

I find the paper to be exciting and important. These organisms are economically important, particularly as potential nuisance organisms, but also because of their role in primary productivity. They also have extremely complex evolutionary histories and similarly complex genomes. performing any bioinformatic analysis of these organisms is a substantial challenge because almost every gene exists in high copy number and with complex and often obscure patterns of homology. The manuscript brings forward these challenges, and makes a substantial step forward in elucidating the evolution of a group that is fascinating and important, but remarkably difficult to work with. I feel that it is an important analysis, and should be of interest to a broad audience.

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

Summary

This manuscript entitled "Divergent and diversified proteome content across a serially acquired plastid lineage" by Novak Vanclova et al. proposes the origin and evolution of plastids in kareniacean dinoflagellates. The authors generated new transcriptome data from Karenia mikimotoi, Karenia papilionacea, Karlodinium micrum, Karlodinium armiger, and Takayama helix. Combining them to the previously published transcriptome data from kareniacean dinoflagellates, they constructed the pan-kareniacean transcriptome library. They surveyed plastid-targeted protein-coding transcripts in the dataset, and consequently they estimated ~14.5% of the transcriptome data were of plastid-targeted ones. Of them, 65-80% were derived from a peridinin-containing dinoflagellate ancestor while ~15% were derived from EGTs from a haptophyte endosymbiont of the current plastid origin. By using the plastid-targeted transcript dataset, they investigated 1) origins of the plastid-targeted protein-coding transcripts by single gene-trees, 2) the plastid origin and evolution by the multigene dataset of 22 conserved plastid-targeted protein-coding transcripts and of 3) plastid genome-derived transcripts, 4) plastid functions, 5) diversity of plastid-targeted signals in kareniacean dinoflagellates, and 6) the distributions of kareniacean species by using the Tara Oceans database. On the basis of their results, they proposed many hypotheses regarding kareniacean dinoflagellate evolution, such as i) the chrysochromulinales-origin of the plastids, ii) more recent acquisition of the plastid than previously thought, iii) a plastid replacement within kareniaceae evolution, iv) the strict selection of signal peptides but non-conserved transit peptides in the kareniacean plastid-targeted proteins, and v) correlated or non-correlated distribution patterns of kareniaceaen dinoflagellates to specific haptophyte lineages.

Although their proposals are interesting, I have many concerns to be addressed. Especially, their analyses on which the above proposals are based seem to be still preliminary and inconclusive. To support their proposals more confidently, I also suggest some additional analyses.

Major comments

1. seemingly inconsistency between the authors' claims The most striking is inconsistency of the authors' claims proposed in this manuscript. Their proposals include a) the common ancestor of kareniaceans has not possessed a fucoxanthin plastid but the plastid has been acquired more recently, b) an ancestor of Takayama and Karlodinium has gained a fucoxanthin plastid from a (chrysochlomulinales) haptophyte, c) an ancestor of Karenia has gained a fucoxanthin plastid from Karlodinium. However, they also demonstrate a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama. If I understand correctly, "a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama" would seemingly be inconsistent to and challenge two of the authors' claims: no haptophyte-derived plastid in the common ancestor of kareniacean dinoflagellates and a Karlodinium-to-Karenia plastid transfer (Fig. 7). If the Karenia plastid is derived from Karlodinium, I have no idea why haptophyte-derived plastid proteome of Karenia is larger than that of Karlodinium. After the plastid acquisition in Karenia, Karenia might have gained more genes for plastid-targeted proteins from haptophytes by LGTs. If this is true, many single gene trees would suggest different origins of plastid-targeted proteins between Karenia and Karlodinium/Takayama. Can we see it in the single gene analyses? I would like authors to rationalize the inconsistency in the main text.

Author response: We agree with the reviewer that the evolutionary origins and dynamics of the kareniacean plastid proteome are complex, and thank them for their suggestion.

First, to take into account the different evolutionary scenarios that could explain the present-day distribution of the kareniacean plastids, including the new plastid genome sequences identified in response to the reviewer’s suggestions, we have made a revised version of Fig. 8 evaluating three different hypotheses (see below). Nonetheless, we feel that the Karlodinium-to-Karenia model we propose is plausible, based on the following observations:

• We identify 1,418 plastid protein gene trees in which at least two of the three studied genera (Karenia, Karlodinium, Takayama), and 748 in which all three resolve as monophyletic, and with a haptophyte sister-group (i.e., a common plastid-late origin; Fig. S2). This points to a common haptophyte ancestry in all three groups, as opposed to independent endosymbiotic consumptions of free-living haptophytes in Karenia and Karlodinium micrum.

• We see no such shared signal with the RSD, which shares only 42 proteins with at least two other kareniacean genera (Fig. S4). Thus, and consistent with previous studies (Hehenberger et al., PNAS 2019) we cannot invoke an ancestral presence of a fucoxanthin plastid shared with the RSD in the last common kareniacean ancestor. This discrepancy thus likely points to a serial transfer of the kareniacean plastid from either Karlodinium into Karenia or vice versa (Fig. 8).

• Concerning the direction of this transfer, among 1,059 gene trees of plastid-late origin found in both Takayama, Karenia and Karlodinium, 873 place Takayama as basal to a monophyletic clade of Karenia and Karlodinium, i.e. support a specific plastid transfer between the latter two genera. The most parsimonious explanation for this is the origin of the fucoxanthin plastid in the common Takayama/ Karlodinium ancestor, which was subsequently transferred into Karenia. It is true that Karenia contains both a greater absolute proportion of predicted plastid-targeted proteins (Fig. 1) and greater number of unique KO number annotations (Table S4) of plastid-late origin than either Karlodinium or Takayama. That said, this signal may be influenced by multiple other factors beyond how old the given endosymbiosis is (i.e., longer coexistence implies more EGT). For example, the number of plastid-late gene in a host genome may depend on the frequency of duplication of plastid-late genes and the receptiveness of the host nuclear genome to incoming horizontally derived genes. It may further be influenced by the presence and relative selective advantage or disadvantage of competing genes of host nuclear origin (i.e. plastid-early genes) that may be differentially selected over plastid-late genes, which might vary between Karenia and Karlodinium due to differential retention of the ancestral peridinin-type plastid in each lineage.

We have elaborated on this point in the Discussion, noting that there may have been “a direct niche competition between the peridinin and fucoxanthin plastid … with possibly different selective pressure on retention of individual imported proteins” (lines 370-372), “relatively recent origin and spread throughout the kareniacean genome, e.g., via gene duplications” (line 459), and finally that precedent for divergent evolutionary trajectories in different Kareniaceae exists from the Karenia and Karlodinium plastid genomes that “contain partially non-overlapping sets of genes that suggest independent post-endosymbiotic plastid genome reduction” (lines 403-404). Nonetheless, we acknowledge that the evolutionary model we propose is not definitive, and that alternative explanations may find more favour with increased genome data.

Signal peptide prediction I think the modified ASAFind would be greatly helpful for future studies on automatic prediction of plastid proteomes in kareniacean dinoflagellates. However, I found no data on selection criteria for the signal peptide prediction program SignalP5.0 used. I believe such data would be very important to interpret the previously published paper by Gruber et al. in which prediction methods for plastid-targeting sequences are compared to each other to see how sensitively and specifically they can capture the plastid proteomes.

Gruber et al. 2020. Comparison of different versions of SignalP and TargetP for diatom plastid protein predictions with ASAFind.

According to Gruber et al. (2020), signalP5.0 is not suitable for prediction of signal peptides for diatoms, in consistent with the authors' claim for kareniacean dinoflagellates. This inconsistency would be difference of the nature in signal peptides between diatoms and kareniacean dinoflagellates. Even if so, it would be useful to see quantitatively how much different their signal peptides are in terms of their suitable prediction programs.

Author response: In our preliminary benchmarking using only the previously published transcriptomes (see additional sheet in Supplementary tables), SignalP 5.0 performed substantially better in terms of specificity than SignalP 3.0 (i.e., 22 versus 34/ 728 retrieved positive hits of proteins with uniquely non-plastidial functions), with comparable sensitivity in the correct prediction of positive control proteins. Given the size of our dataset, and the substantial risk of false positive detection in the highly expanded and redundant dinoflagellate transcriptomes we have used, we feel that the greater specificity of SignalP 5.0 is important to integrate in our model selection. We have clarified this position in the Methods, stating “First, the relative effectiveness of two SignalP versions … SignalP 5.0 was used for all subsequent analysis.” (lines 525-529).

I also have a concern about use of the combination of PrediSI and ChloroP, combination which is suitable for the plastid proteome prediction in Euglena gracilis. The authors should rationalize why the method for Euglena plastids can be applicable without any modification to the plastid proteome prediction in kareniacean dinoflagellates. Although Euglena plastids are enclosed by three membranes, kareniacean plastids are by four. Therefore, from the side of molecular mechanisms in protein import, the method suitable for Euglena plastids is not necessarily suitable for kareniacean dinoflagellate plastids.

By using PrediSI and ChloroP, they detected additional "candidate plastid proteomes" including several proteins not detectable by SignalP5.0 and the modified ASAFind. That seems great. However, they did not seem to consider false positives since there is no mention on it. Although the additional candidates predicted by PrediSI and ChloroP included true plastid proteins of kareniacean dinoflagellates, many might not be. Nevertheless, the authors suggest 7.5 to 14.5% in K. micrum and K. brevis, respectively, are of plastid-targeted ones. I am so afraid if the proportions would be highly overestimated due to false positives by PrediSI and ChloroP. To rationalize the use of PrediSI and ChloroP, the authors should show sensitivity and specificity by quantitative analyses with a benchmark dataset.

Author response: We thank the author for this comment. The reasoning behind using the parallel PrediSI+ChloroP strategy was the previously reported similarity of the plastid signal structure between euglenids and peridinin dinoflagellates (c.f., Lukes et al., PNAS, 2009) and the previous observation that some kareniaceae posses plastid-targeting sequences resembling those of peridinin dinoflagellates (c.f., Hehenberger et al., PNAS, 2019). Per the reviewers’ suggestion, we present a modified sensitivity/ specificity testing PrediSI+ChloroP, alongside other alternative targeting predictors in Figure S15. While the PrediSI+ChloroP sensitivity is very low, its specificity is comparable with the modified ASAFind, and in this regard outperforms other targeting predictor tools, thus rationalising the use of both targeting prediction tools together.

Origin and evolution of kareniacean plastids The authors suggest the chrysochromulinales origin of the kareniacean dinoflagellate plastids and the Karlodinium-to-Karenia plastid transfer, on the basis of phylogenetic analyses using the concatenated datasets with the 22 conserved plastid-targeted proteins and with plastid-genome derived transcripts. It is very interesting that those plastid-targeted proteins in kareniacean dinoflagellates might be phylogenetically closely related to chrysochromulinales haptophyte I have suggestions on the analyses and interpretation

As the 22 analyzed genes are nuclear-encoded plastid targeted genes, they are a quite small portion of entire plastid proteins. I am not convinced by that evolution of the small number of genes reflects evolution of fucoxanthin plastids of which proteomes are comprised of >1000 proteins. How many genes for haptophyte-derived plastid-targeted proteins suggest the monophyly of kareniaceaen dinoflagellates and chrysochromulinales haptophytes should be investigated by, for example, a coalescence-based analysis such as Astral for all the detected haptophyte-derived plastid-targeted proteins including the 22 genes. This is because the monophyly could be reconstructed only by one or few, limited number of proteins even if the concatenated dataset is analyzed.

Relevant to this, plastid-targeted proteins derived from a peridinin-containing ancestor might still have phylogenetic signals of host evolution. I am interested in whether such analyses with peridinin plastid-derived plastid-targeted proteins reconstruct Takayama and Karlodinium as monophyletic but separate Karenia from them, as suggested in the phylogenomics with non-plastid proteins.

Author response: We agree with the reviewer concerning the problematic nature of concatenations with small numbers of genes, particularly if the underlying gene trees are not phylogenetically congruent to one another, and have chosen to replace the concatenation with a more global evaluation of the different plastid protein origins across our entire dataset. Using automated sorting approaches, we have evaluated the support for our evolutionary model across hundreds of gene trees. We feel that this approach supercedes coalescence-based techniques, as it enables us to treat each gene topology as an independent event, and to consider multiplicity in the origin of the kareniacean plastid proteome. We present these data in a new Fig. 2 and S2.

As stated above, these data strongly support monophyly of all three Kareniacean genera. Concerning the potential Chrysochromulinalean plastid signal in our dataset, we have reanalysed our data and quantify a substantial number of trees (220/ 1,418 of plastid-late origin) that specifically place multiple kareniacean genera within the Chrysochromulinales. This figure is more than twice the number (91) that place the kareniaceae with the next most occurrent haptophyte group in our dataset, Isochrysidales. We nonetheless have chosen to no longer present this as a cryptic plastid endosymbiosis, in the absence of clear examples of extant kareniaceae still possessing this plastid, saying purely in the Discussion that “a common ancestor of the studied organisms either possessed a stable plastid or had a long-term symbiotic relationship (e.g., kleptoplastidic) with a haptophyte lineage related to the extant Chrysochromulinaceae” (lines 363-365).

Concerning the phylogenetic placement of each karenicean genus, the majority of our plastid-late trees specifically recover the monophyly of Karenia and Karlodinium. Remarkably, we find that Takayama and Karlodinium only resolve together in 69/ 1,039 plastid-late gene trees in which all three genera are represented, strongly refuting a vertical origin of the haptophyte-derived components of their plastid proteome. This is not due to the Phaeocystales origin of the current Takayama plastid genome, which is found in only 21 of our plastid protein trees. Nonetheless, as the reviewer suggests, the opposite trend (1,505/ 2,804 gene trees grouping Takayama and Karlodinium as monophyletic) was observed amongst plastid-early gene trees, which might reflect a cryptic peridinin plastid shared between these groups. We expand on these results in the Discussion, stating “Many of the plastid-early gene trees copy the organismal topology …this awaits structural confirmation via microscopy” (lines 383-386).

Finally, to enable reviewer comprehension of the relationships shown, we have presented some exemplar topologies of some of the trees previously displayed in the concatenation, provided in a new Fig. S5.2.

For the phylogenetic analysis of plastid genome-derived transcripts, I might be wrong, but I could not find any information on dataset sizes (i.e., the numbers of sites) and evolutionary models for the analyses in the main text nor supplementary document. Although one may see the dataset sizes when looking at the original datasets in the supplementary files, such information is substantial and thus is to be described in the materials and methods section. I am afraid if this analysis was performed with a small dataset size. I would like to know total lengths of the concatenated sequences and especially that for Takayama. The phylogenetic position of Takayama, distantly related to the other kareniaceans, in this tree might be caused by a larger portion of gaps in the Takayama sequences than in the other kareniaceans.

Author response: As noted in our response to Reviewer 2, we have included three new supplementary figures (S16-S18) with statistics on alignment size, length, and average gap percentage distribution. The average and median values of these three measurements do not differ significantly when calculated separately for different organisms. We have clarified in the Methods that the concatenated alignments retained (PhyloFisher, and plastid-encoded genes) were “constructed by IQ-TREE with the LG+C60+F model for the plastid matrices and posterior mean site frequency (PMSF) model (LG+C60+F+G with a guide tree constructed with C20) for PhyloFisher matrix” (lines 630-632).

Moreover, due to lack of the plastid genome sequence of Takayama, no one could confidently identify plastid genome-derived transcripts: some of those could be derived from second, nuclear copies that might be pseudogenes. Otherwise, even if they are plastid-derived, no one can evaluate whether they are transcripts after or prior to RNA editing. I am afraid if the dataset used is comprised of a mixture of edited and non-edited sequences in kareniacean sequences. Either of sequences after or prior to RNA editing, latter of which are identical with DNA sequences, should be consistently used for the phylogenetic analysis. In any case, the plastid genomes are necessary for this analysis, and the authors can easily obtain them by DNAseq as they have the cultures.

Author response: We thank the Reviewer for their insightful response. We agree that understanding the evolution of kareniacean plastid genomes are crucial to understanding their evolutionary history.

We have accordingly, as described above, integrated a new main text Fig. 5 building a concatenated tree of plastid marker genes (psbA, psych, psbD, psaA, rbcL, and 16S rDNA) historically and commonly used to assess the evolutionary origins of fucoxanthin plastids (e.g., Takishita et al., Phycol Res 1999; Dorrell and Howe, PNAS 2012). These sequences were amplified cryopreserved stocks of total RNA and specific primers, amplified by RT-PCR. We have chosen here to use RNA sequences, to account for the presence of plastid RNA editing, which has been shown to play an important role in maintaining sequence identity between kareniaceaen plastids and haptophyte relatives despite a high DNA mutation rate in the former (Jackson et al., MBE 2013; Klinger et al., GBE 2018), rather than DNA sequences for this analysis.

Additionally, we would like to note that while plastid genomes are generally relatively simple to sequence and assemble, this is not the case in Kareniaceae. The existing plastid genome assemblies are partially incomplete and suggest more complex and possibly unstable structures (e.g., involving at least some minicircles in Karlodinium micrum, Espelund et al., PLoS One 2012; Richardson et al., MBE 2014). From personal communication with our colleagues, we are aware of some efforts to sequence additional kareniacean plastid genomes that unfortunately have not yielded satisfactory results and publications to this day. This strongly invites a separate project focused on kareniacean plastid genomes but is vastly out of scope of this study.

As described above, we have obtained striking new results which we are happy to report in the revised manuscript and which suggest even more, so far unnoticed, plastid replacements in the kareniacean lineage. In light of these finding, parts of the Results and Discussion sections have been extensively rewritten, and the schematic models presented in Fig. 8 has been updated to account for the distinct evolutionary origins of the Karlodinium armiger and Takayama helix plastids.

In addition, although I might be wrong, the phylogenomic analysis for plastid-encoded transcripts might be performed with their nucleotide sequences according to the figure title and legend of Figure S4 mentioning "nucleotide phylogenetic matrix" and the file name "plastid_coded_nt_concatenation_files.tar". If so, translated amino acid sequences should be subjected to phylogenetic analysis, to avoid a well-known artifact that is caused by saturation of substitutions at the 3rd codon.

Author response: With the exception of our 16S rDNA trees (in supporting data), all of our trees were generated with conceptual amino acid translations using a standard codon translation table, in accordance with previous studies (e.g., Klinger et al. GBE 2018). We have revised the file and figure names accordingly.

Duplication of an ATP synthase subunit Duplication and relocation of ATP synthase subunit delta seems interesting. In figure S6.4.1, could you clarify why the possible extensions containing signal peptides lack the initiation methionine at N-termini? I wonder they are 5′ UTRs but artifactually detected as signal peptides, if they all indeed lack Met. To evaluate this point, I recommend 5′ RACE followed by transformation into a model organism as performed in previous studies by some of the authors.

Author response: We reinvestigated these sequences more thoroughly using raw nucleotide data and conclude that the evidence for their retargeting to plastids is very weak and the reported extensions more likely represent untranslated regions some of which were falsely predicted as signal peptides. This section was removed from the new version of the manuscript, although we have noted in Supplementary Text 6.4 that: “A targeted HMMER search for possible distant homologs revealed that the distantly related functional analog of this protein in mitochondrial F-type ATP synthase (ATP5D, K02134) is duplicated in all species except Takayama. The additional copies, however, do not possess a detectable plastid-targeting signal and the specific functions of this duplicated subunit remain to be determined” (lines 107-111).

Comparison of transit peptides Amino acid compositions in transit peptides would vary when targeted compartments are different. In complex plastids, there are functionally distinct compartments: lumen, stroma, periplastidal compartment (PPC). Comparison should therefore be conducted separately for lumen-targeted, stroma-targeted and PPC-targeted proteins in order to claim their transit peptides are not conserved.

Author response: We acknowledge that this question was not explored in our analysis. We therefore re-analyzed our datasets taking the inferred sub-plastidial (thylakoid vs other, based on function) localization of the proteins into account. Our results showed no notable differences between these subsets and are reported in supplementary figure S10.

RDS never possessed a stable fucoxanthin plastid Although the authors cite Hehenberger et al. 2019 for that RDS never possessed a stable fucoxanthin plastid, as far as I know, that paper seems not to mention it. Could you let me know where that is mentioned in the paper? Hehenberger et al. instead proposed the retention of non-photosynthetic peridinin plastid.

Author response: We have modified the Results text, noting that we only identify 42 plastid-late proteins shared between RSD and other Kareniaceae, and in the Discussion that these data provide only limited support for a shared fucoxanthin plastid. We further clarify in the Introduction that “In some cases, the co-existence of a new organelle or endosymbiont with a remnant of the ancestral plastid has been proposed” (lines 106-108) and “It has previously been suggested that the RSD retains a non-photosynthetic form of peridinin plastid” (lines 378-379) with regard to the Hehenberger paper.

Regardless of whether Hehenberger et al. mentioned or not, Novák Vanclová et al. propose that RDS never possessed a stable fucoxanthin plastid because, if I understand correctly, they detected no or few haptophyte-derived RDS genes for plastid-targeted proteins of which origins are shared with those of Karlodinium, Karenia, and Takayama. What about the possibility that the last common ancestor of kareniacean dinoflagellates possessed a fucoxanthin plastid in addition to peridinin plastid followed by almost complete losses of those haptophyte-derived genes after loss of a fucoxanthin plastid in evolution leading to RSD? Free living eukaryotes were appeared to have lost a plastid in recent studies and they have only a few or no genes showing evidence of a plastid previously retained. We cannot rule out that an ancestor of kareniacean dinoflagellates possessed both of peridinin and fucoxanthin plastids, as the authors mention in the main text, and either plastid was inherited to each lineage by differential losses. Accordingly, I would say Fig. 7 is a too much strong proposal as alternative hypotheses are still present. They should be introduced equally.

Author response: We thank the reviewer for this comment. As discussed above, we evaluate the possibility of a cryptic peridinin plastid shared in different kareniaceae, which is suggested at a genetic level by our data but awaits structural confirmation.

We agree that alternative hypotheses may be invoked for the origins of the current kareniacean plastids, and have modified our Fig. 8 to present three alternative possibilities: serial transfer, independent acquisition, and coexistence of an ancestral peridinin and fucoxanthin plastid, as the reviewer suggests. The presence of an ancestral fucoxanthin plastid that was subsequently replaced in Takayama and Karlodinium armiger is strongly suggested by the monophyly of the plastid-late signal across all kareniacean species studied, except RSD. We nonetheless feel that the frequent monophyletic placement of the Karenia and Karlodinium micrum plastids to the exclusion of Takayama in our plastid-late gene trees strongly argues against a vertical inheritance of this plastid from the common kareniacean ancestor, and more likely reflects a serial transfer between the Karenia and Karlodinium / Takayama branches. We have evaluated the evidence for and against each hypothesis in the Discussion and in the Fig. 8 legend.

rRNA copy numbers in dinoflagellates It is known that the rRNA gene copy number varies among populations or strains in dinoflagellates; some possess several dozens of times as many rRNA gene copies as others (Galluzzi et al. 2010). Is it informative to see the ocean wide rRNA gene amplicon data for the kareniacean dinoflagellates? The numbers of rRNA gene-derived reads would not necessarily reflect the cell abundance of dinoflagellates.

Galluzzi et al. 2010. Analysis of rRNA gene content in the Mediterranean dinoflagellate Alexandrium catenella and Alexandrium taylori: implications for the quantitative real-time PCR-based monitoring methods. J Appl Phycol 22:1-9

Author response: We thank the reviewer for raising this point. The exploration of Kareniaceae distribution was intended primarily to investigate their respective ecological relevance in terms of niche diversity, in particular compared with the well-known cosmopolitan patterns of haptophytes, rather than comparing their abundance patterns. We feel that our approach, treating each Kareniacean genus independently, is sufficient for this, but have now clarified in the Results that the different abundances observed “may be biased by the different ribosomal DNA copy numbers in different genera” (lines 330-331) and have cited the reference the reviewer has kindly supplied.

We further note in the Discussion that “It will therefore be worthwhile in the future to assess the distributions of other more recently developed marker genes (Penot et al., 2022; Pierella Karlusich et al., 2023)” (lines 371-372).

Minor points

1. the dataset size for the 241 protein-based host phylogeny should also be described in the main text. Author response: The information (72,162 positions241 genes, removal of sequences with >66% gaps) has been included in the Materials and Methods.

The authors mention in Discussion "Thus, our results illuminate the mechanistics of a fundamental process that may under pin vast tracts of chloroplast evolution". If I understand correctly, I think this is based on "shopping bag model" when considering plastid replacements in dinoflagellates. It is helpful to add more details to clarify why the authors would like to claim so. "Chloroplast" should be replaced with "plastid".

Author response: We agree that the term plastid is more appropriate in this context, and have used it globally throughout the manuscript. We have mentioned once in the Introduction “primary plastids, i.e. chloroplasts” to orient the non-specialist reader.

We have elaborated on our definition of the Shopping Bag model, and the specific importance of the Kareniaceae, in the Discussion: “The idea that individual genes encoding plastid-targeted proteins may exhibit evolutionary affiliation with other groups than the plastid donor, typifying the “shopping bag” model (Larkum et al., 2007), is well-established in many plastid lineages” (lines 350-352).

Nonetheless, we feel that our data are in many ways different to those previously observed in other plastid lineages. This may reflect that the kareniacean plastid has undergone one, and potentially multiple, recent replacement events. Nonetheless, the predominant contribution of the host to the plastid proteome is striking, which we elaborate in the Discussion: “Our data show that the dinoflagellate host was the principal contributor of nucleus-encoded proteins supporting the kareniacean plastid proteome” (lines 352-353).

Supplementary document S6.6 I found the term nitrogen fixation, but should this be replaced with "nitrogen assimilation"?

Author response: We have corrected the text as requested.

Figure S5 For those LGTs, all the trees should be shown in supplementary text as they are only 11 or 12 trees. Especially, please add the chlorophyllide b reductase and chlorophyllase in the figure.

Author response: Trees for all laterally transferred genes mentioned in the text have been provided among supplementary figures (S7.1-10).

References I am not picky about a format of the reference list, but I think it should be consistent throughout the list. I recommend adding journals, volumes, and pages precisely for cited papers. I found lack of them at least in Novak Vanclova et al. and Pierella Karlusich et al.

Author response: We corrected the incomplete citations and will perform a complete reformatting of the references to comply with the requirements of a concrete affiliate journal.

Figures In figure 3, I strongly recommend adding RDS data, while distinguishing them by another color if they are derived from different origins from those of Karenia, Karlodinium, and Takayama. This would make the authors claim clearer that there are few haptophyte-derived genes for plastid targeted proteins of which origins are shared with those of the other kareniacean dinoflagellates.

Author response: We believe the comparison to RSD is not among the main stories of our study and adding this dimension to the already complex discussion and metabolic map schematic would compromise the overall clarity. This point is already noted by Reviewer 1 (above). However, this question may indeed be asked by some readers, therefore we decided to include the results for RSD as an additional column in the supplementary table S3 and as an additional graphical element in the supplementary version of the map schematic (figure S8). Per the reviewer’s comments above, we have further stated the number of plastid-late trees shared (42) between the RSD and other kareniaceae in the Results text.

In figures S5.1-2 showing LGTs, I found two paralogs of kareniacean dinoflagellates. What does "CP" mean? If "CP" means ChloroPlast-targeted, both paralogs of K. brevis in HARS and those of K. micrum are of plastid-targeted in TARS and they do not have cytosolic ones. I am afraid if these cases are caused by false positives of detection for plastid-targeted proteins by PredSI and ChloroP. Similarly, in figure S5.4, I found two distant paralogs of heam oxygenase in the tree and the taxon names for both types in kareniaceans include "CP." Are both targeted to the plastids or of false positives?

Author response: The annotation with “CP” and darker colour denotes proteins that were predicted as plastid-targeted by our pipeline. We have clarified in supporting text 6.8 that we investigated our aminoacyl-tRNA synthetases for possible dual targeting to both plastid and mitochondria but found no evidence for it.

We have searched the K. brevis SP3 HARS sequence (CAMPEP-0189291366) by CD-search and note that the conserved domain (underlined) starts at residue 24 after the first predicted methionine (bold), which is inconsistent with the probable length a plastid-targeting sequence, and we have noted in the figure legend that this is likely to represent a false positive.

CAMPEP_0189291366_Karenia-brevis-SP3-20130916

SWLVLLAFALTTPGPVVAVSATILRGLLVGLQRPCAAALRLSCCAATRALPLPGASELGSRFAAAAASSAR__M__GKEGKKKEDGKKKKDETKTEKLIGLEPPSGTRDFFPAEMRQQRYIFNKFRETANLYGFQEYDAPVLEHQELYIRKQGEEITDQMYSFDDKEGAKVTLRPEMTPTLARMVLNLMRVETGEMAAQLPLKWFSIPQCWRFETTQRGRKREHYQWNMDIVGVTSIYAEAELLSAICNFFESVGITSKDVGLRVNSRKVLNAVTKLAGVPDDRFAETCVIIDKLDKIGAEAVKTEMREKIGLPEEVGERIVKATGAKSLEEFADLAGVGQNNPEVLELKHLFELAEDYGYGDWLIFDASVVRGLGYYTGVVFEGFDRAGVLRAICGGGRYDRLLTKFGSPKEIPCVGFGFGDCVIAELLKEKGVTPSLPEHIDFVVAAFNSEMMGKAMNAARRLRLGGKSVDIFTEPGKKVGKAFNYADRVGADMVAFIAPDEWAKGLVRIKALRMGQDVPDDQKQKDVPLEDLANVDSYFGLAPAAAPVMSAAPAASTVKSTAPALAVPAAAKASAPKAAAPSGTGADVEAFLVDHPYVGGFRPCARDRTLFDELRLTSGRPSTPALGRWYDHIDSFPAVVRASWC

The green HARS sequences (including that of Karenia brevis SP1) in contrast typically have conserved domains starting after residues 50-60, and are likely to be genuinely plastid-targeted. Reflecting that the automated prediction approach used within our dataset may contain other such false positive results (c.f., Fig. S18), we have chosen for tree-sorting and pathway reconstruction analyses to only consider genes in which we can identify plastid-targeted homologues of the same inferred phylogenetic origin in at least two distinct Kareniacean genera (Figs. 2, 3).

For the Karlodinium micrum TARS sequence we have identified a second TARS sequence (CAMPEP_0200847158) that is of apparent dinoflagellate origin and lacks a credible targeting sequence, and have updated the tree accordingly.

In the case of heme oxygenases, we are convinced that (at least) two paralogs of distinct origins are indeed plastid targeted. The presence of multiple copies of this enzyme has been noticed in other organisms including some plants (e.g., Dammeyer and Frankenberg-Dinkel, Photochemical & Photobiological Sciences, 2008) and may be reflective of functional specialization or regulation / expression under different conditions. We have discussed this in the supporting text 6.1: “Two evolutionarily distinct versions of the biliverdin-producing haem oxygenase seem to be present …the specific metabolic functions of the green- and haptophyte-like haem oxygenases in the fucoxanthin plastid await experimental characterisation.” (lines 52-58).

Reviewer #3 (Significance (Required)):

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This study by Novak Vanclova et al. provide new transcriptome datasets from multiple species in kareniacean dinoflagellates including harmful and toxic species. Their transcriptome datasets would help understand their biology, evolution, and ecology. The authors also provide a program that predicts plastid proteomes in those dinoflagellates, which would be useful for future studies to focus on kareniacean dinoflagellate plastids, after further refinement. The most important aspect of this study is that many plastid-targeted proteins might be derived from a particular haptophyte lineage, although it is still not sure whether they are derived from LGTs or EGTs. Phylogenetic analyses performed in this study should be improved by adding some plastid genomes, in order to gain more conclusive results. In addition to methods, interpretation of the current results and proposals on plastid evolution should be toned-down.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

Although there are technical issues, this study improves our conceptual understanding the plastid proteome evolution in Kareniacean dinoflagellates. The plastid proteomes are comprised of proteins with more various origins in those dinoflagellates, suggesting more complex plastid proteome evolution than previously thought.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This study seems to be "basic research".

Please 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.

algal evolution, eukaryotic evolution, mitochondrial metabolisms, plastid metabolisms, phylogenomics

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript entitled "Divergent and diversified proteome content across a serially acquired plastid lineage" by Novak Vanclova et al. proposes the origin and evolution of plastids in kareniacean dinoflagellates. The authors generated new transcriptome data from Karenia mikimotoi, Karenia papilionacea, Karlodinium micrum, Karlodinium armiger, and Takayama helix. Combining them to the previously published transcriptome data from kareniacean dinoflagellates, they constructed the pan-kareniacean transcriptome library. They surveyed plastid-targeted protein-coding transcripts in the dataset, and consequently they estimated ~14.5% of the transcriptome data were of plastid-targeted ones. Of them, 65-80% were derived from a peridinin-containing dinoflagellate ancestor while ~15% were derived from EGTs from a haptophyte endosymbiont of the current plastid origin. By using the plastid-targeted transcript dataset, they investigated 1) origins of the plastid-targeted protein-coding transcripts by single gene-trees, 2) the plastid origin and evolution by the multigene dataset of 22 conserved plastid-targeted protein-coding transcripts and of 3) plastid genome-derived transcripts, 4) plastid functions, 5) diversity of plastid-targeted signals in kareniacean dinoflagellates, and 6) the distributions of kareniacean species by using the Tara Oceans database. On the basis of their results, they proposed many hypotheses regarding kareniacean dinoflagellate evolution, such as i) the chrysochromulinales-origin of the plastids, ii) more recent acquisition of the plastid than previously thought, iii) a plastid replacement within kareniaceae evolution, iv) the strict selection of signal peptides but non-conserved transit peptides in the kareniacean plastid-targeted proteins, and v) correlated or non-correlated distribution patterns of kareniaceaen dinoflagellates to specific haptophyte lineages.

Although their proposals are interesting, I have many concerns to be addressed. Especially, their analyses on which the above proposals are based seem to be still preliminary and inconclusive. To support their proposals more confidently, I also suggest some additional analyses.

Major comments

1. seemingly inconsistency between the authors' claims The most striking is inconsistency of the authors' claims proposed in this manuscript. Their proposals include a) the common ancestor of kareniaceans has not possessed a fucoxanthin plastid but the plastid has been acquired more recently, b) an ancestor of Takayama and Karlodinium has gained a fucoxanthin plastid from a (chrysochlomulinales) haptophyte, c) an ancestor of Karenia has gained a fucoxanthin plastid from Karlodinium.

However, they also demonstrate a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama. If I understand correctly, "a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama" would seemingly be inconsistent to and challenge two of the authors' claims: no haptophyte-derived plastid in the common ancestor of kareniacean dinoflagellates and a Karlodinium-to-Karenia plastid transfer (Fig. 7). If the Karenia plastid is derived from Karlodinium, I have no idea why haptophyte-derived plastid proteome of Karenia is larger than that of Karlodinium. After the plastid acquisition in Karenia, Karenia might have gained more genes for plastid-targeted proteins from haptophytes by LGTs. If this is true, many single gene trees would suggest different origins of plastid-targeted proteins between Karenia and Karlodinium/Takayama. Can we see it in the single gene analyses? I would like authors to rationalize the inconsistency in the main text. 2. Signal peptide prediction I think the modified ASAFind would be greatly helpful for future studies on automatic prediction of plastid proteomes in kareniacean dinoflagellates. However, I found no data on selection criteria for the signal peptide prediction program SignalP5.0 used. I believe such data would be very important to interpret the previously published paper by Gruber et al. in which prediction methods for plastid-targeting sequences are compared to each other to see how sensitively and specifically they can capture the plastid proteomes.

Gruber et al. 2020. Comparison of different versions of SignalP and TargetP for diatom plastid protein predictions with ASAFind.

According to Gruber et al. (2020), signalP5.0 is not suitable for prediction of signal peptides for diatoms, in consistent with the authors' claim for kareniacean dinoflagellates. This inconsistency would be difference of the nature in signal peptides between diatoms and kareniacean dinoflagellates. Even if so, it would be useful to see quantitatively how much different their signal peptides are in terms of their suitable prediction programs.

I also have a concern about use of the combination of PrediSI and ChloroP, combination which is suitable for the plastid proteome prediction in Euglena gracilis. The authors should rationalize why the method for Euglena plastids can be applicable without any modification to the plastid proteome prediction in kareniacean dinoflagellates. Although Euglena plastids are enclosed by three membranes, kareniacean plastids are by four. Therefore, from the side of molecular mechanisms in protein import, the method suitable for Euglena plastids is not necessarily suitable for kareniacean dinoflagellate plastids. By using PrediSI and ChloroP, they detected additional "candidate plastid proteomes" including several proteins not detectable by SignalP5.0 and the modified ASAFind. That seems great. However, they did not seem to consider false positives since there is no mention on it. Although the additional candidates predicted by PrediSI and ChloroP included true plastid proteins of kareniacean dinoflagellates, many might not be. Nevertheless, the authors suggest 7.5 to 14.5% in K. micrum and K. brevis, respectively, are of plastid-targeted ones. I am so afraid if the proportions would be highly overestimated due to false positives by PrediSI and ChloroP. To rationalize the use of PrediSI and ChloroP, the authors should show sensitivity and specificity by quantitative analyses with a benchmark dataset. 3. Origin and evolution of kareniacean plastids The authors suggest the chrysochromulinales origin of the kareniacean dinoflagellate plastids and the Karlodinium-to-Karenia plastid transfer, on the basis of phylogenetic analyses using the concatenated datasets with the 22 conserved plastid-targeted proteins and with plastid-genome derived transcripts. It is very interesting that those plastid-targeted proteins in kareniacean dinoflagellates might be phylogenetically closely related to chrysochromulinales haptophyte I have suggestions on the analyses and interpretation

As the 22 analyzed genes are nuclear-encoded plastid targeted genes, they are a quite small portion of entire plastid proteins. I am not convinced by that evolution of the small number of genes reflects evolution of fucoxanthin plastids of which proteomes are comprised of >1000 proteins. How many genes for haptophyte-derived plastid-targeted proteins suggest the monophyly of kareniaceaen dinoflagellates and chrysochromulinales haptophytes should be investigated by, for example, a coalescence-based analysis such as Astral for all the detected haptophyte-derived plastid-targeted proteins including the 22 genes. This is because the monophyly could be reconstructed only by one or few, limited number of proteins even if the concatenated dataset is analyzed.

Relevant to this, plastid-targeted proteins derived from a peridinin-containing ancestor might still have phylogenetic signals of host evolution. I am interested in whether such analyses with peridinin plastid-derived plastid-targeted proteins reconstruct Takayama and Karlodinium as monophyletic but separate Karenia from them, as suggested in the phylogenomics with non-plastid proteins.

For the phylogenetic analysis of plastid genome-derived transcripts, I might be wrong, but I could not find any information on dataset sizes (i.e., the numbers of sites) and evolutionary models for the analyses in the main text nor supplementary document. Although one may see the dataset sizes when looking at the original datasets in the supplementary files, such information is substantial and thus is to be described in the materials and methods section. I am afraid if this analysis was performed with a small dataset size. I would like to know total lengths of the concatenated sequences and especially that for Takayama. The phylogenetic position of Takayama, distantly related to the other kareniaceans, in this tree might be caused by a larger portion of gaps in the Takayama sequences than in the other kareniaceans. Moreover, due to lack of the plastid genome sequence of Takayama, no one could confidently identify plastid genome-derived transcripts: some of those could be derived from second, nuclear copies that might be pseudogenes. Otherwise, even if they are plastid-derived, no one can evaluate whether they are transcripts after or prior to RNA editing. I am afraid if the dataset used is comprised of a mixture of edited and non-edited sequences in kareniacean sequences. Either of sequences after or prior to RNA editing, latter of which are identical with DNA sequences, should be consistently used for the phylogenetic analysis. In any case, the plastid genomes are necessary for this analysis, and the authors can easily obtain them by DNAseq as they have the cultures.

In addition, although I might be wrong, the phylogenomic analysis for plastid-encoded transcripts might be performed with their nucleotide sequences according to the figure title and legend of Figure S4 mentioning "nucleotide phylogenetic matrix" and the file name "plastid_coded_nt_concatenation_files.tar". If so, translated amino acid sequences should be subjected to phylogenetic analysis, to avoid a well-known artifact that is caused by saturation of substitutions at the 3rd codon. 4. Duplication of an ATP synthase subunit Duplication and relocation of ATP synthase subunit delta seems interesting. In figure S6.4.1, could you clarify why the possible extensions containing signal peptides lack the initiation methionine at N-termini? I wonder they are 5′ UTRs but artifactually detected as signal peptides, if they all indeed lack Met. To evaluate this point, I recommend 5′ RACE followed by transformation into a model organism as performed in previous studies by some of the authors. 5. Comparison of transit peptides Amino acid compositions in transit peptides would vary when targeted compartments are different. In complex plastids, there are functionally distinct compartments: lumen, stroma, periplastidal compartment (PPC). Comparison should therefore be conducted separately for lumen-targeted, stroma-targeted and PPC-targeted proteins in order to claim their transit peptides are not conserved. 6. RDS never possessed a stable fucoxanthin plastid Although the authors cite Hehenberger et al. 2019 for that RDS never possessed a stable fucoxanthin plastid, as far as I know, that paper seems not to mention it. Could you let me know where that is mentioned in the paper? Hehenberger et al. instead proposed the retention of non-photosynthetic peridinin plastid. Regardless of whether Hehenberger et al. mentioned or not, Novák Vanclová et al. propose that RDS never possessed a stable fucoxanthin plastid because, if I understand correctly, they detected no or few haptophyte-derived RDS genes for plastid-targeted proteins of which origins are shared with those of Karlodinium, Karenia, and Takayama. What about the possibility that the last common ancestor of kareniacean dinoflagellates possessed a fucoxanthin plastid in addition to peridinin plastid followed by almost complete losses of those haptophyte-derived genes after loss of a fucoxanthin plastid in evolution leading to RSD? Free living eukaryotes were appeared to have lost a plastid in recent studies and they have only a few or no genes showing evidence of a plastid previously retained. We cannot rule out that an ancestor of kareniacean dinoflagellates possessed both of peridinin and fucoxanthin plastids, as the authors mention in the main text, and either plastid was inherited to each lineage by differential losses. Accordingly, I would say Fig. 7 is a too much strong proposal as alternative hypotheses are still present. They should be introduced equally. 7. rRNA copy numbers in dinoflagellates It is known that the rRNA gene copy number varies among populations or strains in dinoflagellates; some possess several dozens of times as many rRNA gene copies as others (Galluzzi et al. 2010). Is it informative to see the ocean wide rRNA gene amplicon data for the kareniacean dinoflagellates? The numbers of rRNA gene-derived reads would not necessarily reflect the cell abundance of dinoflagellates.

Galluzzi et al. 2010. Analysis of rRNA gene content in the Mediterranean dinoflagellate Alexandrium catenella and Alexandrium taylori: implications for the quantitative real-time PCR-based monitoring methods. J Appl Phycol 22:1-9

Minor points

1. the dataset size for the 241 protein-based host phylogeny should also be described in the main text.
2. The authors mention in Discussion "Thus, our results illuminate the mechanistics of a fundamental process that may under pin vast tracts of chloroplast evolution". If I understand correctly, I think this is based on "shopping bag model" when considering plastid replacements in dinoflagellates. It is helpful to add more details to clarify why the authors would like to claim so. "Chloroplast" should be replaced with "plastid".
3. Supplementary document S6.6 I found the term nitrogen fixation, but should this be replaced with "nitrogen assimilation"?
4. Figure S5 For those LGTs, all the trees should be shown in supplementary text as they are only 11 or 12 trees. Especially, please add the chlorophyllide b reductase and chlorophyllase in the figure.
5. References I am not picky about a format of the reference list, but I think it should be consistent throughout the list. I recommend adding journals, volumes, and pages precisely for cited papers. I found lack of them at least in Novak Vanclova et al. and Pierella Karlusich et al.
6. Figures In figure 3, I strongly recommend adding RDS data, while distinguishing them by another color if they are derived from different origins from those of Karenia, Karlodinium, and Takayama. This would make the authors claim clearer that there are few haptophyte-derived genes for plastid targeted proteins of which origins are shared with those of the other kareniacean dinoflagellates. In figures S5.1-2 showing LGTs, I found two paralogs of kareniacean dinoflagellates. What does "CP" mean? If "CP" means ChloroPlast-targeted, both paralogs of K. brevis in HARS and those of K. micrum are of plastid-targeted in TARS and they do not have cytosolic ones. I am afraid if these cases are caused by false positives of detection for plastid-targeted proteins by PredSI and ChloroP. Similarly, in figure S5.4, I found two distant paralogs of heam oxygenase in the tree and the taxon names for both types in kareniaceans include "CP." Are both targeted to the plastids or of false positives?

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This study by Novak Vanclova et al. provide new transcriptome datasets from multiple species in kareniacean dinoflagellates including harmful and toxic species. Their transcriptome datasets would help understand their biology, evolution, and ecology. The authors also provide a program that predicts plastid proteomes in those dinoflagellates, which would be useful for future studies to focus on kareniacean dinoflagellate plastids, after further refinement. The most important aspect of this study is that many plastid-targeted proteins might be derived from a particular haptophyte lineage, although it is still not sure whether they are derived from LGTs or EGTs. Phylogenetic analyses performed in this study should be improved by adding some plastid genomes, in order to gain more conclusive results. In addition to methods, interpretation of the current results and proposals on plastid evolution should be toned-down.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

Although there are technical issues, this study improves our conceptual understanding the plastid proteome evolution in Kareniacean dinoflagellates. The plastid proteomes are comprised of proteins with more various origins in those dinoflagellates, suggesting more complex plastid proteome evolution than previously thought.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This study seems to be "basic research".

Please 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.

algal evolution, eukaryotic evolution, mitochondrial metabolisms, plastid metabolisms, phylogenomics

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Referee #2

Evidence, reproducibility and clarity

This is a well done, detailed bioinformatic analysis of genomic and transcriptomic data from an important lineage of dinoflagellates that have undergone serial substitution of their plastid. On the whole I am enthusiastic about the paper; it presents valuable new insights, and is rigorously performed. However, I have to object to the way the term "proteome" is used in the paper; the manuscript is talking about the predicted proteome, not a measured proteome. This is something of a technical distinction, but it is an important one because the transcriptome and the proteome don't necessarily track each other, and there is little or no actual proteomic data available from dinoflagellates. We assume that transcript abundance has something to do with proteome abundance, but this is often violated. What this paper is really addressing is the potential proteome, because if a given gene is completely absent from the genome and the transcriptome we can be confident it will not be present in the proteome. The converse is not true. For this reason I feel it is important to be clear on the distinction. I would be satisfied in this regard by minor modifications, using the term "predicted proteome" in the title, and being more direct in the introduction about the distinction.

Overall the analyses are impressive. I do have to squirm a little when I see automated analyses generating alignments where the threshold is less than 75% gaps and at least 100 nucleotides aligned. I looked at the supplementary data and the figshare files and could not find the alignments themselves, so I don't know what fraction of the sequences are in that territory. Because phylogenetic analysis (as performed here) treats the alignments as an observation, and because the alignments include sequences with more than 50% gaps, it is entirely possible that some taxa, or even whole segments of the tree, are based on non-overlapping data.

Mind you, we have done similar analyses, and I don't think this invalidates the results, but it does open up the possibility of some dramatic artifacts. Consequently, I would recommend a) making the alignments available (or more obvious where to find them), and b) providing more detail on the alignments, including, if possible, to add a figure (probably in the supplementary data) that visualizes them. It is not given in the text itself, but according to the figure 2 caption there are 22 sequences thought to be "plastid late", and 241 in the pan-eukaryotic dataset. This is a scale that is feasible to put in a figure showing, for example, each aligned residue as a color and indels as grey. Such a figure is readable even when the individual residues are only a few pixels in size (less than a millimeter when printed). I also recommend describing the final alignments more fully in the text. Most of the summary statistics are presented in normalized form, and that can obscure patterns that come from poorly sampled taxa.

Better clarify on the characteristics of the alignments will make it easier to interpret the findings overall. Although this is critical to interpreting the results, gappy alignments are not uncommon in analyses of this sort, and setting that aside the analyses presented are comprehensive and thorough. The discussion does a good job of addressing the significance of the work, and potential causes of error are addressed adequately (aside from the matter of the alignments).

Significance

I find the paper to be exciting and important. These organisms are economically important, particularly as potential nuisance organisms, but also because of their role in primary productivity. They also have extremely complex evolutionary histories and similarly complex genomes. performing any bioinformatic analysis of these organisms is a substantial challenge because almost every gene exists in high copy number and with complex and often obscure patterns of homology. The manuscript brings forward these challenges, and makes a substantial step forward in elucidating the evolution of a group that is fascinating and important, but remarkably difficult to work with. I feel that it is an important analysis, and should be of interest to a broad audience.

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Referee #1

Evidence, reproducibility and clarity

The manuscript investigated the composition of the plastid proteomes of seven distantly-related kareniacean dinoflagellates, including newly-sequenced members of three genera (Karenia, Karlodinium, and Takayama). Using a custom plastid-targeting predictor, automatic single-gene tree building and phylogenetic sorting of plastid-targeted proteins for plastid proteome construction, the authors suggest that the haptophyte order Chrysochromulinales is the closest living relative of the fucoxanthin plastid donor. Interestingly, the N-terminal targeting sequences of kareniacean plastid signal peptides, reveal a high sequence conservation. Moreover, ecological and mechanistic factors are suggested that may have driven the endosymbiotic acquisition of the fucoxanthin plastid. Overall, this is a comprehensive and interesting analysis.

Other comments.

1. For analyses of N-terminal targeting sequences, why did the authors not consider to employ Predalgo as an additional tool?
2. Given the fact that peridinin or fucoxanthin pigment binding is in the focus of the paper, a more detailed introduction of the peridinin and fucoxanthin light-harvesting systems should be given.
3. The authors state "It is also possible that there has been a direct niche competition between the peridinin and fucoxanthin plastid that may have coexisted in the same host for a period of time with possibly different selective pressure on retention of their respective proteins based on their interaction with plastid-encoded components, e.g., extrinsic photosystem subunits not assembling correctly with their intrinsic haptophyte-like counterparts." It is tempting to ask, whether peridinin light-harvesting systems have left traces in the fucoxanthin plastid, possibly due to mistargeting of peridinin light-harvesting systems into the fucoxanthin plastid? Are some photosynthetic subunits "in-between" peridinin and fucoxanthin plastids?
4. Figure 3 is difficult to understand, e.g. for PSI and PSII which subunits are shown, why has PSI "more" contribution from dinoflagellates as compared to PSII?
5. Data shown in figure 4, is there experimental evidence for signal peptide cleavage site(s). Could these data been used to predict mature plastid targeted protein sequence?
6. The authors state "Partial Least Square (PLS) analysis shows a set of environmental variables (salinity, silicate, iron) positively correlated with abundances of both Karenia and Takayma and also haptophytes as a whole, but at the same time negatively correlated to Karlodinium (Figure S8), further illustrating that the latter genus is quite distant from the rest in its biogeographical pattern." How could this be interpreted in the light of the plastid proteomes?

Significance

The current manuscript gives insights into the endosymbiotic acquisition of the fucoxanthin plastids.

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General Statements

Ezrin, Radixin, and Moesin (ERMs) serve as crucial cytoskeletal linker proteins, connecting the actin cytoskeleton to the plasma membrane upon activation. ERMs are essential regulators of cell morphogenesis across every cell types reported so far, and have been implicated in vital cellular functions such as migration, and invasion. In our study, we discovered that ERMs are dispensable for the cortical organization of macrophages. In accordance with this surprising finding, we found that the migration of macrophages was not affected upon knock-out of the three ERMs. Our findings challenge the prevailing belief that ERMs universally regulate cortical organization. Instead, they indicate that the actin cortex of macrophages has evolved to possess a high degree of adaptability and plasticity, enabling these immune cells to function independently of ERM proteins.

We thank the editors of Review Commons that handled our manuscript and all three reviewers for their positive assessment of our manuscript and for their constructive suggestions.

Description of the planned revisions

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

In the manuscript, the authors systematically test the role of ERM proteins in macrophages using RNA silencing as well as the genetic knockout approaches. Previous studies have highlighted the fundamental importance of ERM proteins as structural and regulatory components of the cell cortex governing several essential functions such as the generation of surface features such as filopodia, maintenance of cortex-plasma membrane attachment, bleb retraction, cortical mechanics, and cell migration. The authors performed a series of experiments to comprehensively test each of these functions (including cell migration in 2D surface and 3D matrix in vitro, ex vivo on tumor implants, as well as in vivo) and found that none of these are significantly affected when ERM proteins are downregulated in macrophages. Overall, the paper is solid, the experiments are well-designed and conclusive, and the manuscript is written well.

We thank the reviewer for these encouraging comments.

I have no significant concerns with the study. My only experimental suggestion is related to a previously shown function of ERM protein in macrophages- the ERM proteins play an important role in phagosome maturation in macrophages (Defacque et al., EMBO, 2000; Lars-Peter et al., PNAS, 2006; Mylvaganam et al., Current Biology, 2021). It would be nice if authors could explore this phenotype in their perturbation system.

We thank the reviewer for this valuable suggestion. ERM proteins have indeed been proposed as important for macrophage phagocytosis. Importantly, their necessity for the early steps of this process is still debated, as conclusions differ depending on the cellular model used and the type of particle to be internalised (Erwig et al., PNAS USA 2006; Di Pietro et al., Sci. Rep. 2017; Gomez and Descoteaux, Biochem. Biophys. Res. Commun. 2018; Mu et al., Nat. Commun. 2018; Okazaki et al., J. Physiol. Sci. 2020). While the implication of ERMs in the early steps of phagocytosis remains controversial, there seems to be a consensus to implicate ezrin and moesin in phagosome maturation (Defacque et al. EMBO 2000 ; Erwig et al., PNAS USA 2006; Marion et al., Traffic 2011; Gomez and Descoteaux, Biochem. Biophys. Res. Commun. 2018).

We have already started addressing the ability of ERM-depleted macrophages to perform phagocytosis. In particular, we quantified the dynamics of phagocytosis of ovalbumin-coated or IgG-opsonized polystyrene beads, which did not reveal any difference between WT and ERM-depleted macrophages.

Proposed revision: We propose to include in the manuscript our quantification of IgG-coated and non-coated phagocytosis, and evaluate whether phago-lysosome fusion is delayed in ERM-depleted macrophages.

A minor concern with the study is, as the authors have already pointed out, that ERM proteins may still be required for some functions in macrophages under specific (environmental?) conditions. It is of course impossible to experimentally test all possible conditions that may involve ERMs, however, the authors should include a note on the hypothetical conditions that may require ERMs in macrophages. They should also discuss possible hypothetical reasons why macrophages may have evolved a cortex that does not rely on ERM proteins for specific functions. Overall, a more extended discussion on the role of ERM proteins (or the lack of them) in macrophages is required.

As suggested, in the revised version of the manuscript we will add a more extensive discussion of the role of ERM proteins in macrophages, and in particular the hypothetical conditions that might require their presence, as well as the reasons why macrophages have developed a particular cortex.

Reviewer #1 (Significance (Required)):

The manuscript is important on many accounts: The ERM proteins are considered crucial membrane-cytoskeletal linkers in many cellular systems. The study presents a surprising finding that cortical phenomena requiring membrane-cytoskeletal attachment do not essentially need ERM proteins providing a fundamental conceptual advance. The results from this study will also inform both experimental as well as theoretical studies of cortical organization and dynamics in the future. Furthermore, overexpressed mutant forms of ERMs are used as sensors as well as perturbing agents of cortical actin dynamics in many cellular systems. These utilities can now be further substantiated and if required, revised in light of the results from this study.

I am an immune cell biologist specializing in early lymphocyte activation and cytoskeleton dynamics.

We would like to thank the reviewer for pointing out the importance of our work for our understanding of the function of the cellular cortex, and for highlighting the fact that it may lead to a reinterpretation of the results obtained using ERM mutants.

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

Summary ERM proteins are known to play a central role in linking the cortical actin cytoskeleton with the plasma membrane, which is involved in regulating a diverse range of actin-rich membrane structures. The authors question the role that ERM proteins play in regulating cell shape changes and migration, specifically in macrophages. To test this, they designed an approach to systematically delete each ERM in macrophages - followed by the production of a triple-ERM ko line (tKO) using HoxB8 myeloid progenitor cells. The tKO line was subjected to a series of in vitro and in vivo experiments - all of which involve a series of imaging techniques to monitor membrane dynamics, protein subcellular organisation and cellular behaviours (e.g. rolling fraction, sticking fraction and chemotaxis). Their overall conclusion is that ERM are dispensable for macrophage membrane structures and migration.

General comments.

The experiments are very well executed. The manuscript in short demonstrates that the ERM proteins are dispensable for macrophage migration (both in 2D and 3D contexts), but there is very little beyond this work that points to what they might be doing instead. In this regard, given that the focus is exclusively on macrophage migration, the work comes across as quite specialised.

We thank the reviewer for appreciating the quality of our work.

We respectfully disagree to their assessment of the limited scope of our findings. Given the crucial importance of the migration of macrophages for so many of our body's functions, our findings will have a wide-ranging impact. Furthermore, and as acknowledged by Reviewers 1 and 3, we believe that the discovery that ERMs do not play a universal role in cortical mechanics and in cell migration, as hitherto believed, reaches a much wider scientific audience than that of the macrophage field. By proposing a unique research model (a triple KO for ERMs), our work allows to question many studies carried out with less direct molecular tools, such as the use of drugs or mutants of ERMs.

We acknowledge the fact that although our data convincingly demonstrate that the ERM proteins are dispensable for macrophage migration, they do not reveal alternative functions for these proteins. We agree that it could be interesting to search for alternative functions for ERM proteins in macrophages in future studies. However, we believe that such studies are out of the scope of the present manuscript.

The biggest concern I have is with the in vivo part. It should be noted that the work outlined in the manuscript does not actually address diapedesis, which is monitoring transmigration from the blood into tissue. Rolling and sticking do not define diapedesis. The experiments that the authors have conducted may have captured diapedesis events, but that very much depends on the length of time that the IVM was conducted. The authors would need to qualify their claims in this regard. Removing this work altogether would not lessen the impact, given that diapedesis is not shown. The work would therefore be very much in vitro/ex vivo.

We agree with the reviewer that, due to technical limitations, we only measured the rolling and sticking capacity of the +/-ERM cells and did not measure diapedesis directly. Following Reviewer's comments, we have thus modified the text of the manuscript and no longer use the term ‘diapedesis’ to describe our in vivo intravital imaging studies.

We also clarified the fact that we did not inject differentiated macrophages into the circulation, but macrophage precursors obtained by the treatment of progenitors with a 1 day treatment only (and not a 7 day treatment) with 20 ng/mL M-CSF.

Here, highlighted in yellow, are the changes to the text (in the Introduction, Results, Methods and Legends sections):

Introduction, p3:

“Surprisingly, we found that ERMs are dispensable for macrophages to migrate in diverse contexts, including in vitro 2D migration and 3D invasion of extracellular matrix, ex vivo tissue infiltration through healthy dermis and tumor tissue, and for the in vivo adhesion of macrophage precursors to an activated endothelium.”

Results, p6:

“ERM tKo cells without ezrin, radixin, and moesin exhibit no impairment in their ability to adhere to vascular endothelium in vivo and infiltrate the ear derma or fibrosarcoma.

To further investigate the migratory properties of ERM-deficient cells in vivo, we first assessed their ability to adhere to activated vascular endothelium into mice bearing a fibrosarcoma (Gui et al., 2018).”

Results, p8:

“Our study uncovered a surprising finding: ezrin, radixin and moesin are dispensable for key aspects of macrophage behavior, including the formation of lamellipodia and filopodia, the dynamics of membrane ruffles and podosomes, migration in vitro (in 2D or 3D matrices) and ex vivo (into dermis or tumor tissues) as well as for the in vivo adhesion of macrophage precursors to activated vascular endothelium).”

Methods, p14:

“In vivo analysis of adhesion to vascular endothelium with wide-field intravital microscopy”

And

“HoxB8-progenitors were directed towards monocyte/macrophage differentiation using a 1 day treatment with 20 ng/mL mouse M-CSF.”

Figure 4 legend, p33:

“Fig. 4: ERM tKO cells have no defect in adhesion to vascular endothelium in vivo and infiltrate tissues explants ex vivo

1. In vivo adhesion to vascular endothelium

Fibrosarcoma cells were injected into the flank of a mice. After a week, tumor was exposed for intravital microscopy, and the femoral artery of recipient mice was catheterized for injection of exogenous cells. Differentially labeled WT and TKO-ERM macrophage precursors were injected in the blood and their behaviour in tumor blood vessels was assessed by real-time imaging. Rolling fractions were quantified as the percentage of rolling cells in the total flux of cells in each blood vessel, and sticking fractions were quantified as the percentage of rolling cells that firmly adhered for a minimum of 30 seconds.”

Proposed revision: We propose to keep the results of the in vivo experiments in the manuscript, including the modifications proposed by the reviewer and listed above.

Specific questions

How sure are the authors that they are capturing these events in cremasteric venules?

As described in the Results and Methods section, these measurements were not captured in cremasteric venules but in fibrosarcoma tumour blood vessels, where we have previously demonstrated strong recruitment of circulating monocytes to infiltrate tumor tissue (Gui et al., Cancer Immunol. Res. 2018).

Is there any sign of cells being trapped in the microcirculation?

The diameter of the tumor blood vessels analysed is consistent with tumor post-capillary venules, and we have not seen cells trapped in these tumor blood vessels.

The reason for injecting macrophages intravenously is not explained.

We injected cells intravenously in order to compare their capacity to adhere to activated tumor blood vessels by intravital microscopy. This is now clarified in the corresponding result section (p6):

“For that purpose, one day differentiated wild-type or ERM-deficient cells were fluorescently labelled with two different cell trackers, mixed in a 1:1 ratio, and co-injected intra-arterially into recipient mice in order to analyse their behaviour in tumor blood vessels by intravital microscopy.”

Are these experiments modelling intravascular (patrolling) macrophages? Monocytes will typically differentiate into macrophages in tissue.

We again apologize for the lack of clarity. In these experiments, we did not inject fully differentiated (seven days) macrophages but progenitors directed towards monocyte/macrophage differentiation using a 1 day treatment with 20 ng/mL mouse M-CSF. We believe that these experiments model the adhesion/recruitment of monocytes by activated vascular endothelium in the tumor microenvironment.

The fact that the cells are able to "roll" and "stick" suggests that they have the complimentary cell adhesion molecules, although this is not addressed in the study.

We agree with the reviewer. Our intravital microscopy analyses indicate that the injected cells have the complementary cell adhesion molecules for firm adhesion to activated tumor blood vessels. Importantly, our data clearly demonstrate that the capacity of ERM-tKO cells to bind vascular endothelium in the tumor microenvironment is similar to that of WT cells (Fig. 4A).

Reviewer #2 (Significance (Required)):

The strength of the manuscript is based on the robust in vitro experiments, however such experiments are difficult to address in vivo - mainly because of the issue that macrophages (unless patrolling macrophages) are not a useful model to investigate for ivm experiments.

We thank the reviewer for recognizing the robustness of our in vitro experiments. We fully agree with the reviewer that the in vivo experiments are more challenging and that the behaviour of monocytes/(patrolling) macrophages is difficult to mimic in vivo. However, we believe that our intravital microscopy analyses are important because they demonstrate that ERM-tKO cells retain the capacity to bind firmly (sticking) to activated tumor blood vessels in vivo.

This would be of great interest to the macrophage field, which is quite limited in scope. An advancement in the field would be to learn what is taking over the role of ERM in macrophages. As such, this becomes a report with a series of experiments to confirm that ERM are not involved.

Again, we respectfully disagree with the reviewer, as this work goes against the dogma that ERMs are generally the most important mechanical links between the plasma membrane and the cytoskeleton. By clearly establishing that this is not the case in macrophages, cells whose importance for our immunity justifies the importance of their investigation, this study could make it possible to reconsider the functioning of the cellular cortex and the role of ERMs in other cellular systems.

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

Verdys and colleagues report an elegant study in which the authors describe that ERM proteins are dispensable for migrating monocyte-derived macrophages. The methods are adequate and the results support the conclusions.

We thank the reviewer for these very supportive comments.

Major points:

- Although the authors demonstrate, by multiple methods, the dispensability of ERM proteins in the migration of macrophages derived from monocytes, the role of these proteins must also be evaluated in the phagocytosis process (another relevant functional aspect of macrophages).

This is an excellent suggestion, which should make it possible to clarify the role of ERMs in this important function of macrophages.

ERM proteins have indeed been proposed as important for macrophage phagocytosis. Importantly, their necessity for the early steps of this process is still debated, as conclusions differ depending on the cellular model used and the type of particle to be internalised (Erwig et al., PNAS USA 2006; Di Pietro et al., Sci. Rep. 2017; Gomez and Descoteaux, Biochem. Biophys. Res. Commun. 2018; Mu et al., Nat. Commun. 2018; Okazaki et al., J. Physiol. Sci. 2020). While the implication of ERMs in the early steps of phagocytosis remains controversial, there seems to be a consensus to implicate ezrin and moesin in phagosome maturation (Defacque et al. EMBO 2000 ; Erwig et al., PNAS USA 2006; Marion et al., Traffic 2011; Gomez and Descoteaux, Biochem. Biophys. Res. Commun. 2018).

We have already started addressing the ability of ERM-depleted macrophages to perform phagocytosis. In particular, we quantified the dynamics of phagocytosis of ovalbumin-coated or IgG-opsonized polystyrene beads, which did not reveal any difference between WT and ERM-depleted macrophages.

Proposed revision: We propose to include in the manuscript our quantification of IgG-coated and non-coated phagocytosis, and evaluate whether phago-lysosome fusion is delayed in ERM-depleted macrophages.

• How is the activation of key downstream targets of ERM proteins involved in macrophage migration in KO models?_

This is a very pertinent question. However, while ERMs have been described as being downstream of several signalling pathways, their own downstream targets are unfortunately poorly documented and, to our knowledge, none are known in macrophages.

In different cellular contexts, it has been proposed that ERMs regulate PI3K (Gautreau et al. PNAS USA 1999), Ras (Sperka et al. Plos One 2011) or that they are involved in the initiation of protein translation (Briggs et al. Neoplasia 2012), but these results have not yet been confirmed and we believe they are outside the scope of this study.

During macrophage migration, we consider that their obvious main target is cortical actin, and demonstrate in this manuscript that the functional coupling between actin and the plasma membrane is not affected by full ERM knockout.

Reviewer #3 (Significance (Required)):

Advance: The present study fills a gap in the participation of ERM proteins in cell migration. The results obtained on the dispensability of these proteins in macrophage migration can pave avenues for identifying new processes and proteins associated with migration in this context.

Audience: The audience for this study is very broad.

We again thank the reviewer for recognising the importance of this work for the understanding of cell migration.

My expertise: I have expertise in cellular and molecular biology with a focus on processes associated with cancer. Among the numerous research fronts of the group led by me, we recently identified the EZR gene (which encodes the ezrin protein) as a prognostic marker and molecular target in acute leukemias.

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

In the revised version of the article, we have taken into account all relevant changes proposed by the reviewers. We modified the text of the manuscript and no longer use the term ‘diapedesis’ to describe our in vivo intravital imaging studies, and clarified the fact that we did not inject differentiated macrophages into the circulation, but macrophage precursors obtained by the treatment of progenitors with a 1 day treatment only (and not a 7 day treatment) with 20 ng/mL M-CSF.

Here, highlighted in yellow, are the changes to the text (in the Introduction, Results, Methods and Legends sections):

Introduction, p3:

“Surprisingly, we found that ERMs are dispensable for macrophages to migrate in diverse contexts, including in vitro 2D migration and 3D invasion of extracellular matrix, ex vivo tissue infiltration through healthy dermis and tumor tissue, and for the in vivo adhesion of macrophage precursors to an activated endothelium.”

Results, p6:

“ERM tKo cells without ezrin, radixin, and moesin exhibit no impairment in their ability to adhere to vascular endothelium in vivo and infiltrate the ear derma or fibrosarcoma.

To further investigate the migratory properties of ERM-deficient cells in vivo, we first assessed their ability to adhere to activated vascular endothelium into mice bearing a fibrosarcoma (Gui et al., 2018). For that purpose, one day differentiated wild-type or ERM-deficient cells were fluorescently labelled with two different cell trackers, mixed in a 1:1 ratio, and co-injected intra-arterially into recipient mice in order to analyse their behaviour in tumor blood vessels by intravital microscopy.”

Results, p8:

“Our study uncovered a surprising finding: ezrin, radixin and moesin are dispensable for key aspects of macrophage behavior, including the formation of lamellipodia and filopodia, the dynamics of membrane ruffles and podosomes, migration in vitro (in 2D or 3D matrices) and ex vivo (into dermis or tumor tissues) as well as for the in vivo adhesion of macrophage precursors to activated vascular endothelium).”

Methods, p14:

“In vivo analysis of adhesion to vascular endothelium with wide-field intravital microscopy”

And

“HoxB8-progenitors were directed towards monocyte/macrophage differentiation using a 1 day treatment with 20 ng/mL mouse M-CSF.”

Figure 4 legend, p33:

“Fig. 4: ERM tKO cells have no defect in adhesion to vascular endothelium in vivo and infiltrate tissues explants ex vivo

1. In vivo adhesion to vascular endothelium

Fibrosarcoma cells were injected into the flank of a mice. After a week, tumor was exposed for intravital microscopy, and the femoral artery of recipient mice was catheterized for injection of exogenous cells. Differentially labeled WT and TKO-ERM macrophage precursors were injected in the blood and their behaviour in tumor blood vessels was assessed by real-time imaging. Rolling fractions were quantified as the percentage of rolling cells in the total flux of cells in each blood vessel, and sticking fractions were quantified as the percentage of rolling cells that firmly adhered for a minimum of 30 seconds.”

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Referee #3

Evidence, reproducibility and clarity

Verdys and colleagues report an elegant study in which the authors describe that ERM proteins are dispensable for migrating monocyte-derived macrophages. The methods are adequate and the results support the conclusions.

Major points:

• Although the authors demonstrate, by multiple methods, the dispensability of ERM proteins in the migration of macrophages derived from monocytes, the role of these proteins must also be evaluated in the phagocytosis process (another relevant functional aspect of macrophages).
• How is the activation of key downstream targets of ERM proteins involved in macrophage migration in KO models?

Significance

Advance: The present study fills a gap in the participation of ERM proteins in cell migration. The results obtained on the dispensability of these proteins in macrophage migration can pave avenues for identifying new processes and proteins associated with migration in this context.

Audience: The audience for this study is very broad.

My expertise: I have expertise in cellular and molecular biology with a focus on processes associated with cancer. Among the numerous research fronts of the group led by me, we recently identified the EZR gene (which encodes the ezrin protein) as a prognostic marker and molecular target in acute leukemias.

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Referee #2

Evidence, reproducibility and clarity

Summary

ERM proteins are known to play a central role in linking the cortical actin cytoskeleton with the plasma membrane, which is involved in regulating a diverse range of actin-rich membrane structures. The authors question the role that ERM proteins play in regulating cell shape changes and migration, specifically in macrophages. To test this, they designed an approach to systematically delete each ERM in macrophages - followed by the production of a triple-ERM ko line (tKO) using HoxB8 myeloid progenitor cells. The tKO line was subjected to a series of in vitro and in vivo experiments - all of which involve a series of imaging techniques to monitor membrane dynamics, protein subcellular organisation and cellular behaviours (e.g. rolling fraction, sticking fraction and chemotaxis). Their overall conclusion is that ERM are dispensable for macrophage membrane structures and migration.

General comments.

The experiments are very well executed. The manuscript in short demonstrates that the ERM proteins are dispensable for macrophage migration (both in 2D and 3D contexts), but there is very little beyond this work that points to what they might be doing instead. In this regard, given that the focus is exclusively on macrophage migration, the work comes across as quite specialised.

The biggest concern I have is with the in vivo part. It should be noted that the work outlined in the manuscript does not actually address diapedesis, which is monitoring transmigration from the blood into tissue. Rolling and sticking do not define diapedesis. The experiments that the authors have conducted may have captured diapedesis events, but that very much depends on the length of time that the IVM was conducted. The authors would need to qualify their claims in this regard. Removing this work altogether would not lessen the impact, given that diapedesis is not shown. The work would therefore be very much in vitro/ex vivo.

Specific questions

How sure are the authors that they are capturing these events in cremasteric venules? Is there any sign of cells being trapped in the microcirculation? The reason for injecting macrophages intravenously is not explained. Are these experiments modelling intravascular (patrolling) macrophages? Monocytes will typically differentiate into macrophages in tissue. The fact that the cells are able to "roll" and "stick" suggests that they have the complimentary cell adhesion molecules, although this is not addressed in the study.

Significance

The strength of the manuscript is based on the robust in vitro experiments, however such experiments are difficult to address in vivo - mainly because of the issue that macrophages (unless patrolling macrophages) are not a useful model to investigate for ivm experiments.

This would be of great interest to the macrophage field, which is quite limited in scope.

An advancement in the field would be to learn what is taking over the role of ERM in macrophages. As such, this becomes a report with a series of experiments to confirm that ERM are not involved.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript, the authors systematically test the role of ERM proteins in macrophages using RNA silencing as well as the genetic knockout approaches. Previous studies have highlighted the fundamental importance of ERM proteins as structural and regulatory components of the cell cortex governing several essential functions such as the generation of surface features such as filopodia, maintenance of cortex-plasmamembrane attachment, bleb retraction, cortical mechanics, and cell migration. The authors performed a series of experiments to comprehensively test each of these functions (including cell migration in 2D surface and 3D matrix in vitro, ex vivo on tumor implants, as well as in vivo) and found that none of these are significantly affected when ERM proteins are downregulated in macrophages. Overall, the paper is solid, the experiments are well-designed and conclusive, and the manuscript is written well.

I have no significant concerns with the study. My only experimental suggestion is related to a previously shown function of ERM protein in macrophages- the ERM proteins play an important role in phagosome maturation in macrophages (Defacque et al., EMBO, 2000; Lars-Peter et al., PNAS, 2006; Mylvaganam et al., Current Biology, 2021). It would be nice if authors could explore this phenotype in their perturbation system.

A minor concern with the study is, as the authors have already pointed out, that ERM proteins may still be required for some functions in macrophages under specific (environmental?) conditions. It is of course impossible to experimentally test all possible conditions that may involve ERMs, however, the authors should include a note on the hypothetical conditions that may require ERMs in macrophages. They should also discuss possible hypothetical reasons why macrophages may have evolved a cortex that does not rely on ERM proteins for specific functions. Overall, a more extended discussion on the role of ERM proteins (or the lack of them) in macrophages is required.

Significance

The manuscript is important on many accounts: The ERM proteins are considered crucial membrane-cytoskeletal linkers in many cellular systems. The study presents a surprising finding that cortical phenomena requiring membrane-cytoskeletal attachment do not essentially need ERM proteins providing a fundamental conceptual advance. The results from this study will also inform both experimental as well as theoretical studies of cortical organization and dynamics in the future. Furthermore, overexpressed mutant forms of ERMs are used as sensors as well as perturbing agents of cortical actin dynamics in many cellular systems. These utilities can now be further substantiated and if required, revised in light of the results from this study.

I am an immune cell biologist specializing in early lymphocyte activation and cytoskeleton dynamics.

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Reply to the reviewers

We would like to thank all reviewers for their careful evaluation of our manuscript and their thoughtful feedback, which we could use to improve its quality significantly.

Reviewer #1 (Evidence, reproducibility and clarity):

Summary: This study addresses the problem of what is the optimal ribosome composition in terms of relative RNA and protein content, to ensure optimal growth rate and minimal energy waste. The RNA-world hypothesis suggests that primitive ribosomes were RNA-only objects, and in fact this would appear to be very advantageous from an energetic point of view, since RNA synthesis requires a much lower energy expenditure than protein synthesis. Yet a large fraction of present-day ribosome mass is protein, ranging from 30% to nearly 70% depending on the organism. The authors hypothesize that one of the main functions of ribosomal proteins is to stabilize the RNA and to protect it against degradation. According to their idea, the fast degradation of a protein-free rRNA would offset the energetic advantage given by its cheaper synthesis. To test the hypothesis, they developed a mathematical model whereby to evaluate the optimal ribosome composition under a number of different conditions.

Major comments: The paper is well-written and very readable. I am not an expert of mathematical modelling, so I cannot go into the details of the model presented. As a biologist, I can say that the conclusion arrived at are reasonable and well-justified.

We thank the reviewer for the positive evaluation.

Perhaps the point of view is rather narrow, since ribosomal proteins are known to be important not only for RNA protection and ribosome stability, but also to ensure the accuracy of decoding and, in certain contexts, to allow the ribosomes to interact with other cellular ligands. The authors make only very slight reference to these questions, so it would be worthwhile to further comment on them.

Thank you for your suggestion. To address it, we expanded the discussion as follows:<br /> "Finally, we need to consider that ribosomal proteins may play other roles in the cells, especially in eukaryotic organisms. Ribosomal proteins participate in translation processes, for example, binding of translation factors, release of tRNA, and translocation. They may also affect the fidelity of translation (Nikolay et al., 2015). Furthermore, they play roles in various cellular processes such as cell proliferation, apoptosis, DNA repair, cell migration and others (Kisly and Tamm, 2023). These additional functions might have conferred evolutionary fitness advantages. Nevertheless, the primary role of ribosomal proteins seems to be stabilization and folding of rRNA (Nikolay et al., 2015; Kisly and Tamm, 2023)."

Furthermore, their explanation of why ribosome composition should be so different in different organisms (e.g. protein-poor bacterial ribosomes versus protein-rich archaeal ones) is not entirely convincing. For instance, they suggest that archaea may have protein-richer ribosomes than bacteria because they live in extreme environments, thus needing a further aid to stabilize the organelle. While this may be a factor, one must point out that non-extremophilic archaea (e.g. methanogens) have protein-rich ribosomes, making it obvious that other factors must be at play.<br />

We appreciate the reviewer's feedback. Ribosome composition is indeed complex and influenced by various factors. While extreme environments (may) contribute to protein-rich ribosomes in archaea, it's important to note that not all archaea share this characteristic. Some, like Halobacteriales, Methanomicrobiales, and Methanobacteriales, have ribosomes with protein content similar to bacteria.

Furthermore, there are species in both archaea and bacteria with low protein content in their ribosomes despite extreme habitats. This suggests that alternative strategies, possibly involving specific sequence variants in the rRNA (Nissley et al., 2023), play a role in stabilizing ribosomes. In our model, these findings would correspond to a decreased kdegmax. However, these sequence variants are not universal.

Amils et al. (1993) suggest that protein-rich ribosomes in archaea are (more) ancient and proteins may have been lost in some species, possibly to favor higher growth rates (and in agreement with our theoretical analysis). An intriguing avenue for further research would be a phylogenetic analysis of archaeal evolution to investigate the emergence of different ribosome compositions.

To address your concerns, we added the following paragraph to the discussion:<br /> "Additionally, some extremophilic organisms, such as the bacteria Chloroflexus aurantiacus or Fervidobacterium islandicum, exhibit ribosomes with lower protein content (approximately 40%) compared to extremophilic archaea (50%). It has been suggested that protein-rich ribosomes can be traced back to the oldest phylogenetic lineages, with some ribosomal proteins being lost over time (Amils et al., 1993; Acca et al., 1993). Organisms with lower protein content in their ribosomes may have evolved alternative strategies to thrive in extreme conditions. Examples of such strategies include the presence of specific rRNA sequence variants or base modifications, as recently discussed by Nissley et al. (2023).

Moreover, certain archaeal species, such as those from Methanobacteriales or Halobacteriales, have transitioned to milder environmental conditions and subsequently shed unnecessary ribosomal proteins (Acca et al., 1993; Amils et al., 1993).

To gain a comprehensive understanding of ribosome evolution in response to changing conditions, a thorough phylogenetic analysis is warranted. This analysis should be complemented by measurements of growth rate, translation rate, RNA degradation rate, among other parameters, to delineate the order of protein loss or gain, and the emergence of sequence variations and base modifications."

Minor comments: none in particular. Referencing is adequate, text is clear and the figures are clear and well-organized.

Thank you.

Reviewer #1 (Significance):

As I stated above, the main weakness of this study may be that it concentrates overwhelmingly on a single problem, i.e. the energetic cost of adding proteins to an RNA-only ancestral ribosome. On the other hand, this is a question seldom addressed when talking about ribosome composition, which indeed makes this paper valuable and interesting. The authors expand and advance a previous study of the same kind (to which they make ample reference).

Although rather specialized, I think this paper, in its general conclusions, may be of interest to most of those working in the field of protein synthesis and ribosome evolution.

Referee's keywords: archaea, ribosome evolution, translation, translation initiation

Reviewer #2 (Evidence, reproducibility and clarity):

The authors explore a mathematical model to rationalize the variable RNA content in ribosomes across species. The mathematical model particularly considers the idea that the protein-to-RNA ratio in ribosomes emerges as a consequence of faster rRNA than r-protein synthesis coupled with a faster degradation of rRNA. This is an interesting analysis. The idea is well explained and the math of the model is overall well explained. Overall, I thus support publication of this analysis.

We thank the reviewer for the positive evaluation.

However, while reading the manuscript I was continuously wondering about two major aspects which, I suggest, should be considered more prominently in the text:

1. How clear is it that rRNA is more unstable than r-protein?
2. Why should the translation rate (the speed with which ribosomes assemble new proteins) not be highly dependent on the ribosome-to-protein ratio (with some intermediate ratio ensuring efficient synthesis and efficient translation?

Currently these points are considered briefly in the discussion part. I suggest that these points should at least be discussed more prominently in the introduction. I further appreciate any more detailed thoughts the authors have on these questions.

Finally, I think the discussion section would benefit strongly from a more detailed consideration of possible future experiments. Which data is needed to probe the idea? What types of experiments could be performed to probe the model.

We added a paragraph to the discussion with suggestions for experiments:<br /> "There are still many open questions about ribosome biogenesis and evolution. Our model could guide future experiments. There are a few studies that assessed the effect of individual rP deletions in E. coli, for example mutation in S10 increased RNA degradation (Kuwano et al., 1977), and mutation in L6 lead to disrupted ribosomal assembly (Shigeno et al., 2016). A systematic knock-out screen of all ribosomal proteins could be done (as in Shoji et al. (2011)), complemented with quantification of RNA degradation and misfolding.

In case of extremophilic organisms with protein-rich ribosomes, temperature sensitivity could also be assessed. We would expect that deletion of the extra proteins would cause growth defects only at high temperatures.

Furthermore, after removal of proteins from archaeal protein-rich ribosomes, laboratory evolution could be performed to see whether growth rate increases beyond wild-type.

Comprehensive datasets, akin to the work of Bremer and Dennis in 2008 for E. coli, should be generated for non-standard organisms by measuring various parameters such as transcription and translation rates, ribosome and RNAP activities, and other relevant factors.

Finally, as mentioned earlier, phylogenetic analysis or ribosome evolution across different species and environments could be done."

More detailed comments:

Regarding i: rRNA is pretty stable compared to other RNA types in the cell. The authors argue it is unstable. The specific question then seems to become how stable rRNA is compared to r-protein? Generally, proteins are also stable, but what data is available to support that r-proteins are more stable than rRNA?

While rRNA that is already integrated into a ribosome is stable, nascent RNA may be susceptible to degradation (Jain, 2018). It has been observed that even during exponential growth, some rRNA is degraded (Gausing, 1997; Jain 2018) and the degradation rate increases if ribosome assembly is delayed (Jain, 2018). This suggests that rRNA that is synthesized in excess cannot be stored and used later. Furthermore, when rRNA is overexpressed in excess of rPs, it is rapidly degraded (half life 15-70 min) (Siehnel and Morgan, 1985).

On the other hand, the turnover of proteins is negligible (Bremer and Dennis 2008), and most ribosomal proteins can exist in a free form without RNA. For example, under starvation/in stationary phase, rRNA is degraded, but most proteins are stable and can be reused later (Reier et al., 2022; Deutscher, 2003).

The precise mechanisms of the rRNA instability are not clear. The simplest explanation is that rRNA that is not protected by rPs is attacked by RNases. Another option is that rRNA without proteins is difficult to fold and can get trapped in misfolded states. These are then degraded as a part of quality control. The model developed in this paper allows for both of these mechanisms.

We added these references to the discussion:<br /> "In order to explain a mixed (RNA+protein) ribosome, we consider rRNA degradation in our extended model, thereby increasing the costs for RNA synthesis. While rRNA that is already integrated into a ribosome is stable, nascent RNA may be susceptible to degradation (Jain, 2018). Indeed, it has been experimentally observed that even at maximum growth rate, 10% of newly synthesized rRNA is degraded (Gausing, 1977), and the degradation rate increases if ribosome assembly is delayed (Jain, 2018). Furthermore, when rRNA is overexpressed in excess of rPs, it is rapidly degraded (Siehnel and Morgan, 1985). Due to the extremely high rates at which rRNA is synthesized, errors become inevitable, necessitating the action of quality control enzymes such as polynucleotide phosphorylase (PNPase) and RNase R to ensure ribosome integrity (Dos Santos et al., 2018). The absence of the RNases results in the accumulation of rRNA fragments, ultimately leading to cell death (Cheng and Deutscher, 2003; Jain, 2018).

In contrast, protein turnover is negligible (Bremer & Dennis, 2008), and most ribosomal proteins can exist without rRNA and can be reused (Reier et al., 2022; Deutscher, 2003). Therefore, we do not consider protein degradation in our model."

Regarding ii: Building on their model results, the authors rationalize the highly varying RNA-to-protein ratio in ribosomes across species. The model considers a non-varying rate with which ribosomes synthesize new proteins. This is briefly discussed in the discussion section. However, this appears to be a major assumption that, I think, should be stated clearly stated earlier in the text, including the abstract and introduction. Second, I wonder how the authors then rationalize variations in translation rate across species. Translation rates and the speeds with which ribosomes are varying strongly across species (indicated for example well by the change in the slope between ribosome content/rRNA and growth rate - slope in Fig. 2A). Why could the rRNA-to-protein ratio not be important in playing a role here?

We decided not to consider the effect of rRNA/protein ratio in ribosomes on translation rate mainly because it is not clear in what way it affects it. Proteins are better catalysts than rRNA. Yet, eukaryotic ribosomes which have higher protein content, have lower translation rates. For archaea and mitochondria, we were not able to find data but it is unlikely that the translation rates are faster because the growth rates are not faster.

We added a paragraph to the introduction that explains our assumption:<br /> "We focus on the primary role of ribosomal proteins, which is stabilizing rRNA (by preventing its degradation or misfolding).

Ribosome protein content might also affect other parameters, such as translation rate. Proteins are generally better catalysts than RNA (Jeffares et al., 1998), but the ribosome's catalytic core is formed by rRNA (Tirumalai et al., 2021) and operates at a relatively slow catalytic rate compared to typical enzymes. This suggests that there is little evolutionary pressure to increase the catalytic rate. Furthermore, ribosomes with the lowest protein content, like the E. coli ribosome, exhibit the highest translation rates (Bonven and Gulløv, 1979; Hartl and Hayer-Hartl, 2009; Bremer and Dennis, 2008). Therefore, we do not consider the impact on translation rate in this study."

And a sentence to the abstract:<br /> "In this study, we develop a (coarse-grained) mechanistic model of a self-fabricating cell and validate it under various growth conditions. Using resource balance analysis (RBA), we examine how the maximum growth rate varies with ribosome composition, assuming that all kinetic parameters remain independent of ribosome composition."

More minor point, but I was also not sure about the justification that ribosome mass is constant (line 111). The mass of an amino acid and a nucleotide is quite different. Why should overall mass matter, and not for example the number of amino acids and proteins. I think it also would be good here to motivate the assumption better early on instead of commenting on it in the discussion section.

Thank you for your suggestion. We agree with the reviewer that we should make our assumption of keeping the ribosome mass constant, which we used for simplicity, clearer from the beginning. Therefore, we have added the following statement to the introduction:<br /> "For simplicity, we assume a constant ribosome mass."

Reviewer #2 (Significance):

Protein synthesis by ribosomes is a major determinant of the rate with which microbes and other fast growing cells accumulate biomass. To better understand cell growth it is thus essential to better understand the makeup of ribosomes. Széliová et al present a mathematical model to entertain the idea that the varying RNA content in ribosomes across species is a consequence of RNA degradation. The model makes clear predictions which can guide future experiments.

Reviewer #4 (Evidence, reproducibility and clarity):

Summary

In this manuscript, Széliová et al. used a simple self-replicating cell model to study why the ribosome consists of both RNA and protein from an economic point of view. Their base model predicts an RNA-only ribosome, which is not surprising since the smaller RNAP has a higher turnover number compared to the larger ribosome. When rRNA instability is included, the model predicts an "RNA+Protein" ribosome. In particular, the predicted ribosome composition is comparable to the measured ribosome composition when strong cooperative binding of ribosomal proteins to rRNA is considered. The authors conclude that the maximal growth rate is achieved by the real ribosome composition when rRNA instability is taken into account.

Major comments:

1. The authors modeled the rRNA degradation rate as a function of the concentration of fully assembled ribosomes (equation 5). However, only partially assembled ribosomes are susceptible to RNase, and they make up only a small fraction of total ribosomes. The majority of ribosomes are fully assembled. In addition, the turnover number obtained from Fazal et al. (2015) and used here is the degradation rate of double-stranded RNA, not the fully assembled ribosomes, which have a stable tertiary structure. In my opinion, the rRNA degradation rate should be modeled as a function of the concentration of partially assembled ribosomes (i.e., pre-R in Figure 7) rather than the concentration of fully assembled ribosomes.

We agree with the reviewer that the way we model the process is not entirely biologically accurate. The problem is that even if we add the assembly intermediates, their concentration would be zero as they do not catalyze any reaction (similarly to the metabolites). Therefore, the degradation rate would also always be zero. Given the current modeling setup, the obvious proxy for the intracellular rRNA concentration is the rRNA concentration in the (assembled) ribosome, c_R*(1-x_rP).

1. Compared to the work by Kostinski and Reuveni (2020), the authors have made an improvement by avoiding the use of constant ribosome allocation to ribosomal protein (Φ_rP^R) and RNAP (Φ_RNAP^R), allowing these parameters to vary with predicted growth rates (by changing 𝑥_rP). This is indeed important, as bacteria are very likely to adjust these parameters in response to different growth conditions. However, certain other growth rate-dependent parameters are still treated as constants (or treated as nutrient-specific parameters) across predicted growth rates under given conditions. For example, experiments have shown that the fraction of active RNAP (f_RNAP^act) and the ribosome elongation rate (k_R^el) are growth rate-dependent (Bremer and Dennis, 1996). In contrast, when the authors predict the maximum growth rate by changing 𝑥_rP, f_RNAP^act and k_R^el are held constant regardless of the predicted growth rates.

The fraction of active RNAP (f_RNAP^act) was growth-rate dependent in all our simulations (see Table 2), only the fraction of active ribosomes (f_R^act) was kept constant according to Bremer and Dennis, 1996 & 2008.

We decided to keep the elongation rate (k_R^el) constant similar to Scott et al. 2010 (their explanation is in the supplementary material “Correlation [1] and the control of ribosome synthesis”).

We reran the simulations with variable k_R^el. It has no impact on the predictions of optimal ribosome composition. However, the linear dependence of RNA/protein ratio is less steep and predicts an offset at zero growth rate.

We added the results to the supplementary material and the following text to the results section (for the base model):<br /> "…the base model correctly recovers the well-known linear dependence of the RNA to protein ratio and growth rate (Scott et al. 2010), see Figure 2a, but not the offset at zero growth rate, since our model does not contain any non-growth associated processes and we assume constant translation elongation rate kelR as in Scott et al. (2010). At low growth rate, kelR decreases, most likely because of the lower availability of the required substrates (Bremer and Dennis, 2008; Dai et al., 2016). Interestingly, when we use variable kelR, we observe a nonzero offset (Appendix 1, Figure 2)."

and in a later section:<br /> "Using variable or constant kelR has no impact on the predicted optimal ribosome composition. As in the base model, variable kelR leads to predicted non-zero offset of RNA/protein ratio at zero growth rate (Appendix 1, Figure 6)."

1. _If amino acids or nucleotides are provided in the media, the cell does not have to synthesize all of them de novo. However, the model assumes that the cell always synthesizes all amino acids or nucleotides de novo for growth on growth on amino acid-supplemented media or on LB. This problem could in principle be solved by assuming very fast kinetics of the metabolic reactions in these media, but that should be discussed in the manuscript. Furthermore, why does the turnover number for EAA depend on the growth rate while that of ENT is constant?<br /> > _

We focused on the “enzyme” EAA because it forms a significant fraction of the proteome. However, for consistency, we now also made ENT turnover number depend on growth rate. It made no significant impact on the simulation results.

We agree with the reviewer that the model is currently very simplified and the enzymes ENT and EAA are used even in the media supplemented with AAs/NTs. However, these enzymes represent lumped pathways that aim to take into account not only AA/NT synthesis but also the different ‘nutrient efficiencies’ of the carbon sources (as in Scott et al. 2010). Therefore, to approximate these effects we increase the kcat of EAA (and now also ENT) with growth rate.

We added a paragraph to the results section to explain these simplifications:<br /> "We used parameters from E. coli grown in six different media. Three of them are rich media (Gly+AA, Glc+AA, LB) where amino acids (and nucleotides) are provided so cells only have to express the corresponding transporters instead of the synthesis pathways. In our model, the enzymes ENT and EAA represent lumped pathways for glycolysis and nucleotide / amino acid synthesis, and we only consider one type of transporter. Therefore, to model the changing `nutrient quality' of the different media (inspired by Scott et al. 2010), we assume that turnover numbers of EAA and ENT increase with growth rate."

1. All parameters related to transcription (RNAP) and translation (ribosome) used in this manuscript are adopted from Kostinski and Reuveni (2020), which are slightly modified based on Bremer and Dennis' research (1996, 2008). However, the authors changed some of the original parameters or data points, but did not provide explanations for these changes:

(a) The original data depicted a growth rate-dependent translation elongation rate, but Table 2 presents it as a constant value.

Please see the reply to point 2 above.

(b) Figure 2b displays five experimental data points, as opposed to the six data points in the original dataset and other figures in this manuscript.

The values for the transcription rate were taken from Bremer and Dennis’s paper from 1996 which only contains five growth rates. We updated the Figure 2b – it now displays data from Bremer and Dennis 2008 for six growth rates.

(c) The model does not consider the fraction of RNAP transcribing rRNA (Φ_rRNA^RNAP), except in Appendix Figure 4. In the original data (Bremer and Dennis 1996), the fraction of RNAP transcribing rRNA increases dramatically with growth rate; however, in this study, it remains constant at 1.

Our goal was to keep the model as simple as possible and keep the number of required parameters to a minimum. We only included the figure in the supplementary material because it does not change the conclusions, even though it makes the predictions quantitatively better. In the future we would like to achieve this improvement by expanding the model (with mRNA, tRNA, non-specific RNAP binding to DNA etc.). We added a sentence to the discussion to point out again how the results are affected if Φ_rRNA^RNAP is included, and how this parameter could be mechanistically included in the model in the future.

"Furthermore, incorporating other types of RNA (mRNA, tRNA) and energy metabolism, or even constructing a genome-scale RBA model (Hu et al., 2020), will likely lead to more quantitative predictions of fluxes and growth rate. A strong indication of this is that including a variable RNAP allocation into the model leads to quantitatively better predictions (see Appendix 1, Figure 5). Therefore, in the future, we aim to model RNAP allocation mechanistically. This will involve for example adding other RNA species (mRNA, tRNA), and considering non-specifically bound RNAP which is a significant fraction of RNAP (Klumpp and Hwa, 2008)."

Furthermore, Φ_rRNA^RNAP was first introduced in line 205 but was not explained until line 337.

We added an explanation to the sentence in line 205:<br /> "If we consider RNAP allocation to rRNA (k_RNAP^el^bar = k_RNAP^el f_act^RNAP Φ_rRNA^RNAP, where Φ_rRNA^RNAP is the fraction of RNAP allocated to the synthesis of rRNA), the results get closer to the experimental data (Appendix 1, Figure 5)."

The value(s) of Φ_rRNA^RNAP for Appendix Figure 4 are also missing from this manuscript.

We added the missing values to the figure caption.

1. How, exactly, is the unit of flux converted to mmol g-1 h-1?

We are not exactly sure what the reviewer means by this question. As an example of unit conversion, we provide an explanation for the conversion of literature RNAP fluxes. The RNAP fluxes predicted by the model are in mmol g^-1 h^-1. The RNAP fluxes in Bremer and Dennis (2008) were in nt min^-1 cell^-1. To convert them to mmol g^-1 h^-1, we used the values of dry mass/cell from Bremer and Dennis (2008) and the number of nucleotides in rRNA (the stoichiometric coefficient n_rRNA). The code for the conversion is available on GitHub (https://github.com/diana-sz/RiboComp) in the script fluxes_vs_growth_rate.py.

1. What is the (dry) mass constraint and how is it defined? In the manuscript, both the second equation in line 101 and the bottom row of Table 1 are dry mass constraint(s). Why are they different? Furthermore, why is the right-hand side of the second equation in line 101 a dimensionless 1, and how does the last row of Table 1 result in the unit of growth rate, time^(-1)?

These are two forms of the same constraint. We added a paragraph to the methods section that explains how to convert the equations (capacity constraints, dry mass constraint) into the form in Table 1.

In the first form of the equation, ⍵Tc = 1, the units of ⍵ are g/mmol, and the units of c are mmol/g, so they cancel out.

The rows in Table 1 are multiplied by the vector of fluxes, so we get ⍵C [g/mmol] * vIC [mmol/gh] = μ [1/h].

1. The concentrations of all components that serve as "substrates" will be zero when growth rate is maximized, as these molecules do not catalyze any reactions, nor do they influence reaction kinetics in the model. These "0" concentration components are C, AA, NT, rP, and rRNA. Why are these concentrations even included in the model?

The reviewer is correct in pointing out that these species have zero concentrations at maximum growth, and it would be possible to simplify the model accordingly. However, we have chosen not to merge these reactions to maintain clarity in distinguishing between metabolic and macromolecular synthesis processes. Additionally, while we currently use the model to predict optimal behavior, it is not inherently limited to this purpose, as it can equally describe sub-optimal states (as in Figure 2b). Finally, if needed, we can easily introduce minimum concentration constraints (e.g. obtained from measurements) for any of these species without affecting our overall arguments.

Minor comments:

1. Questions regarding Figure 2:

(a) The explanation of Figure 2a is unclear. Intuitively, I assumed that it was a comparison between model predictions and experimental data, with the points representing experimental data and the line representing predictions; and the authors wrote in the figure legend "The points represent maximum growth rates in six experimental conditions". However, the growth rates shown in the figure do not match the original experimental data. Are all the data in the figure predictions?

Yes, the points are predictions and the line is a linear fit. We changed the figure caption as follows:<br /> "The model predicts a linear relationship between RNA to protein ratio and growth rate. The points represent the predicted maximum growth rates in six experimental conditions (Table 2). The line is a linear fit."

(b) Figure 2b is difficult to understand. This figure shows the non-optimal solutions of the model. It is unclear how these solutions are achieved and why there are three lines in the figure.

We expanded the figure caption to make it clearer:<br /> "Alternative RNAP fluxes at different non-optimal growth rates in glucose minimal medium. These are obtained by varying the growth rate step by step from zero to maximum and enumerating all solutions (elementary growth vectors as defined in Müller et al. (2022)) for each growth rate. The grey and blue lines are the alternative solutions. The blue line corresponds to solutions, where rRNA and ribosomes do not accumulate (constraints rRNA' andcap R' in Table 1 are limiting)."

1. Table 1 is also difficult to understand. While the stoichiometric constraints can be easily derived, the capacity constraints and the dry mass constraint cannot be easily derived from related equations from the text.

We added a paragraph into the methods section that explains how to convert the equations (capacity constraints, dry mass constraint) into matrix form.

1. As the authors ask a question in the title, they should provide an explicit answer in the abstract.

We added a sentence to the abstract:<br /> "Our model highlights the importance of RNA instability. If we neglect it, RNA synthesis is always ``cheaper' than protein synthesis, leading to an RNA-only ribosome at maximum growth rate. However, when we account for RNA turnover, we find that a mixed ribosome composed of RNA and proteins maximizes growth rate."

1. The authors should cite a seminal modeling paper, which was the first to examine resource allocation in simplified self-replicating cell systems (Molenaar et al. 2009, Molecular Systems Biology 5:323).

The citation was added.

1. The meaning of v is not consistently defined throughout the manuscript. It refers to the fluxes of enzymatic reactions in some instances, but in other contexts, it refers to the fluxes of the entire network of enzymatic reactions and protein synthesis reactions (Figure 1, Equation 1, and Line 386).

We have made the notation more consistent. When we refer to the fluxes of the entire network we now use v_tot instead of v.

1. Line 85, it might be difficult to interpret "RNAP fluxes" as the flux of rRNA synthesis without reading the subsequent text.

_We added the explanation in brackets.<br /> "_We validate the model by predicting RNAP fluxes (rRNA synthesis fluxes)."

1. Typo in line 102-103. "...protein fluxes 𝒘" → "...protein synthesis fluxes 𝒘".

Thank you for spotting that, we added the missing word.

1. Line 104, f_RNAP^act and f_R^act are not explained in the text; and their biological significance cannot be understood from their names in Table 2 ("RNAP activity" and "Ribosome activity").

We added a sentence that explains these parameters:<br /> "f_RNAP^act is the fraction of actively transcribing RNAPs, and f_R^act is the fraction of actively translating ribosomes."

1. Notion "**" in Table 2. The coupling between transcription and translation means the coupling of "mRNA" transcription and translation, not rRNA. At least in E. coli, the transcription rate of rRNA is faster than that of mRNA.

The transcription rate of the archaeal RNAP was determined in vitro. To our knowledge, data for transcription rates of rRNA vs. mRNA in vivo are not available. Therefore, the translation rate is only a very rough estimate.

1. Is the citation correct in line 136? I didn't find related information in Bremer and Dennis' paper after a quick scan.

We corrected the citation. Additionally, we added references that indicate that if rRNA is transcribed in excess of available r-proteins, it gets rapidly degraded:<br /> "In fact, the accumulation of free rRNA in a cell is biologically not realistic as it is bound by rPs already during transcription (Rodgers and Woodson, 2021). Furthermore, if rRNA is expressed in excess of rPs, it is rapidly degraded (Siehnel and Morgan, 1985)."

1. Lines 136-138. The statement is not accurate, as the fraction of inactive ribosomes increases with decreasing growth rate in E. coli (Dai et al. 2016, Nat Microbiol 2, 16231). If the studied growth rates are relatively high, it is acceptable to use a constant active ribosome fraction as an approximation, but this approximation should be made explicit.

We used the fractions of active ribosomes as reported in Bremer and Dennis, 2008 which are constant between growth rates of 0.4-2.1 1/h. In Dai et al. 2016, it was similarly observed that above the growth rate of ~0.5 1/h, the active fraction is quite constant. We rephrase the text to make it more accurate:<br /> "For the growth rates studied here (0.4-2.1 1/h), the fraction of inactive ribosomes stays roughly constant at 15-20% (Bremer and Dennis, 1996, 2008; Dai et al., 2016). In our model, we have already incorporated this fraction using the effective translation elongation rate (k_R^el^bar = k_R^el*f_R^act). However, below the growth rate of ~0.5 1/h, the fraction of active ribosomes rapidly decreases (Dai et al. 2016)."

1. The citation in line 142 is not accurate. It should be (Bremer and Dennis, 1996).

We corrected the citation.

1. Lines 192-193: "six" different growth media, not five.

Thank you for pointing that out, we corrected it.

1. Line 287: The statement "... translation rate does not increase in ribosomes with a higher protein content" could be misinterpreted as discussing translation elongation rate changes with different protein content in ribosomal protein mutant strains in a given species. It should be rephrased to remove ambiguity.

We rephrased the sentence as follows:<br /> "…translation rate does not increase in ribosomes from different species which have higher protein content."

1. Parameters for the three panels in Figure 8 are missing.

The parameters used for mitochondria are the same as for E. coli in glucose minimal media. The only difference is that a fraction of rPs can be imported. We added a sentence to the figure caption to clarify this:<br /> "The model can be adjusted to predict mitochondrial protein-rich ribosome composition. All parameters used for the simulation of mitochondria are the same as for E. coli in glucose minimal media, except a fraction of rPs can be imported for free from the cytoplasm and does not have to be synthesized. For simplicity, we assumed that 1/3 of rPs are imported. (In reality, almost all rPs are imported, but mitochondria make additional proteins to provide energy for the whole cell.)"

Reviewer #4 (Significance):

Strengths: Why the ribosome is composed of RNA and protein parts is a fundamental biological question. This manuscript proposes a very interesting hypothesis, arguing that the mixed ribosome composition results from rRNA instability. To test their hypothesis, the authors parameterize a simplified self-replicating cell model with realistic parameters. The model is first developed/parameterized for E. coli, and it could be easily adapted to other organisms with higher ribosomal protein content.

Limitations: The main limitations of this manuscript lie in the development of the model, especially the modeling of rRNA degradation and the use of constant values for growth rate-dependent parameters.

Advances: (1) This manuscript proposes a new hypothesis that rRNA instability is a universal factor that influences the ribosome composition across living organisms. (2) Compared to Kostinski and Reuveni's work, the authors have made certain improvements by including adjustable ribosome allocation to RNA and ribosomal protein when maximizing growth rate, which may lead to more realistic conclusions.

Audience: This work will be of interest to people in the field of theoretical biology, computational biology, and evolution, as well as to researchers studying ribosome structure and function.

Areas of expertise: Microbial systems biology, computational biology, and prokaryotic genomics.

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Referee #4

Evidence, reproducibility and clarity

Summary

In this manuscript, Széliová et al. used a simple self-replicating cell model to study why the ribosome consists of both RNA and protein from an economic point of view. Their base model predicts an RNA-only ribosome, which is not surprising since the smaller RNAP has a higher turnover number compared to the larger ribosome. When rRNA instability is included, the model predicts an "RNA+Protein" ribosome. In particular, the predicted ribosome composition is comparable to the measured ribosome composition when strong cooperative binding of ribosomal proteins to rRNA is considered. The authors conclude that the maximal growth rate is achieved by the real ribosome composition when rRNA instability is taken into account.

Major comments:

1. The authors modeled the rRNA degradation rate as a function of the concentration of fully assembled ribosomes (equation 5). However, only partially assembled ribosomes are susceptible to RNase, and they make up only a small fraction of total ribosomes. The majority of ribosomes are fully assembled. In addition, the turnover number obtained from Fazal et al. (2015) and used here is the degradation rate of double-stranded RNA, not the fully assembled ribosomes, which have a stable tertiary structure. In my opinion, the rRNA degradation rate should be modeled as a function of the concentration of partially assembled ribosomes (i.e., pre-R in Figure 7) rather than the concentration of fully assembled ribosomes.
2. Compared to the work by Kostinski and Reuveni (2020), the authors have made an improvement by avoiding the use of constant ribosome allocation to ribosomal protein (Φ_rP^R) and RNAP (Φ_RNAP^R), allowing these parameters to vary with predicted growth rates (by changing 𝑥_rP). This is indeed important, as bacteria are very likely to adjust these parameters in response to different growth conditions. However, certain other growth rate-dependent parameters are still treated as constants (or treated as nutrient-specific parameters) across predicted growth rates under given conditions. For example, experiments have shown that the fraction of active RNAP (f_RNAP^act) and the ribosome elongation rate (k_R^el) are growth rate-dependent (Bremer and Dennis, 1996). In contrast, when the authors predict the maximum growth rate by changing 𝑥_rP, f_RNAP^act and k_R^el are held constant regardless of the predicted growth rates.
3. If amino acids or nucleotides are provided in the media, the cell does not have to synthesize all of them de novo. However, the model assumes that the cell always synthesizes all amino acids or nucleotides de novo for growth on growth on amino acid-supplemented media or on LB. This problem could in principle be solved by assuming very fast kinetics of the metabolic reactions in these media, but that should be discussed in the manuscript. Furthermore, why does the turnover number for EAA depend on the growth rate while that of ENT is constant?
4. All parameters related to transcription (RNAP) and translation (ribosome) used in this manuscript are adopted from Kostinski and Reuveni (2020), which are slightly modified based on Bremer and Dennis' research (1996, 2008). However, the authors changed some of the original parameters or data points, but did not provide explanations for these changes:

(a) The original data depicted a growth rate-dependent translation elongation rate, but Table 2 presents it as a constant value.

(b) Figure 2b displays five experimental data points, as opposed to the six data points in the original dataset and other figures in this manuscript.

(c) The model does not consider the fraction of RNAP transcribing rRNA (Φ_rRNA^RNAP), except in Appendix Figure 4. In the original data (Bremer and Dennis 1996), the fraction of RNAP transcribing rRNA increases dramatically with growth rate; however, in this study, it remains constant at 1. Furthermore, Φ_rRNA^RNAP was first introduced in line 205 but was not explained until line 337. The value(s) of Φ_rRNA^RNAP for Appendix Figure 4 are also missing from this manuscript.<br /> 5. How, exactly, is the unit of flux converted to mmol g-1 h-1?<br /> 6. What is the (dry) mass constraint and how is it defined? In the manuscript, both the second equation in line 101 and the bottom row of Table 1 are dry mass constraint(s). Why are they different? Furthermore, why is the right-hand side of the second equation in line 101 a dimensionless 1, and how does the last row of Table 1 result in the unit of growth rate, time^(-1)?<br /> 7. The concentrations of all components that serve as "substrates" will be zero when growth rate is maximized, as these molecules do not catalyze any reactions, nor do they influence reaction kinetics in the model. These "0" concentration components are C, AA, NT, rP, and rRNA. Why are these concentrations even included in the model?

Minor comments:

1. Questions regarding Figure 2:

(a) The explanation of Figure 2a is unclear. Intuitively, I assumed that it was a comparison between model predictions and experimental data, with the points representing experimental data and the line representing predictions; and the authors wrote in the figure legend "The points represent maximum growth rates in six experimental conditions". However, the growth rates shown in the figure do not match the original experimental data. Are all the data in the figure predictions?

(b) Figure 2b is difficult to understand. This figure shows the non-optimal solutions of the model. It is unclear how these solutions are achieved and why there are three lines in the figure.<br /> 2. Table 1 is also difficult to understand. While the stoichiometric constraints can be easily derived, the capacity constraints and the dry mass constraint cannot be easily derived from related equations from the text.<br /> 3. As the authors ask a question in the title, they should provide an explicit answer in the abstract.<br /> 4. The authors should cite a seminal modeling paper, which was the first to examine resource allocation in simplified self-replicating cell systems (Molenaar et al. 2009, Molecular Systems Biology 5:323).<br /> 5. The meaning of v is not consistently defined throughout the manuscript. It refers to the fluxes of enzymatic reactions in some instances, but in other contexts, it refers to the fluxes of the entire network of enzymatic reactions and protein synthesis reactions (Figure 1, Equation 1, and Line 386).<br /> 6. Line 85, it might be difficult to interpret "RNAP fluxes" as the flux of rRNA synthesis without reading the subsequent text.<br /> 7. Typo in line 102-103. "...protein fluxes 𝒘" → "...protein synthesis fluxes 𝒘".<br /> 8. Line 104, f_RNAP^act and f_R^act are not explained in the text; and their biological significance cannot be understood from their names in Table 2 ("RNAP activity" and "Ribosome activity").<br /> 9. Notion "**" in Table 2. The coupling between transcription and translation means the coupling of "mRNA" transcription and translation, not rRNA. At least in E. coli, the transcription rate of rRNA is faster than that of mRNA.<br /> 10. Is the citation correct in line 136? I didn't find related information in Bremer and Dennis' paper after a quick scan.<br /> 11. Lines 136-138. The statement is not accurate, as the fraction of inactive ribosomes increases with decreasing growth rate in E. coli (Dai et al. 2016, Nat Microbiol 2, 16231). If the studied growth rates are relatively high, it is acceptable to use a constant active ribosome fraction as an approximation, but this approximation should be made explicit.<br /> 12. The citation in line 142 is not accurate. It should be (Bremer and Dennis, 1996).<br /> 13. Lines 192-193: "six" different growth media, not five.<br /> 14. Line 287: The statement "... translation rate does not increase in ribosomes with a higher protein content" could be misinterpreted as discussing translation elongation rate changes with different protein content in ribosomal protein mutant strains in a given species. It should be rephrased to remove ambiguity.<br /> 15. Parameters for the three panels in Figure 8 are missing.

Significance

Strengths: Why the ribosome is composed of RNA and protein parts is a fundamental biological question. This manuscript proposes a very interesting hypothesis, arguing that the mixed ribosome composition results from rRNA instability. To test their hypothesis, the authors parameterize a simplified self-replicating cell model with realistic parameters. The model is first developed/parameterized for E. coli, and it could be easily adapted to other organisms with higher ribosomal protein content.

Limitations: The main limitations of this manuscript lie in the development of the model, especially the modeling of rRNA degradation and the use of constant values for growth rate-dependent parameters.

Advances: (1) This manuscript proposes a new hypothesis that rRNA instability is a universal factor that influences the ribosome composition across living organisms. (2) Compared to Kostinski and Reuveni's work, the authors have made certain improvements by including adjustable ribosome allocation to RNA and ribosomal protein when maximizing growth rate, which may lead to more realistic conclusions.

Audience: This work will be of interest to people in the field of theoretical biology, computational biology, and evolution, as well as to researchers studying ribosome structure and function.

Areas of expertise: Microbial systems biology, computational biology, and prokaryotic genomics.

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 authors explore a mathematical model to rationalize the variable RNA content in ribosomes across species. The mathematical model particularly considers the idea that the protein-to-RNA ratio in ribosomes emerges as a consequence of faster rRNA than r-protein synthesis coupled with a faster degradation of rRNA. This is an interesting analysis. The idea is well explained and the math of the model is overall well explained. Overall, I thus support publication of this analysis. However, while reading the manuscript I was continuously wondering about two major aspects which, I suggest, should be considered more prominently in the text:

i. How clear is it that rRNA is more unstable than r-protein?

ii. Why should the translation rate (the speed with which ribosomes assemble new proteins) not be highly dependent on the ribosome-to-protein ratio (with some intermediate ratio ensuring efficient synthesis and efficient translation?

Currently these points are considered briefly in the discussion part. I suggest that these points should at least be discussed more prominently in the introduction. I further appreciate any more detailed thoughts the authors have on these questions. Finally, I think the discussion section would benefit strongly from a more detailed consideration of possible future experiments. Which data is needed to probe the idea? What types of experiments could be performed to probe the model.

More detailed comments:

Regarding i: rRNA is pretty stable compared to other RNA types in the cell. The authors argue it is unstable. The specific question then seems to become how stable rRNA is compared to r-protein? Generally, proteins are also stable, but what data is available to support that r-proteins are more stable than rRNA?

Regarding ii: Building on their model results, the authors rationalize the highly varying RNA-to-protein ratio in ribosomes across species. The model considers a non-varying rate with which ribosomes synthesize new proteins. This is briefly discussed in the discussion section. However, this appears to be a major assumption that, I think, should be stated clearly stated earlier in the text, including the abstract and introduction. Second, I wonder how the authors then rationalize variations in translation rate across species. Translation rates and the speeds with which ribosomes are varying strongly across species (indicated for example well by the change in the slope between ribosome content/rRNA and growth rate - slope in Fig. 2A). Why could the rRNA-to-protein ratio not be important in playing a role here?

More minor point, but I was also not sure about the justification that ribosome mass is constant (line 111). The mass of an amino acid and a nucleotide is quite different. Why should overall mass matter, and not for example the number of amino acids and proteins. I think it also would be good here to motivate the assumption better early on instead of commenting on it in the discussion section.

Significance

Protein synthesis by ribosomes is a major determinant of the rate with which microbes and other fast growing cells accumulate biomass. To better understand cell growth it is thus essential to better understand the makeup of ribosomes. Széliová et al present a mathematical model to entertain the idea that the varying RNA content in ribosomes across species is a consequence of RNA degradation. The model makes clear predictions which can guide future experiments.

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Referee #1

Evidence, reproducibility and clarity

Summary: This study addresses the problem of what is the optimal ribosome composition in terms of relative RNA and protein content, to ensure optimal growth rate and minimal energy waste. The RNA-world hypothesis suggests that primitive ribosomes were RNA-only objects, and in fact this would appear to be very advantageous from an energetic point of view, since RNA synthesis requires a much lower energy expenditure than protein synthesis. Yet a large fraction of present-day ribosome mass is protein, ranging from 30% to nearly 70% depending on the organism. The authors hypothesize that one of the main functions of ribosomal proteins is to stabilize the RNA and to protect it against degradation. According to their idea, the fast degradation of a protein-free rRNA would offset the energetic advantage given by its cheaper synthesis. To test the hypothesis, they developed a mathematical model whereby to evaluate the optimal ribosome composition under a number of different conditions.

Major comments: The paper is well-written and very readable. I am not an expert of mathematical modelling, so I cannot go into the details of the model presented. As a biologist, I can say that the conclusion arrived at are reasonable and well-justified. Perhaps the point of view is rather narrow, since ribosomal proteins are known to be important not only for RNA protection and ribosome stability, but also to ensure the accuracy of decoding and, in certain contexts, to allow the ribosomes to interact with other cellular ligands. The authors make only very slight reference to these questions, so it would be worthwhile to further comment on them.<br /> Furthermore, their explanation of why ribosome composition should be so different in different organisms (e.g. protein-poor bacterial ribosomes versus protein-rich archaeal ones) is not entirely convincing. For instance, they suggest that archaea may have protein-richer ribosomes than bacteria because they live in extreme environments, thus needing a further aid to stabilize the organelle. While this may be a factor, one must point out that non-extremophilic archaea (e.g. methanogens) have protein-rich ribosomes, making it obvious that other factors must be at play.

Minor comments: none in particular. Referencing is adequate, text is clear and the figures are clear and well-organized.

Significance

As I stated above, the main weakness of this study may be that it concentrates overwhelmingly on a single problem, i.e. the energetic cost of adding proteins to an RNA-only ancestral ribosome. On the other hand, this is a question seldom addressed when talking about ribosome composition, which indeed makes this paper valuable and interesting. The authors expand and advance a previous study of the same kind (to which they make ample reference).

Although rather specialized, I think this paper, in its general conclusions, may be of interest to most of those working in the field of protein synthesis and ribosome evolution.

Referee's keywords: archaea, ribosome evolution, translation, translation initiation

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1. General Statements

We thank the reviewers for their comments, and their appreciation of the value and thoroughness of our work in identifying a novel and clinically relevant consequence of centrosome amplification in favoring cell death. The reviewers accurately identify weaknesses of our work which we had also pointed out in the discussion of our manuscript. In particular, we agree as pointed out by Reviewer 1 that direct links between our cellular and clinical observations are difficult to establish given the low level of centrosome amplification observed in the tumor samples. Although multiple hypothesis might explain why preferentially eliminating a small population of cells is beneficial for the patients, we consider that this is out of the scope of this manuscript. However, given that our cellular and clinical observations point in the same direction, we remain confident in the value of presenting them together in this manuscript. We have made it clearer both in the results section and discussion that further work is required to better understand the influence of low levels of centrosome amplification on chemotherapy responses in patients.

We also thank the reviewers for their suggestions to improve the in vitro work we have performed. Our point by point response below lists the experiments we plan to perform, and corrections we have already included in this submitted version. Although Reviewer 3 points out that the molecular mechanism underlying apoptotic priming in cells with centrosome amplification remains a mystery, we argue that the identification of this priming already provides a mechanistic explanation for enhanced chemotherapy responses. Our careful and thorough analysis of these responses, using a diversity of advanced technical approaches was key to achieve this. We were also able to clearly rule out that priming is caused by a previously characterized centrosome amplification consequence, demonstrating its novelty. Reviewer 3’s characterization of our work as “archival” is diminishing to say the least, and we believe multiple aspects of this work will be built upon, even beyond the identification of a molecular mechanism which will of course also be important. Indeed, centrosome amplification is observed in a diversity of healthy cell types (megakaryocytes, B cells, hepatocytes…) and could contribute to the homeostasis of these tissues via apoptotic priming. We predict the translational perspectives of this work also to be important, from the point of view of centrosome amplification in disease, but also in understanding apoptotic priming and responses to BH3-mimetics.

2. Description of the planned revisions

Reviewer 1, Major comments:

1. The conclusion that centrosome amplification primes to apoptosis irrespective of mitotic defects is largely based on low resolution timelapse analysis (20x magnification, 10 minute imaging intervals, no tubulin). Imaging at this resolution is likely to miss mitotic defects, reducing the confidence with which this conclusion can be drawn.

We were unsure of the exact point brought up by Reviewer 1 here and we have consulted Reviewer 1 (through Reviews commons) to confirm the revision plan. In Figure 5A, we show that the level of heterogeneity stemming from chromosome instability is lower for PLK4OE than for MPS1 inhibition, and Figure 5D then shows that apoptotic priming only occurs in PLK4OE, and not in response to MPS1 inhibition. Combined, these experiments allow us to conclude that apoptotic priming occurs independently of mitotic defects. Nevertheless, we propose to reproduce the live-imaging of mitosis, increasing the resolution and including tubulin, to better visualize mitotic defects in response to the different mitotic perturbations induced.

1. Data from timelapse analysis of DNA content in Fig. 2 are used to conclude that Plk4OE cells are more sensitive to carboplatin due to mitotic defects that occurred without multipolar spindles. However, it is premature to conclude that multipolar spindles were not involved in DNA mis-segregation without visualizing the spindles themselves. While DNA positioning can be used as a proxy for spindle morphology, as performed here, it only reliably detects multipolar spindles when all poles are relatively equal in size and the multipolar spindle is maintained throughout mitosis. However, the poles in multipolar spindles often differ in size and ability to recruit DNA. Additionally, they often cluster over time, which can preclude their identification when only visualizing DNA, especially at 20x magnification. Compelling evidence that high mis-segregation is occurring without multipolar spindles would require visualizing the spindles and also demonstrating the cause of the increased chromosome mis-segregation. (Are acentric fragments being mis-segregated as lagging chromosomes?)

We agree with Reviewer 1 that the “High mis-segregation” mitotic phenotype we describe is poorly characterized in our original manuscript, and that we cannot formally exclude that multipolar spindles are involved, although we observe this phenotype in similar proportions in PLK4Ctl and PLK4OE. We also agree that identifying the origin of increased chromosome mis-segregation is relevant here. We therefore propose to characterize spindles and mis-segregating chromosomes by imaging fixed mitotic figures upon Carboplatin treatment, staining for Tubulin, centrosomes, and centromeres. This will allow us to better determine if Carboplatin induces the same mitotic phenotypes in PLK4OE and PLK4Ctl cells.

1. The images in Fig. 3D and 4D are not of sufficient resolution to support the central conclusion that centrosome amplification primes cells for MOMP. This conclusion is further weakened by the facts that 1) Plk4OE was the only source of centrosome amplification tested and 2) Plk4OE was reported to prime for MOMP in only 2 of 3 cell lines. Potential explanations for the lack of priming in SKOV3 cells should be discussed. Additionally, the sensitization in Fig. S4H-J appears quite modest. (These data are also difficult to see, perhaps because the Plk4Ctl -/+ chemo conditions are overlapping.)

We have made images in Fig. 3D and 4D larger. We hope that this makes our observations of Cytochrome C release (quantified in Fig. 3E and 4E) easier to visualize for readers. We would like to point out that our conclusion that centrosome amplification primes for MOMP in OVCAR8 does not only arise from the assays presented in these figures. In Figures 4A and 4C we show by MTT assays and detection of apoptotic cells by cytometry respectively, that PLK4OE OVCAR8 are sensitized to BH3-mimetic WEHI-539 compared to PLK4Ctl cells. We also show this priming using BH3-mimetic Navitoclax in Fig S4F. Regarding the source of centrosome amplification, we use OVCAR8 cells devoid of the inducible PLK4OE transgene and show that “natural” centrosome amplification also makes OVCAR8 cells more sensitive to WEHI-539 (Fig. S4C). This strongly suggests that priming does indeed stem from centrosome amplification and not from other consequences of PLK4 over-expression. Nevertheless we are currently generating cells to induce centrosome amplification via SAS-6 over-expression, to test an alternative source of centrosome amplification.

We do not claim that this apoptotic priming is a universal consequence of centrosome amplification, as indeed we show that it is not observed for the cell line SKOV3 (Fig. S4F). For now, we do not have a clear hypothesis of the reason for the cell line differences. Initially we hypothesized that p53 status could be in cause because OVCAR8 and COV504 both express mutant p53 whereas p53 protein is completely absent in SKOV3. However we observe that p53 does not seem to affect cell death signaling in OVCAR8 (Fig. S3C-D), making this hypothesis less likely. The 3 cell lines are indeed very different in terms of origin and genomic alterations, making it difficult at this stage to propose an evidence-based explanation of differences in terms of apoptotic priming.

Finally, regarding the sensitization to chemotherapy associated priming presented in Fig. S4H-J, we have made the figures bigger and non-overlapping hoping that this makes them easier to read. Additionally, we agree that the effect of centrosome amplification appears modest. The trypan-blue assays we used have the advantage of being relatively high-throughput, but they only detect a fraction of the killed cells: only cells that are late in the apoptotic process but that haven’t yet been degraded. This makes the assay less sensitive. The general tendency we observe nevertheless proposes an association between apoptotic priming induced by centrosome amplification, and an enhanced sensitivity to a diversity of chemotherapy agents. We propose to confirm this for OVCAR8 cells treated with Olaparib, by performing cytometry experiments staining for AnnexinV and Propidium Iodide in order to increase sensitivity by detecting earlier signs of apoptosis.

Reviewer 2, Major comments:

1. The authors state that (Line 133) "the increased multipolarity we observe in presence of the combined chemotherapy is caused by the effect of Paclitaxel on the capacity of cells to cluster centrosomes." Could the authors to back up this claim by reanalyzing the imaging data to look for clustering as a survival mechanism versus inhibition of clustering in Paclitaxel-treated cells? Or indeed test any of the range of available clustering inhibitors directly on PLK4OE and thus prove the contribution of clustering to survival?

We agree that the conclusion that Paclitaxel suppresses centrosome clustering is not sufficiently backed by experimental data. We cannot directly view clustering in the live-imaging experiments we performed, because we are visualizing neither tubulin nor centrosomes. To clarify this point, we will:

1. Image fixed mitotic figures of Plk4Ctl and PLK4OE cells untreated or treated with Paclitaxel, staining for tubulin and centrosomes to identify if indeed Paclitaxel increases the proportion of anaphases with multiple poles characterized by the presence of centrosomes. We will use this type of assay as live imaging approaches to film both microtubules and centrosomes will not be feasible within the timing of this revision, but also because paclitaxel responses maybe modified if tubulin dyes are used such as Sir-tubulin.
2. We will use HSET inhibitor CW069, to test if this also prevents centrosome clustering.
3. If this is the case, we will then test if CW069 also preferentially kills PLK4OE compared to PLK4Ctl by Trypan-blue viability assays.

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

Reviewer 1, Major comments:

1. In its current form, the title suggests that the major role of centrosome amplification in sensitizing to chemotherapy is independent of multipolar divisions. Based on Figure 1, this is misleading. Figure 1D shows that in centrosome amplified cells treated with combination chemotherapy, the most common cause of death is high mis-segregation on multipolar spindles. Modifying the title to "Centrosome amplification favors the response to chemotherapy in ovarian cancer by priming for apoptosis in addition to promoting multipolar division" would more accurately reflect the data.

We agree with Reviewer 1 that our title should include the promotion of multipolar divisions, and have modified the title accordingly.

1. Line 191 points out that more Plk4OE cells that were in G1 at the beginning of carboplatin died than Plk4Ctl cells. However, in Fig. 2H-I, it looks like longer G1 durations in the presence of carboplatin led to increased cell death and that the Plk4OE cells happened to spend more time in G1 at the beginning of carboplatin treatment than Plk4Ctl cells did. Is this the case? Quantification of the average time spent in G1 for each group would be helpful.

Upon Carboplatin exposure, G1 length is indeed longer for PLK4OE cells compared to PLK4Ctl cells, as shown in Fig. S2D for complete G1 phases observed after the first mitosis (although the induced lengthening is mild compared to the observed extension of G2 induced upon carboplatin exposure shown in Fig. S2D). The same tendency, although not significant, is observable for cells in G1 at the beginning of carboplatin treatment, although it is harder to conclude because these are not complete G1 phases.

To assess links between G1 phase length and cell fate, we have plotted the length of G1 depending on whether cells live or die, focusing on cells of the second generation for which G1 length is complete. We observed no link between G1 length and cell fate, and have added this figure as Fig. S1E.

Reviewer 1, minor comments:

1. The authors cite Fig. 1B when drawing the conclusion that "combined chemotherapy induced a stronger reduction of viable cells produced per lineage in PLK4OE compared to PLK4Ctl". But Fig. 1B shows that combination chemotherapy produced a similar decrease in viable cells per lineage +/- Plk4OE. If anything, the Plk4OE+ cells showed slightly less sensitivity because they proliferated more poorly in the absence of chemotherapy. This is also true for carboplatin sensitivity in Fig. 2D (line 156).

Here our focus is actually more on the proportion of cell death that on the number of viable cells. We agree that the way we wrote this makes it confusing so we have re-written this paragraph to make it clearer.

1. Line 202 concludes that Fig. S2H-I shows that Plk4OE doesn't affect recruitment of DNA damage repair factors. The dotted outlines around the nuclei in Fig. S2H-1 make it very difficult to see, but it appears that gH2AX, FancD2, and 53BP1 signals are lower in Plk4OE cells.

We have made images in Fig. S2H bigger and the dotted outlines around nuclear less strong, and we hope this makes the signal easier to see. Strong cell to cell variations in signal make it hard to draw conclusions from images, although we have aimed to present this heterogeneity. The quantifications shown in Fig. S2I however show that there are no differences in Rad51 or FANCD2 recruitment in PLK4OE cells. For 53BP1 however, we observed less recruitment in PLK4OE for one biological replicate (squares in quantification shown in Fig. S2I) but not in the two other replicates. Although there may be some interesting observation here, this difference does not appear sufficiently robust to consider it as relevant in the context of this study.

1. The images for "dies in interphase" and "dies in mitosis" in Fig. 1B are suboptimal. Alternative images would be beneficial.

We have modified the images and added timepoints to make the phenotypes clearer. We have also added supplementary movies to better visualize the events (See Movie S1A for cell death events).

1. It would be helpful to discuss the clinical relevance of WEHI-539 and Navitoclax.

We have further developed the section of our discussion about the clinical relevance of BH3-mimetics and these drugs.

1. The discussion states that "mitotic drugs that limit centrosome clustering have had limited success in the clinic". I am not aware of any drugs that limit centrosome clustering that are suitable for in vivo use and the citation provided does not mention centrosome clustering.

We thank Reviewer 1 for this comment. Indeed, we oversimplified things a bit here, and have rewritten this paragraph. We have however kept the citation because although this reference does not directly mention centrosome clustering, some of the discussed drugs have been shown to kill cancer cells via centrosome unclustering in vitro in other studies.

1. The dark purple and black are very difficult to discriminate (Figure 1,2 and S1), as are the light green and light turquoise (Fig. 4A,S4A-B, S4F, S4H).

We changed these colors in the indicated graphs, and also in other figures where they were used. We hope these changes make the figures easier to read.

1. Line 246 claims that Fig. S3B shows that p21 and PUMA mildly increase upon carboplatin exposure, but it isn't clear that these increase in a biologically or statistically significant manner.

We have modified this paragraph because indeed it seems unlikely that the differences are statistically or biologically significant.

1. The green used to indicate S/G2 in Fig. S2A-B is different in Plk4 Ctrl vs Plk4OE cells.

We thank Reviewer 1 for spotting this and have changed the colors.

1. I do not believe that carboplatin + paclitaxel is standard of care treatment for breast or lung cancer, as stated on line 48-49.

Based on the guidelines of the NIH, we believe that these two drugs are indeed used in combination for the treatment of Stage IV non small cell lung cancer, as well as triple-negative breast cancer. (https://www.cancer.gov/types/lung/hp/non-small-cell-lung-treatment-pdq#_48414_toc, https://www.cancer.gov/types/breast/hp/breast-treatment-pdq#_1049).

However, given the complexity and diversity of treatment protocols, we have modified the text so as not to convey the idea that these are the only drugs used.

1. This study advances, but does not complete our understanding of centrosome amplification in breast cancer, as stated on line 75.

Agreed and changed.

1. Line 297 describes Navitoclax as an "inhibitor of BCL2, BCL-XL and BCL2". (ie BCL2 is listed twice).

Thank you for noticing this, we have corrected this.

1. It's not clear why line 120, which refers to effects of combined chemotherapy, cites Fig. S1G-I, which apparently show data from untreated (even without dox?) Plk4Ctrl and Plk4OE cells.

We indeed meant to refer to Fig. 1E-F and have therefore made this change.

1. In Fig. S6A, how can the mitotic index be 200%?

We thank Reviewer 1 for noticing the poor labelling of this figure. It is not a percentage of cells we are presenting, but the number of mitotic figures identified in 10 analyzed fields. We have corrected the figure.

Reviewer 2 major comments:

1. Fig 3: Results line 229-236 refer to quantification of fragmented nuclei which the authors interpret as poised for apoptosis. Micronuclei are also quantified- do the authors interpret this phenotype as advanced apoptosis? There is no mention of apoptotic bodies in the analysis. I would ask the authors to provide a bank of representative images with explanations to illustrate their interpretation of the range of morphologies - differences between nuclear fragmentation, versus micronuclei versus DNA contained in apoptotic bodies.

The cells we defined as “poised for apoptosis” are cells that release cytochrome C in presence of a pan-caspase inhibitor. These cells are therefore activating mitochondrial outer membrane permeabilization without executing apoptosis. It is then within these cells that we observe different nuclear morphologies, reflecting different behaviors in mitosis rather than apoptosis advancement. Apoptotic bodies are not observed in these cells, because they are actually not executing apoptosis owing to the presence of the pan-caspase inhibitor. We visualized apoptotic bodies only in absence of pan-caspase inhibitor. These are indicated by white arrow-heads, in Fig. 3D which was made bigger for more clarity. We have also added images of nuclei to present the different morphologies we describe in Fig. 3F.

1. Although this patient cohort is described in a previous publication, authors should include a cohort description in a table within supplemental for this manuscript: age range of patients, number of patients in each stage, size of tumours, and most relevant to this study, treatment regimens- adjuvant versus neoadjuvant, surgery vs no surgery? How is the cohort selected- sequentially selected? inclusion/exclusion criteria? Statement in abstract "we show that high centrosome numbers associate with improved chemo responses" is too specific as we have no information on the treatment regimens received by the patients (neo or adjuvant chemo versus surgical/radiological interventions?). Maybe treatment response would be more appropriate? Were there any cases of Pathological complete (or even near complete) response in this cohort and if so, what was the CNR in those cases?

We have included the cohort description in Supplementary Table 1. This is a retrospective cohort, so no specific inclusion criteria were applied. Treatment mainly consisted of surgery (100% patients) followed by adjuvant chemotherapy consisting of platinium salts and/or taxanes (84% of patients, 67% treated with both). Despite the wide common ground of treatment (surgery followed by taxanes and/or platinium salts for 84% of patients), we have nevertheless modified the abstract as suggested by Reviewer 2. Regarding complete or near-complete response, there were no such cases in this cohort.

Reviewer 2, minor comments:

Just some minor points on language:<br /> Line 54: Suggest rephrasing of the statement "and this can be favored by centrosome amplification (29) "<br /> Perhaps a word like potentiated instead of favored?<br /> Line 67: Again consider using an alternative to favored "We show that centrosome amplification favors the response to combined Carboplatin and Paclitaxel via multiple mechanisms."<br /> Favored is in fact used throughout the manuscript text- in my opinion this is not a scientific enough term and would consider replacing with alternative.

We have replaced the term favor with more appropriate terms, depending on the context.

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

Reviewer 1, major comments:

1. In a previous technical tour de force (Morretton et al, EMBO Mol Med 2022), the Basto lab quantified centriole numbers in the ovarian patient cancer samples analyzed here, and found that the percentage of cells with centrosome amplification in a given ovarian tumor is quite small, only reaching a maximum of 3.2%. It is critical background information to cite that quantification here. This information also begs the question of whether introducing this low rate of centrosome amplification is sufficient to cause a more global apoptotic priming in the sample, as suggested.

We have now included this important background information in our results section. We agree with Reviewer 1 that the low levels of centrosome amplification in tumors may not cause a more global apoptotic priming in the whole tumor. However, based on our findings, this low proportion of cells will most likely be more sensitive to chemotherapy. We cannot affirm for now what will be the consequences of the preferential elimination of these cells. However, given centrosome amplification’s potential to promote malignant behaviors such as genetic instability or invasiveness, we hypothesize that the elimination of these cells may have effects on tumor survival that are not proportional to their numbers. Testing this hypothesis would require many more experiments using in vivo models, which we cannot carry out within the scope of this study.

Reviewer 2, major comments:

1. Fig 6: While the authors have already acknowledged this as a weakness of the study, can the patient data really be compared to cell line data on CA because inclusion of CNRs between 1.4 and 2 as "high CNR" is questionable given that this ratio represents a completely normal centrosome complement? Are the authors confident enough in the imaging technique that all centrosomes are being detected? Can the authors justify the inclusion of the 1.4-2 CNR tumours by breaking down individual patient data on response to various treatments? Have the authors tried to analyse the cohort for OS and RFS using only those 9% of tumours exhibiting CA? What does the analyses of Fig 6 and S6 look like with a CNR cut-off of 2 instead of 1.45? Does the re-analysis show a better correlation between CNR and FIGO stage?

At the single-cell level, centrosome amplification is indeed defined as the presence of more than 2 centrosomes per cell. Tumor samples are characterized by heterogeneous centrosome numbers, with some regions showing extensive centrosome loss, and some others showing nuclei associated with either one, two or various levels of centrosome amplification. In such a heterogeneous population of cells, it is therefore not straight-forward to use the cut-off CNR=2 to define tumors with centrosome amplification. We have nevertheless analyzed the clinical parameters using the cut-off for CNR at 2 as proposed. Using this cut-off, High CNR patients still show improved overall survival, but a non-statistically significant extension of time to relapse. There are very few patients with CNR>2 (6 for overall survival and 5 for time to relapse), and therefore we remain unconvinced by the statistical value of such an analysis.

The definition of a cut-off at 1.45 was not arbitrary. We dichotomized the population into two groups using the Classification And Regression Trees (CART) method. Taking into consideration the binary outcome “relapse within 6 months or no relapse within 6 months” this method resulted in the categorization of the cohort into low CNR (£ 1.45) and high CNR (> 1.45). Independently, we also used predictiveness curves to estimate an optimal cut-off parameter for a continuous biomarker such as the CNR. The threshold obtained by this robust methodology was in agreement with CART approach with a cut-off of 1.40.

Dichotomizing the population does not guarantee the identification of significant clinical differences between the generated groups. We therefore analyzed overall survival and time to relapse ex post, and observed that high CNR and low CNR populations differed significantly for both these parameters.

Regarding FIGO stage, given frequent late detection of ovarian cancer, 59% of the cohort is considered at stage III (See Fig. S6C). All patients with CNR>2 are in the group of Stage III, except one which is Stage II. However, no patient with CNR>2 is in Stage IV, arguing that even with a higher CNR cut-off, there is no association between CNR and Figo stage.

1. The experimental PLK4 overexpression system is an accepted and clean method to induce CA in vitro. Could the authors comment in the discussion on how they envision CA being induced as a sensitizing agent in the clinical setting to support the translational aspects of their work?

In the clinical setting, we do not suggest to induce centrosome amplification as a sensitization agent. Indeed, centrosome amplification induces multiple phenotypes associated with malignancy (genomic instability, invasiveness). The translational aspects of our work relate more to the detection of centrosome amplification as a potential biomarker of chemotherapy responses, from conventional chemotherapies to BH3-mimetics for which biomarkers are absent. This aspect we have commented on in our discussion.

Reviewer 2, minor comments:

Line 263: "Centrosome amplification primes for MOMP and sensitizes cells to a diversity of chemotherapies." CA primes to one very specific BCL-XL inhibitor in this section so consider modifying the title of the section.

We agree that centrosome amplification makes cells sensitive to a specific BCL-XL inhibitor. However, we nevertheless claim that this very specific priming, can potentiate these cells responses to a diverse range of chemotherapies with different targets (paclitaxel, carboplatin, and olaparib).

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Referee #3

Evidence, reproducibility and clarity

This is a valuable archival paper that catalogues the effects of combined treatment with paclitaxel and carboplatin predominantly on one ovarian cancer cell line, OVCAR8, in which extra centrosomes can be induced by induced overexpression of Plk4. It systematically examines cellular responses to this drug treatment regimen in control and Plk4 overexpressing cells. Together the experiments show that Plk4-mediated formation of extra-centrosomes sensitizes cells to cell death independently of any effect upon spindle multipolarity and chromosome segregation, irregular spindle formation and mitotic errors, and of the DNA damage response. The authors then go on to show that Plk4 over expression results in premature cleavage of Caspase 3 and so favors the apoptotic response. \This appears to be mediate through increased mitochondrial outer membrane permeabilization. The PIDDosome is believed to contribute to apoptosis in the presence of extra centrosomes through a p%£ mediated pathway. However, in this case, apoptosis appears to be independent of p53 and also of the PIDDosome, as show by deleting a key PIDDosome component. The authors are therefore left with a bit of a mystery in terms of providing a mechanistic explanation of their findings.<br /> I do recommend publication of this paper in its present form as the study has been carried out very carefully and it is very important for workers in the field to know what has been tried in attempt to explain the phenomenon of increased cell death following Plk4 overexpression. It does not lead to a new mechanistic discovery but highlights an important phenomenon that we still have to explain.

Significance

valuable archival information

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Referee #2

Evidence, reproducibility and clarity

Summary

The authors' findings suggest that induction of centrosome amplification synergises with and potentiates the cytotoxic effects of standard chemo in epithelial ovarian cancer cell lines via a mechanism involving mitochondrial membrane priming and Cyt C release. CA has differential apoptotic priming effects depending on the cell line context. The authors use single cell analysis to characterise the range of mitotic defects through to cell fate following PLK4 OE and the combination treatments. The studies are extended to an ovarian cancer patient cohort where elevated centrosome numbers are associated with better OS and RFS. These findings have the potential to improve future patient stratification and treatment in EOC in addition to prognosis of treatment response.

Major comments

1. The authors state that (Line 133) "the increased multipolarity we observe in presence of the combined chemotherapy is caused by the effect of Paclitaxel on the capacity of cells to cluster centrosomes." Could the authors to back up this claim by reanalysing the imaging data to look for clustering as a survival mechanism versus inhibition of clustering in Paclitaxel-treated cells? Or indeed test any of the range of available clustering inhibitors directly on PLK4OE and thus prove the contribution of clustering to survival?
2. Fig 3: Results line 229-236 refer to quantification of fragmented nuclei which the authors interpret as poised for apoptosis. Micronuclei are also quantified- do the authors interpret this phenotype as advanced apoptosis? There is no mention of apoptotic bodies in the analysis. I would ask the authors to provide a bank of representative images with explanations to illustrate their interpretation of the range of morphologies - differences between nuclear fragmentation, versus micronuclei versus DNA contained in apoptotic bodies.
3. Fig 6: While the authors have already acknowledged this as a weakness of the study, can the patient data really be compared to cell line data on CA because inclusion of CNRs between 1.4 and 2 as "high CNR" is questionable given that this ratio represents a completely normal centrosome complement? Are the authors confident enough in the imaging technique that all centrosomes are being detected? Can the authors justify the inclusion of the 1.4-2 CNR tumours by breaking down individual patient data on response to various treatments? Have the authors tried to analyse the cohort for OS and RFS using only those 9% of tumours exhibiting CA? What does the analyses of Fig 6 and S6 look like with a CNR cut-off of 2 instead of 1.45? Does the re-analysis show a better correlation between CNR and FIGO stage?
4. Although this patient cohort is described in a previous publication, authors should include a cohort description in a table within supplemental for this manuscript: age range of patients, number of patients in each stage, size of tumours, and most relevant to this study, treatment regimens- adjuvant versus neoadjuvant, surgery vs no surgery? How is the cohort selected- sequentially selected? inclusion/exclusion criteria?<br /> Statement in abstract "we show that high centrosome numbers associate with improved chemo responses" is too specific as we have no information on the treatment regimens received by the patients (neo or adjuvant chemo versus surgical/radiological interventions?). Maybe treatment response would be more appropriate? Were there any cases of Pathological complete (or even near complete) response in this cohort and if so, what was the CNR in those cases?
5. The experimental PLK4 overexpression system is an accepted and clean method to induce CA in vitro. Could the authors comment in the discussion on how they envision CA being induced as a sensitizing agent in the clinical setting to support the translational aspects of their work?

Minor comments

The manuscript is well written and all data clearly and thoroughly presented.

Just some minor points on language:

Line 54: Suggest rephrasing of the statement "and this can be favored by centrosome amplification (29)"<br /> Perhaps a word like potentiated instead of favored?<br /> Line 67: Again consider using an alternative to favored "We show that centrosome amplification favors the response to combined Carboplatin and Paclitaxel via multiple mechanisms."<br /> Favored is in fact used throughout the manuscript text- in my opinion this is not a scientific enough term and would consider replacing with alternative.<br /> Line 263: "Centrosome amplification primes for MOMP and sensitizes cells to a diversity of chemotherapies." CA primes to one very specific BCL-XL inhibitor in this section so consider modifying the title of the section.

Significance

Overall, this well-written work extends and provides mechanistic detail to understand the role of CA in priming cells for cytotoxicity in response to commonly used chemo agents in the EOC context. It is a thorough study with sound conclusions drawn from the data provided. It also employs a broad range of assays and techniques to explore the hypotheses from every angle. In view of this, this manuscript is a valuable contribution to the literature on the role of CA in ovarian cancer and its treatment.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Edwards et al analyze OVCAR8 cells with dox inducible expression of Plk4. Doxycycline treatment induces centrosome amplification in ~80% of cells. 72 hour timelapse analysis of cells with fluorescent chromosomes revealed that cell death after carboplatin+paclitaxel was more common in Plk4OE than Plk4Ctl cells. Cell death was most common after high chromosome mis-segregation/multipolar division, which resulted in death of ~80% of the daughter cells. However, death was also elevated in cells with no or slight mis-segregation when comparing Plk4OE to PlkrCtl (40% vs 12%), suggesting an additional sensitization effect. Plk4OE also increased cell death in carboplatin alone, most notably after high mis-segregation but also to a lesser extent in cells with no or slight mis-segregation. 17% of Plk4OE cells exposed to carboplatin in G1 died in S/G2 vs 6% of Plk4Ctl. This difference did not appear to be due to DNA damage response or PIDDosome activity. Carboplatin caused caspase 3 cleavage and cytochrome C release to a greater extent in Plk4OE than Pl4Ctl cells, suggesting MOMP priming. Plk4OE sensitizes OVCAR8 cells to the BCL-XL inhibitor WEHI-539, and Plk4OE sensitized COV504 but not SKOV3 cells to the less specific inhibitor Navitoclax. In 88 patients with high grade serous ovarian carcinoma, a high (>1.45) centrosome-to-nucleus ratio was associated with increased relapse-free and overall survival. The authors conclude that centrosome amplification primes ovarian cancer cells to chemotherapy independent of mitotic defects.

Major comments

1. In its current form, the title suggests that the major role of centrosome amplification in sensitizing to chemotherapy is independent of multipolar divisions. Based on Figure 1, this is misleading. Figure 1D shows that in centrosome amplified cells treated with combination chemotherapy, the most common cause of death is high mis-segregation on multipolar spindles. Modifying the title to "Centrosome amplification favors the response to chemotherapy in ovarian cancer by priming for apoptosis in addition to promoting multipolar division" would more accurately reflect the data.
2. In a previous technical tour de force (Morretton et al, EMBO Mol Med 2022), the Basto lab quantified centriole numbers in the ovarian patient cancer samples analyzed here, and found that the percentage of cells with centrosome amplification in a given ovarian tumor is quite small, only reaching a maximum of 3.2%. It is critical background information to cite that quantification here. This information also begs the question of whether introducing this low rate of centrosome amplification is sufficient to cause a more global apoptotic priming in the sample, as suggested.
3. The conclusion that centrosome amplification primes to apoptosis irrespective of mitotic defects is largely based on low resolution timelapse analysis (20x magnification, 10 minute imaging intervals, no tubulin). Imaging at this resolution is likely to miss mitotic defects, reducing the confidence with which this conclusion can be drawn.
4. Data from timelapse analysis of DNA content in Fig. 2 are used to conclude that Plk4OE cells are more sensitive to carboplatin due to mitotic defects that occurred without multipolar spindles. However, it is premature to conclude that multipolar spindles were not involved in DNA mis-segregation without visualizing the spindles themselves. While DNA positioning can be used as a proxy for spindle morphology, as performed here, it only reliably detects multipolar spindles when all poles are relatively equal in size and the multipolar spindle is maintained throughout mitosis. However, the poles in multipolar spindles often differ in size and ability to recruit DNA. Additionally, they often cluster over time, which can preclude their identification when only visualizing DNA, especially at 20x magnification. Compelling evidence that high mis-segregation is occurring without multipolar spindles would require visualizing the spindles and also demonstrating the cause of the increased chromosome mis-segregation. (Are acentric fragments being mis-segregated as lagging chromosomes?)
5. The images in Fig. 3D and 4D are not of sufficient resolution to support the central conclusion that centrosome amplification primes cells for MOMP. This conclusion is further weakened by the facts that 1) Plk4OE was the only source of centrosome amplification tested and 2) Plk4OE was reported to prime for MOMP in only 2 of 3 cell lines. Potential explanations for the lack of priming in SKOV3 cells should be discussed. Additionally, the sensitization in Fig. S4H-J appears quite modest. (These data are also difficult to see, perhaps because the Plk4Ctl -/+ chemo conditions are overlapping.)
6. Line 191 points out that more Plk4OE cells that were in G1 at the beginning of carboplatin died than Plk4Ctl cells. However, in Fig. 2H-I, it looks like longer G1 durations in the presence of carboplatin led to increased cell death and that the Plk4OE cells happened to spend more time in G1 at the beginning of carboplatin treatment than Plk4Ctl cells did. Is this the case? Quantification of the average time spent in G1 for each group would be helpful.

Minor comments

1. The authors cite Fig. 1B when drawing the conclusion that "combined chemotherapy induced a stronger reduction of viable cells produced per lineage in PLK4OE compared to PLK4Ctl". But Fig. 1B shows that combination chemotherapy produced a similar decrease in viable cells per lineage +/- Plk4OE. If anything, the Plk4OE+ cells showed slightly less sensitivity because they proliferated more poorly in the absence of chemotherapy. This is also true for carboplatin sensitivity in Fig. 2D (line 156).
2. Line 202 concludes that Fig. S2H-I shows that Plk4OE doesn't affect recruitment of DNA damage repair factors. The dotted outlines around the nuclei in Fig. S2H-1 make it very difficult to see, but it appears that gH2AX, FancD2, and 53BP1 signals are lower in Plk4OE cells.
3. The images for "dies in interphase" and "dies in mitosis" in Fig. 1B are suboptimal. Alternative images would be beneficial.
4. It would be helpful to discuss the clinical relevance of WEHI-539 and Navitoclax.
5. The discussion states that "mitotic drugs that limit centrosome clustering have had limited success in the clinic". I am not aware of any drugs that limit centrosome clustering that are suitable for in vivo use and the citation provided does not mention centrosome clustering.
6. The dark purple and black are very difficult to discriminate (Figure 1,2 and S1), as are the light green and light turquoise (Fig. 4A,S4A-B, S4F, S4H).
7. Line 246 claims that Fig. S3B shows that p21 and PUMA mildy increase upon carboplatin exposure, but it isn't clear that these increase in a biologically or statistically significant manner.
8. The green used to indicate S/G2 in Fig. S2A-B is different in Plk4 Ctrl vs Plk4OE cells.
9. I do not believe that carboplatin + paclitaxel is standard of care treatment for breast or lung cancer, as stated on line 48-49.
10. This study advances, but does not complete our understanding of centrosome amplification in breast cancer, as stated on line 75.
11. Line 297 describes Navitoclax as an "inhibitor of BCL2, BCL-XL and BCL2". (ie BCL2 is listed twice).
12. It's not clear why line 120, which refers to effects of combined chemotherapy, cites Fig. S1G-I, which apparently show data from untreated (even without dox?) Plk4Ctrl and Plk4OE cells.
13. In Fig. S6A, how can the mitotic index be 200%?

Significance

The importance of centrosome amplification in cancer has long been debated. The possible effects of extra centrosomes on multipolar divisions are well known. An independent apoptosis-priming effect of additional centrosomes is novel and of interest. However, in their previous manuscript (Morretton et al, EMBO Mol Med 2022), the Basto lab showed that centrosome amplification only occurs in a maximum of 3.2% of cells in a given ovarian cancer. Given the large discrepancy between the rate of centrosome amplification in the models here and in ovarian cancers ({greater than or equal to}80% vs {less than or equal to}3%), it is unclear whether the mechanism of apoptosis priming reported here is at play in a clinical setting. It is unclear whether the low rate of centrosome amplification observed in cancers can predispose response to a particular inhibitor, as suggested, particularly when centrosome amplification in {greater than or equal to}80% of cells 1) only induced apoptosis priming in 2 of 3 cell lines (Fig. S4F) and 2) induced relatively modest drug sensitivity (Fig. S4J). If it were shown in an additional experiment that induction of centrosome amplification in a small minority of cells, as occurs in patient tumors, increases MOMP priming and drug response, this would substantially increase the significance of the study.

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1. General Statements [optional]

The findings presented in this manuscript are original and have not been previously published, nor is the manuscript under consideration for publication by another journal. The authors of this manuscript declare to have no conflicts of interest.

1. Description of the planned revisions

We believe that incorporating the suggested corrections and conducting the additional experiments recommended by the reviewers will significantly enhance the quality of this study. These revisions will not only bolster the current conclusions but also broaden the relevance and applicability of our work to a wider scientific audience, extending beyond the field of virology.

As outlined in the following sections, we are fully committed to implementing the experiments proposed by the reviewers and making the necessary modifications to the manuscript in line with their suggestions. Our responses to each specific comment are provided below.

Reviewer #1

Evidence, reproducibility and clarity

Summary: Several target cell entry pathways have been described for different viruses, including endocytic/ fusion pathways, some which are dynamin-dependent.

Here the authors exploited cell lines with multiple dynamin gene disruptions and other cell biological tools, as well as a phenotypic range of previously characterized viruses, to evaluate the relative importance of dynamin and actin for entry of viruses, including SARS-CoV-2.

In cells that lack the serine protease TMPRSS2, dynamin depletion blocked uptake and infection by SARS-CoV-2. Increasing the input virus partially rescued SARS-CoV-2 infection in the absence of dynamin, and both dynamin-dependent and dynamin-independent entry pathways were inhibited by drugs that disrupt actin polymerization.

Examination by electron microscopy indicated that the dynamin-independent endocytic process was clathrin-independent, in that, in the absence of dynamin, the majority of Semliki Forrest Virions were detected in bulb-shaped, non-coated pits. When TMPRSS2 was expressed, SARS-CoV-2 infection was rendered dynamin-independent.

Significance

Overall, the experiments are expertly performed, the results and conclusions are convincing, the text is clearly written and accurately describes the data, and the manuscript makes an important contribution to a complex and important topic in the cell biology of virus infection. It would be reasonable for the authors to publish the manuscript with the current data.

That being said, we have two main questions/comments:

1. The authors point out that SFV differs from SARS-CoV-2 in that it required actin only for the dynamin-independent entry. The EM experiments were done with SFV, not with SARS-CoV-2. This raises the question of the relevance for SARS-CoV-2 of the interesting finding that, in the absence of dynamin, SFV associated with non-coated pits.

If the authors had the tools to do similar EM experiments with SARS-CoV-2, it would be nice to include those results. Otherwise, it is fine to discuss/speculate about SARS-CoV-2 regarding this issue.

RESPONSE:As requested by the reviewer, we are currently perform the suggested EM analysis of SARS-CoV-2 entry in the presence and absence of dynamins.

1. The authors show that TMPRSS2 allows the original Wuhan strain and Delta Variant of SARS-CoV-2 to bypass the need for dynamin. This is presumably because TMPRSS2 allows SARS-CoV-2 to fuse at the plasma membrane, precluding need for endocytosis altogether. The authors also mention literature claiming that Omicron is more dependent upon endocytosis than the Wuhan and Delta variants. If the authors had data with Omicron it would be really nice to include it.

RESPONSE: We have already conducted this experiment and have incorporated the quantitative results into the updated version of the manuscript, now presented as Figure 8.

There were some minor typos/grammar/other quoted here:

• Ultrastructural analysis by electron microscopy showed that this dynamin-independent endocytic processes - cell injests particles and nutrients by encoulfing them - some viruses have been show

RESPONSE: Thank you for noticing the error. We have modified the text as: “Ultrastructural analysis by electron microscopy showed that this dynamin-independent endocytic processes appeared as 150-200 nm non-coated invaginations that have been shown to be efficiently used by numerous mammalian viruses, including alphaviruses, influenza, vesicular stomatitis, bunya, adeno, vaccinia, and rhinovirus.”.

• The final step of an endocytic vesicle formation culminates with the pinching of vesicle off from the PM into the cytoplasm

RESPONSE: We have modified the sentence as: “The concluding stage of endocytic vesicle formation is marked by the vesicle being pinched off from the plasma membrane and released into the cytoplasm.”

• For other viruses, such as respiratory viruses (This word is a little strange here since influenza was mentioned in the last sentence.)

RESPONSE: Thank you for noticing the error, we have removed the mention to respiratory viruses: “ For other viruses (including coronaviruses), the fusion is triggered by proteolytic cleavage of the spike proteins that, once cleaved, undergo conformational changes leading first to the insertion of the viral spike into the host membrane and, upon retraction, the fusion of viral and cellular membranes9,10.”.

• Viruses that use a receptor that is internalized by dynamin-dependent endocytosis (e.g. CPV and the TfR) (just reminding that TfR is not a virus)

RESPONSE: We have amended the sentence to avoid misunderstandings: “Viruses (e.g. CPV) that use a receptor (e.g. TfR) that are internalized by dynamin-dependent endocytosis cannot efficiently infect cells in the absence of dynamins.”.

• that appeared surrounded by an electron dense coated

RESPONSE: We have corrected the typo: “In MEFDNM1,2 DKO cells treated with vehicle control, TEM analysis revealed numerous viruses at the outer surface of the cells (Figure 4 A), as well as inside endocytic invaginations that were surrounded by an electron dense coat, consistent with the appearance of clathrin coated pits47,48 (CCP) (Figure 4 B).”

• The main virial receptor could be internalized using two endocytic

RESPONSE: We have corrected the typo: “The main viral receptor could be internalized using two endocytic mechanisms, one mainly available in unperturbed cells (e.g. dynamin-dependent), the other activated upon dynamin depletion (i.e. dynamin independent).”

• Virus infection was determined by FACS analysis of virial induced EGFP

RESPONSE: We have corrected the typo: ‘Virus infection was determined by FACS analysis of EGFP (VAVC and VSV), mCherry (SINV) or after immunofluorescence of viral antigens using virus-specific antibodies (IAV X31 and UUKV).”.

Reviewer #2

Evidence, reproducibility and clarity

Summary: Ohja et al. present an interesting study investigating dynamin independent endocytic entry mechanism of viral infection. Using a genetic KO of 2 dynamin isoforms they show impacts on the infection of a range of large and small DNA and RNA viruses.

They go onto show that SARS-CoV-2 may utilise a dynamin independent mechanism of infection that requires an intact actin cytoskeleton.

Significance

This work is of interest to the field of virology and has the potential to answer previously understudied entry mechanisms important for a wide range of viruses. It is a well presented piece of work overall.

Major Comments:

• The abstract does not in my opinion reflect the content of the paper and is too 'SARS-CoV-2' centric. The work involves the use of a range of viruses to first define a mechanism that is applicable to SARS-CoV-2 and I think the abstract and title should reflect this.

RESPONSE: As per the reviewer's request, we will make revisions to the Title and Abstract. As a ‘non SARS-CoV-2-centric’ title we have amended the title to: Multiple animal viruses, including SARS-CoV-2, can infect cells using alternative entry mechanisms.

• In figure 1H the authors postulate that the reduced impact of dyn1,2 KO on SFV infection may be due to the interaction with heparin sulphate proteoglycans. Have the authors considered performing experiments using Heparin to block infection in their KO cells -/+ tamoxifen treatment?

RESPONSE: As per the reviewer's request, we will perform the proposed heparin experiments for SFV.

• In Figure 2 the authors assess infection of a range of viruses in dyn1,2 KO cells showing differential effects in some viruses but not all.

Have the authors confirmed whether tamoxifen treatment and the subsequent KD of dyn1,2 effect surface expression of the entry receptors for the viruses tested?

RESPONSE: Although in general blocking receptor endocytosis results in an increase in its cell surface levels, we agree with the Reviewer that the effect of dynamin depletion on receptors levels should be monitored at least for some of the viruses. To address the question raised by the reviewer, we will monitor the surface expression of SFV receptors VLDLR and ApoER2, and of the CPV receptor TfR in the presence and absence of dynamins.

We have already confirmed that there are no changes in the surface expression of SARS-CoV-2 receptor ACE2 in the absence of dynamin and this new data will be added to Figure 7.

• Additionally in this setting, dyn1,2 KD may impact on post entry steps in the virus life cycle such as the initial establishment of viral replication.

Can the authors either provide evidence as to how they have delineated measurement entry over replication or support their findings with psuedotyped virus-like-particles?

RESPONSE: This is an important point. As suggested by the reviewer, we will perform infection experiments in the presence or absence of Dynamins using VLPs pseudotyped with SFV and VSV spikes.

In addition, several of our experiments already indicate that upon dynamin depletion, the main block in virus infection is at the step of cell entry: 1) Upon DNM-depletion, the decrease in SARS-CoV-2 infection strongly correlates with a proportional block in spike (Figure 5) and virions (Figure 7) endocytosis; 2) exogenous expression of even low levels of the cell surface protease TMPRSS2 rescued SARS-CoV-2 infection in cells devoid of dynamins, indicating that merely by-passing endocytosis restores virus infection; 3) as shown in Figure 1 H for SFV, and in Figure 2 for multiple viruses, increasing the multiplicity of infection increases the number of infected cells, indicating that when virions access the dynamin-independent entry route, cells can be efficiently infected; 4) the infection of both negative strand (i.e. Uukuniemi virus, UUKV, Figure 2 ) and positive strand (i.e. human Rhino virus, HRVA1, Figure S3 D-E) RNA viruses, as well as DNA viruses (i.e. Vaccinia, Figure 2, and Adenovirus-5, Figure S3 B-C) are not affected by dynamin depletion, arguing against a general negative impact of dynamin depletion on cellular protein synthesis or other basic cell functions required for virus replication.

• Figure 3, given the unexpected results with the dynamin inhibitors, could this experiment be repeated with the dyn1-3 triple KD presented in figures 5-8?

RESPONSE: As requested by the reviewer, we will repeat the main inhibitor experiments presented in Figure 3 for SFV also in DNM TKO cells.

• Statistical analysis of imaging data in figure 4 would help with the conclusions.

RESPONSE: We have already performed the requested statistical analysis and modified Figure 4 accordingly.

• Additionally, the authors comment that in the KD cells the viruses were trapped in 'stalled CCPs'. What morphological changes determine this classification?

RESPONSE: As previously reported by Ferguson et al. (Developmental Cell, 2009), who developed the conditional MEF DNM knock out cell models, all CCPs are stalled at 6 days post induction of dynamin depletion. When observed by electron microscopy, stalled CCPs are readily identified by the presence of elongated, membranous narrow neck structures that connects the vesicle to the plasma membrane. We have clarified this description in the manuscript text and indicated the morphological features typical for a ‘stalled’ clathrin coated pit in Figure 4 F (black asterisk and white arrowheads).

• Concerning the SARS-CoV-2 work presented in figures 6-8, the use of exogenous expression of the viral entry receptors ACE2 and TMPRSS2 is a concern.

RESPONSE: While the reviewer appreciates that this is a necessary step to allow entry into their MEF-dyn1-3 KD cells, exogenous receptor expression can result in artificial entry of the virus.

• To support their findings, can the authors perform experiments in either cell lines endogenously expressing ACE-2/TMPRSS2 such as Calu3 or Caco2 and KD dyn1-3 using transient siRNA?

RESPONSE: This experiment poses a challenge due to the inherent difficulty of transfecting Caco2 and Calu3 cells and the potential difficulty of achieving a robust (>80%) simultaneous knockdown of all three dynamin isoforms. This is one of the reasons why we chose the conditional knock out approach. Nevertheless, we are committed to attempting this experiment.

• This approach would also provide more evidence for the role of TMPRSS2 presented in SF5 as the limited expression of this protease limits the robustness of the conclusions one can draw from the data presented.

RESPONSE: We appreciate the reviewer's observation, and to address this concern, we plan to not only perform siRNA knockdown of dynamins in cells with endogenous ACE2 and TMPRSS2 but also endeavor to elevate the expression levels of TMPRSS2 in our MEF DNM1,2,3 TKO ACE2 cells. It's worth noting, however, that this task presents a unique challenge since expression of TMPRSS2, a trypsin-like cell surface protease, leads to cell detachment even when expressed at moderate levels.

Minor comments & typo:

• Introduction paragraph 1 engulfing

RESPONSE: The sentence has been amended: “To gain access into the host cell's cytoplasm where viral protein synthesis and genome replication take place, most animal viruses hijack cell’s endocytic pathways1 by which the cell engulfs particles and nutrients into vesicular compartments. “.

• Pg 13 - typo in 'Figurre 6B'

RESPONSE: The typo has been corrected.

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

• Regarding the Reviewer 1 request on the use of Omicron variants, we have already conducted the requested experiments and have incorporated the quantitative results into the updated version of the manuscript, now presented as Figure 8.
• Regarding the Reviewer 2 request on the EM data, we have already performed the requested statistical analysis and modified Figure 4 accordingly. We have also clarified the EM descriptions in the manuscript text and indicated the morphological features typical for a ‘stalled’ clathrin coated pit in Figure 4 F (black asterisk and white arrowheads).

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

none

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Referee #2

Evidence, reproducibility and clarity

Summary

Ohja et al present an interesting study investigating dynamin independent endocytic entry mechanism of viral infection. Using a genetic KO of 2 dynamin isoforms they show impacts on the infection of a range of large and small DNA and RNA viruses. They go onto show that SARS-CoV-2 may utilise a dynamin independent mechanism of infection that requires a intact actin cytoskeleton.

Major Comments

The abstract does not in my opinion reflect the content of the paper and is too 'SARS-CoV-2' centric. The work involves the use of a range of viruses to first define a mechanism that is applicable to SARS-CoV-2 and I think the abstract and title should reflect this.

In figure 1H the authors postulate that the reduced impact of dyn1,2 KO on SFV infection may be due to the interaction with heparin sulphate proteoglycans, have the authors considered performing experiments using Heparin to block infection in their KO cells -/+ tamoxifen treatment

In Figure 2 the authors assess infection of a range of viruses in dyn1,2 KO cells showing differential effects in some viruses but not all. Have the authors confirmed whether tamoxifen treatment and the subsequent KD of dyn1,2 effect surface expression of the entry receptors for the viruses tested? Additionally in this setting, dyn1,2 KD may impact on post entry steps in the virus life cycle such as the initial establishment of viral replication. Can the authors either provide evidence as to how they have delineated measurement entry over replication or support their findings with psuedotyped virus-like-particles?

Figure 3, given the unexpected results with the dynamin inhibitors could this experiment be repeated with the dyn1-3 triple KD presented in figures 5-8.

Statistical analysis of imaging data in figure 4 would help with the conclusions. Additionally, the authors comment that in the KD cells the viruses were trapped in 'stalled CCPs'. What morphological changes determine this classification?

Concerning the SARS-CoV-2 work presented in figures 6-8, the use of exogenous expression of the viral entry receptors ACE2 and TMPRSS2 is a concern. While the reviewer appreciates that this is a necessary step to allow entry into their MEF-dyn1-3 KD cells exogenous receptor expression can result in artificial entry of the virus.

To support their findings, can the authors perform experiments in either cell lines endogenously expressing ACE-2/TMPRSS2 such as Calu3 or Caco2 and KD dyn1-3 using transient siRNA. This approach would also provide more evidence for the role of TMPRSS2 presented in SF5 as the limited expression of this protease limits the robustness of the conclusions one can draw from the data presented.

Minor comments

typo: Introduction paragraph 1 engulfing

Pg 13 - typo in 'Figurre 6B'

Significance

This work is of interest to the field of virology and has the potential to answer previously understudied entry mechanisms important for a wide range of viruses. It is a well presented piece of work overall.

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

Several target cell entry pathways have been described for different viruses, including endocytic fusion pathways, some which are dynamin-dependent. Here the authors exploited cell lines with multiple dynamin gene disruptions and other cell biological tools, as well as a phenotypic range of previously characterized viruses, to evaluate the relative importance of dynamin and actin for entry of viruses, including SARS-CoV-2. In cells that lack the serine protease TMPRSS2, dynamin depletion blocked uptake and infection by SARS-CoV-2. Increasing the input virus partially rescued SARS-CoV-2 infection in the absence of dynamin, and both dynamin-dependent and dynamin-independent entry pathways were inhibited by drugs that disrupt actin polymerization. Examination by electron microscopy indicated that the dynamin-independent endocytic process was clathrin-independent, in that, in the absence of dynamin, the majority of Semliki Forrest Virions were detected in bulb-shaped, non-coated pits. When TMPRSS2 was expressed, SARS-CoV-2 infection was rendered dynamin-independent.

Significance

Overall, the experiments are expertly performed, the results and conclusions are convincing, the text is clearly written and accurately describes the data, and the manuscript makes an important contribution to a complex and important topic in the cell biology of virus infection.

It would be reasonable for the authors to publish the manuscript with the current data. That being said, we have two questions/comments:

1. The authors point out that SFV differs from SARS-CoV-2 in that it required actin only for the dynamin-independent entry. The EM experiments were done with SFV, not with SARS-CoV-2. This raises the question of the relevance for SARS-CoV-2 of the interesting finding that, in the absence of dynamin, SFV associated with non-coated pits. If the authors had the tools to do similar EM experiments with SARS-CoV-2, it would be nice to include those results. Otherwise, it is fine to discuss/speculate about SARS-CoV-2 regarding this issue.
2. The authors show that TMPRSS2 allows the original Wuhan strain and Delta Variant of SARS-CoV-2 to bypass the need for dynamin. This is presumably because TMPRSS2 allows SARS-CoV-2 to fuse at the plasma membrane, precluding need for endocytosis altogether. The authors also mention literature claiming that Omicron is more dependent upon endocytosis than the Wuhan and Delta variants. If the authors had data with Omicron it would be really nice to include it.
3. There were some minor typos/grammar/other quoted here:
4. Ultrastructural analysis by electron microscopy showed that this dynamin-independent endocytic processes
5. cell injests particles and nutrients by encoulfing them
6. some viruses have been show
7. The final step of an endocytic vesicle formation culminates with the pinching of vesicle off from the PM into the cytoplasm
8. For other viruses, such as respiratory viruses (This word is a little strange here since influenza was mentioned in the last sentence.)
9. Viruses that use a receptor that is internalized by dynamin-dependent endocytosis (e.g. CPV and the TfR) (just reminding that TfR is not a virus)
10. that appeared surrounded by an electron dense coated
11. The main virial receptor could be internalized using two endocytic
12. Virus infection was determined by FACS analysis of virial induced EGFP

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Reply to the reviewers

FULL REVISION

The preprint of this article is uploaded in bioRxiv (doi:10.1101/2023.06.03.543550) (June 2023) and has been previously submitted and revised by peers in Review Commons. We attach the full Review, with a detailed answer to the Reviewers and a new revised version of the manuscript following the Reviewer’s comments and suggestions, adding new data, a new Supplementary figure, as well as a revision of the text and discussion. We are thankful to the reviewers for their helpful comments, which have further clarified some of aspects of our work and overall improved the quality of our manuscript.

All the line’s numbering mentioned in the point by point answer to the reviewers refer to the converted pdf of the revised manuscript, including the main figures.

Answers to Reviewer #1

Aísa-Marín et al. present a detailed scRNAseq description of two Nr2e3 mouse models the authors had published in Neurobiology of Disease in 2020. These two mouse models do not mirror known pathogenic variants in human patients, but are useful animal models to understand disease mechanisms in NR2E3-linked retinal degenerations. The present follow-up study has been carefully done, the bioinformatic analysis is sound and selected pathways have been validated at protein level by immunohistochemistry and Western blot. The impact of this data on photoreceptor development and maintenance is somewhat decreased because previous data by the groups of Joseph Corbo, Connie Cepko, Jeremy Nathans, Anand Swaroop and others have already shown several years ago upregulation of cone-specific genes in a spontaneous Nr2e3 mutant mouse, the rd7 mouse. In these papers, hybrid cones both expressing cone- and rod-specific genes have been described and coined 'cods'. The authors are encouraged to use already defined terms in their paper. For instance, the concept of 'half differentiated' photoreceptors is unclear and must be rephrased. In general, existing literature is not always integrated adequately into the submitted work. The detailed remarks are listed below.

We thank the reviewer for this suggestion to incorporate previous terminology in the field for the sake of clarity. Although it is true that previous authors have described hybrid photoreceptors, they have not quantified them, or compared their contribution to the different subpopulations of photoreceptors in different models of disease. For instance, there may be different types of hybrid photoreceptors, as they can be identified both within the cone and the rod populations, they show different characteristics and might perform different roles or else, be indicative of a pathological phenotype.

Taking into account the reviewer’s suggestion, we have carefully revised our text and figures and the terms “intermediate” or “half differentiated photoreceptors” have been substituted by the already existing term “hybrid photoreceptors” of “incompletely differentiated”. We have also included some context in previous work regarding ‘cods’.

See now lines 60, 146, 215, 271, 638-645 in the Discussion, Figure 7 legend and the Graphical Abstract for changes in terminology, and also sentences in lines 518-522, for reference to previous works.

Reviewer #1

One important question the authors must also address in their scRNAseq analysis is why the well described 'mixed' S- and M-opsin expressing cones do not seem detectable, are actually not even mentioned?

We sincerely thank the reviewer for this comment, as it is a relevant piece of information that we missed in our previous analysis. Cones are usually classifed according to the type of opsin they express. In mouse, previous work has described cones expressing solely S- or M-opsins, but also cones that co-express both types of opsins. Indeed, we find these three types of cones, overlapping partially with our cone subpopulations, which are defined by a larger number of signature genes. As previously described, merging the results of the wild-type with the two mutants demonstrate that most cones co-express both opsins (roughly 46%), S- and M-opsins are expressed exclusively in around 13% cone cells each, and somewhat surprisingly around 28% of cones do not express any opsin (Fig. EVF6). However, the dissection of cone results by genotype is more informative, as the percentages vary according to the mutant genotype. In the mutants, the percentage of cones expressing no opsins is higher than in the wild-type at the expense of the cones that should express solely S-opsin (data in EVF5). Again reflecting the impact of Nr2e3 mutations on the differentiation of cones and reinforcing our main message.

We have introduced several sentences in the text to reflect this results and refer to this new figure EVF6 (see lines 292-307 in the Results as well as 575-580 in the Discussion sections.

Reviewer 1. Detailed comments:

1. Graphical abstract: replace 'half differentiated' by incompletely differentiated or similar

As detailed above, we have followed the suggestion of the reviewer and throroughly revised all the text and all Figures. “Half differentiated” and “intermediate photoreceptors” have been substituted by “incompletely differentiated” and “hybrid photoreceptors”, respectively.

1. l.86: to my best knowledge, the shorter isoform has only been described at transcript level in humans, no evidence at protein level, please clarifiy. Please also state that the isoform lacking exon 8 is due to retention of intron 7.

Following the suggestion of the reviewer, we have clarified that the short NR2E3 transcript isoform is due to retention of intron 7, both in human and mouse. We have also clarified that in human, the protein has been computationally predicted, whereas there are experimental evidences in mouse. (lines 94-104).

1. l.89: lacks repressor and dimerization domains. Exon 8 is not coding all repressor and dimerization domains. The authors do not mention neither the D-box in the DBD that also contributes to dimerization, in addition to the LBD (von Alpen et al., Hum Mut, 2015). Furthermore, repressor domain should be presented in the context of the auto-repressed structure of NR2E3 (Zhu et al., Genes Dev, 2015).

We agree with the reviewer that the original text was simplified. For the sake of clarity and following his/her suggestion we now include more context about the structure of NR2E3 and included the suggested references (lines 87-93).

See also below the answer to the points 6, 9 and 13, which are also related.

1. l.90: typo NR2E3

The corresponding line is now on line 105 and the typo has been corrected.

1. l.93-106: incorrect, please rewrite whole paragraph. There is only one single pathogenic variant leading to NR2E3-Gly56Arg-linked autosomal dominant retinitis pigmentosa, all other pathogenic variants are recessive and cause ESCS!

Now these paragraph starts in line 105. We agree with the reviewer that so far only mutation Gly56Arg in NR2E3 is associated to autosomal dominant retinitis pigmentosa. however there are also some (even if few) NR2E3 mutations associated to autosomal recessive forms of RP, in addition to the most well known autosomal recessive mutations that cause ESCS. Here we provide a selection of reports supporting NR2E3 as causative of arRP (that are some more included in HMGD).

In order to avoid further confusion to some readers, we also include these references in the new version (see lines 109-112).

• Gerber, S. et al. The photoreceptor cell-specific nuclear receptor gene (PNR) accounts for retinitis pigmentosa in the Crypto-Jews from Portugal (Marranos), survivors from the Spanish Inquisition. Hum Genet 107, 276–284 (2000). https://doi.org/10.1007/s004390000350
• Kannabiran, et al. Mutations in TULP1, NR2E3, and MFRP genes in Indian families with autosomal recessive retinitis pigmentosa. Mol. Vis. 2012; 18:1165-74..
• Bocquet, B. et al. Homozygosity mapping in autosomal recessive retinitis pigmentosa families detects novel mutations. Mol Vis 19:2487-500.

  1. l.110: see comment above about dimerization.

We have modified the sentence in the text accordingly, see now line 125.

1. l.162: ok, but the main reason for restricting the analysis to photoreceptors should be the photoreceptor-specific expression of Nr2e3 though...

We have specified that Nr2e3 is solely expressed in photoreceptor cells (see line 176).

1. l.165: please specify what is the percentage of rods with respect to all retinal cells

The percentage of rods is around 77.7% of all cells (now on line 180). We value the suggestion, as it adds information to the reader. Therefore, the percentage of each main cell type is now included in Figure 1B.

1. l.210: idem l.89

We have modified the sentence in the text accordingly (now on lines 226-227).

1. l.310: replace 'halfway'

As specified in the answer to the first main point, we have throroughly revised the text and amended the references towards hybrid and incompletely differentiated photoreceptors.

1. l.337: as expected? please detail

We agree that the sentece was not clear. We have now clarified that our results agree with previous studies (see lines 370-371).

1. l.388: discuss also crystallins in other RD models, v.g. Rpe65 ko mice

We thank the reviewer for this suggestion and have included a brief description of the expression of crystallins in response to retinal stress in other RD models, and include the appropriate references (now on lines 422-428).

1. l.469: idem l.89

We have modified the sentence in the text accordingly (see lines 506-509).

1. l.526: Please discuss increase in non-apoptotic cell death markers with respect to published data in the rd7 mouse (Venturini et al., Sci Rep, 2021)

We have included published data in the rd7 mouse and discussed that multiple non-apoptotic cell death markers might be activated in response to NR2E3 disfunction (see lines 587-593).

1. l.580: the proposed dominant negative effect is overtly speculative and not supported by any presented data, please remove.

We have rewritten the sentence removing the dominant negative effect and referring exclusively to our results.

Answers to Reviewer #2

Aísa-Marín et al. present a detailed scRNAseq description of two Nr2e3 mouse models the authors had published in Neurobiology of Disease in 2020. These two mouse models do not mirror known pathogenic variants in human patients, but are useful animal models to understand disease mechanisms in NR2E3-linked retinal degenerations. The present follow-up study has been carefully done, the bioinformatic analysis is sound and selected pathways have been validated at protein level by immunohistochemistry and Western blot.

Major comments:

1. Overall, the conclusions of the study are well supported by the results. The findings provide valuable insights into retinal development and the pathogenesis of NR2E3-associated retinal dystrophies in an animal model, which need to be validated in humans. This limitation should be noted in the manuscript.

Indeed, we agree that our work has used animal models, but further work in human-derived models (e.g. retinal organoids) should be performed to confirm these results. We have clarified this point in the Discussion section (see lines 649-650).

Include an explanation in the text about how the specificity of the different signals detected by immunohistochemistry was assessed.

The specificity of each antibody was assessed by introducing a negative control into the immunostaining procedure, wherein only the secondary antibody was used, as well as by comparison to the staining of the protein of interest in wild type or basal conditions reported in previous work from ours or other groups. This has been now specified in the corresponding Methods section (see lines 912-916).

Explain the observed high variability in the percentage of cones, particularly between the two deltaE8 mutants (Figure 3C).

We believe that the main characteristic of the Nr2e3-mutant retinas is that photoreceptors are not adequately differentiated and thus, affected photoreceptor subpopulations, in this case cones, degnerate and die. The pathogenic phenotype might be somewhat variable between animals from the same genotype (as it also happens in siblings carrying the same mutation). The deltaE8 mutants show a very different cone subpopulation pattern compared to wild-types and they clearly cluster with the other mutant retinas. For instance, cones of subpopulation cone4 might have all died.

We take note of the question posed by the reviewer, and thus have included a graph of the absolute number of cones in each subcluster per retina and genotype, which may help the reader (see new Fig 3C, panel on the right).

Explain why PARP-1 signals in Figure 6E are so thick and intense. Why this thick pattern is also present in the wild type retina?

The IHC of mouse tissue sections using antibodies of mouse origin can result in background by secondary antibody binding to the endogenous Igs (as reported in Eng et al, 2016, https://doi.org/10.1093/protein/gzv054). The PARP-1 antibody is a mouse monoclonal antibody (Abcam, ab14459). The strong signal that we observe in the INL, IPL, and GL of the retina is typically found when using primary mouse antibodies in mouse tissues and corresponds to the reaction of the secondary anti-mouse antibodies binding to the endogenous IgGs in the blood vessels of the retina (we obtain the same result using the secondary antibody as a negative control, see answer to point 2).

For the sake of clarity, we have clarified this background staining in the corresponding figure legend (lines 831-834).

Reviewer #2

Minor comments:

1. Describe the abbreviations used in the text, such as PARP-1, MLKL, IRD, and VADC.

A list of abbreviations has been included at the end of the main text (see lines 663-672).

1. Improve the visibility of number 4 in Figure 3A and describe the meaning of the insert.

Figure 3A has been amended accordingly

1. Label the X-axis (cone subclusters) in Figure 3E.

The X-axis is now correctly labelled in Figure 3E.

1. Describe the meaning of the insert in Figure 4A.

Figure 4A legend now contains the meaning of the insert.

1. Indicate the relationship among inserts in Figure 4F.

Figure 4F and legend have been modified to clarify the meaning of the insert.

1. Use an arrow to indicate the higher expression of CSTB in the cone-rich invaginations in the mutant retinas (Figure 6A).

The Figure 6A has been modified to include white arrowheads indicating the high expression of CSTB in the invaginations of the mutant retinas. This is also indicated in the corresponding Figure 6 Legend (lines 819-820.

1. Revise the Y-axis values in Figure 6B, as they do not correspond to a percentage. Please, provide an explanation for the number of symbols displayed in this panel.

The Y-axis was previously expressed on a per-unit basis. For the sake of clarity and following the reviewer’s suggestion, it has now been appropriately modified to percentage of CSTB colocalizing with opsins.

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Referee #2

Evidence, reproducibility and clarity

Aísa-Marin et al. present a study on alterations in photoreceptor cell fate in NR2E3-associated diseases. The results convincingly reveal the presence of heterogeneous rod and cone populations in the mouse retina, as well as the existence of a novel cone pathway that results in hybrid cones characterized by the expression of genes associated with both cones and rods. Furthermore, the authors show that functional alteration of NR2E3 affects the expression of rod and cone signature genes, providing an interesting animal model to unveil the molecular mechanism underlying these retinal disorders.

Major comments:

1. Overall, the conclusions of the study are well supported by the results. The findings provide valuable insights into retinal development and the pathogenesis of NR2E3-associated retinal dystrophies in an animal model, which need to be validated in humans. This limitation should be noted in the manuscript.
2. Include an explanation in the text about how the specificity of the different signals detected by immunohistochemistry was assessed.
3. Explain the observed high variability in the percentage of cones, particularly between the two deltaE8 mutants (Figure 3C).
4. Explain why PARP-1 signals in Figure 6E are so thick and intense. Why this thick pattern is also present in the wild type retina?

Minor comments:

1. Describe the abbreviations used in the text, such as PARP-1, MLKL, IRD, and VADC.
2. Improve the visibility of number 4 in Figure 3A and describe the meaning of the insert.
3. Label the X-axis (cone subclusters) in Figure 3E.
4. Describe the meaning of the insert in Figure 4A.
5. Indicate the relationship among inserts in Figure 4F.
6. Use an arrow to indicate the higher expression of CSTB in the cone-rich invaginations in the mutant retinas (Figure 6A).
7. Revise the Y-axis values in Figure 6B, as they do not correspond to a percentage. Please, provide an explanation for the number of symbols displayed in this panel.

Significance

While it is known that NR2E3, an orphan nuclear receptor, plays a role in photoreceptor fate and differentiation during retinal development, its precise biological function remains poorly characterized. Additionally, the mechanisms by which inherited functional alterations of NR2E3 lead to RP or ESCS are not well understood. To address these unresolved questions, the authors employ a comprehensive experimental approach, including scRNAseq, RT-PCR, and immunohistochemistry, using retinas from two NR2E3 mutant mice. The technical procedures are well executed, and the complex scRNAseq data are rigorously analyzed and presented in a clear manner. Overall, this is a careful and meticulous study, that provides the fundamental basis for further verification in humans.

In my view, this research is highly relevant for the scientific community interested in the study of retinal development and inherited retinal dystrophies, specifically retinitis pigmentosa (RP) and enhanced S-cone syndrome (ESCS).

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Referee #1

Evidence, reproducibility and clarity

Aísa-Marín et al. present a detailed scRNAseq description of two Nr2e3 mouse models the authors had published in Neurobiology of Disease in 2020. These two mouse models do not mirror known pathogenic variants in human patients, but are useful animal models to understand disease mechanisms in NR2E3-linked retinal degenerations. The present follow-up study has been carefully done, the bioinformatic analysis is sound and selected pathways have been validated at protein level by immunohistochemistry and Western blot. The impact of this data on photoreceptor development and maintenance is somewhat decreased because previous data by the groups of Joseph Corbo, Connie Cepko, Jeremy Nathans, Anand Swaroop and others have already shown several years ago upregulation of cone-specific genes in a spontaneous Nr2e3 mutant mouse, the rd7 mouse. In these papers, hybrid cones both expressing cone- and rod-specific genes have been described and coined 'cods'. The authors are encouraged to use already defined terms in their paper. For instance, the concept of 'half differentiated' photoreceptors is unclear and must be rephrased. In general, existing literature is not always integrated adequately into the submitted work. The detailed remarks are listed below.

One important question the authors must also address in their scRNAseq analysis is why the well described 'mixed' S- and M-opsin expressing cones do not seem detectable, are actually not even mentioned?

Detailed comments:

Graphical abstract: replace 'half differentiated' by incompletely differentiated or similar l.86: to my best knowledge, the shorter isoform has only been described at transcript level in humans, no evidence at protein level, please clarifiy. Please also state that the isoform lacking exon 8 is due to retention of intron 7.

l.89: lacks repressor and dimerization domains. Exon 8 is not coding all repressor and dimerization domains. The authors do not mention neither the D-box in the DBD that also contributes to dimerization, in addition to the LBD (von Alpen et al., Hum Mut, 2015). Furthermore, repressor domain should be presented in the context of the auto-repressed structure of NR2E3 (Zhu et al., Genes Dev, 2015).

l.90: typo NR2E3

l.93-106: incorrect, please rewrite whole paragraph. There is only one single pathogenic variant leading to NR2E3-Gly56Arg-linked autosomal dominant retinitis pigmentosa, all other pathogenic variants are recessive and cause ESCS!

l.110: see comment above about dimerization

l.162: ok, but the main reason for restricting the analysis to photoreceptors should be the photoreceptor-specific expression of Nr2e3 though...

l.165: please specify what is the percentage of rods with respect to all retinal cells

l.210: idem l.89

l.310: replace 'halfway'

l.337: as expected ? please detail

l.388: discuss also crystallins in other RD models, v.g. Rpe65 ko mice

l.469: idem l.89

l.526: Please discuss increase in non‑apoptotic cell death markers with respect to published data in the rd7 mouse (Venturini et al., Sci Rep, 2021)

l.580: the proposed dominant negative effect is overtly speculative and not supported by any presented data, please remove.

Significance

Strength: first scRNAseq analysis in Nr2e3 mouse models, validation at protein level

Limitations: descriptive of gene expression, no mechanims identified, previous literature not adequately incorporated or missing

Audience: specialized, basic research

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Reply to the reviewers

Reviewer #1

The paper provides models of essential complexes formed in bacteria. These models have been predicted by AlphaFold2 and in some of the models, information from existing experimental structures is utilized. The predicted models have been calculated based on standard workflow procedures which are explained in detail and can be reproduced by others. The figures are informative and clear.

We are grateful for the reviewer's insightful comments, which have significantly contributed to improve our manuscript.

Suggestions for improvement:

1. The PDB accession codes of the experimental structures should be providedb. A comparison of the predicted models with the experimental structures should be provided (e.g. same orientation, superposition). In Fig. 6 for example, a figure with superposition or use of the same orientation would be more informative.

As suggested by the reviewer, we have included a new table (Table 1) listing all experimental structures discussed in the main text, with the corresponding PDB codes. All predictions are listed in Supplementary File 1. For instances with available PDB codes, we compared the predicted structures to the experimental ones (new Supplementary Figure 3). In Fig. 6, the structures were difficult to superimpose because the subunits in the complexes have different relative orientations. To help comparing both models, we have added a schematic representation (new Fig. 6c).

The paper will certainly generate many hypotheses based on the predicted models. In this respect, it would be useful for a wide audience in the bioscience field. However, the discussed models will need experimental verification by various techniques, such as X-ray crystallography, cryo-EM, SAXS, and structural proteomics. A more thorough analysis of the literature may help to improve the paper in this respect.

We acknowledge the reviewer's emphasis on the importance of experimental verification of the predicted models. We have conducted a thorough analysis of the literature to identify instances where experimental verification could complement our predictions. We identified several mutations in BirA, documented in the literature, that affect its interaction with AccB. __In BirA mutations M310L and P143T were found to induce a superrepressor phenotype (BirA lacks the capacity to biotinylate AccB). These mutations do not significantly affect the BirA active site, but can destabilize the BirA-AccB interface. __We have added this information in the main text. Also, we investigated whether our complexes have known crosslinks in the xlinkdb database(https://xlinkdb.gs.washington.edu/xlinkdb/). We found information for five of our predicted complexes. In all cases, the distance restraints identified by crosslinking (crosslinked lysines are ~15Å apart) are compatible with our models. We have incorporated these references into a new table in Supplementary File 1. Unfortunately, we could not find more information in the xlinkdb that can be used to further validate our complexes.

Supplementary table. Selected binary complexes modeled by AF2 whose structure is experimentally verified by cross-linking mass spectrometry.

Protein 1

Protein 2

Peptide 1

Pepitde 2

Species

acca

accd

VNMLQYSTYSVISPEGCASILWKSADK

IKSNITPTR

E. coli

dnak

grpe

DDDVVDAEFEEVKDKK

VKAEMENLR

E. coli

rpob

rpoc

GKTHSSGK

KGLADTALK

E. coli

bama

bamd

TVDIKPAR

DVSYLKVAYQNFVDLIR

A. baumannii

secd

secf

ILGKTANLEFR

MPSEDPELGKK

P. aeruginosa

Reviewer #2

This study attempts to identify the 'essential interactome' through combining information in presence/absence genomics across bacteria, information in the STRING database, and predictions from alpha-fold. Overall, the strategy is clear, and I do not have concerns about reproducibility and clarity.

We value the reviewer's constructive evaluation of our manuscript and we would like to thank the reviewer's feedback as it has significantly helped us in improving our manuscript.

Strengths: Clever approach to get at the essential interactome.

Weaknesses: Putative impact. It is clear why understanding which interactions are present are important. But even as the authors suggest, interactions are dynamic and there are plenty of other tools that people could use to find interactions (including AA Coev that the authors themselves cite). The counter argument the authors bring up is the high false positive rate of interactions that is solved by this method. While true, the stringency criteria for what constitutes an interaction in this paper is remarkably high: each protein within the interaction needs to be essential, and needs to have a high confidence score in STRING, and then there is a hyperparameter that dictates the level at which AlphaFold 2 is providing confident answers. In this sense, this is less about an 'essential' interactome, and more about an interactome that is present with the highest true positive rate (trading off with the ability to discover new interactions at a reasonable breadth).

We appreciate the reviewer's insights concerning the stringency criteria for defining interactions. Here, we provide a detailed justification for our selection criteria and show how it aligns with our goal of identifying high-confidence interactions.

1. Protein essentiality: In our model, interactions are considered essential if, and only if, both proteins involved are essential, providing a conservative estimate for the essential interactome. In our revised manuscript, we explored the possibility the potential for two non-essential proteins to form an essential interaction by investigating synthetically lethal interactions. Out of all synthetic lethal interactions in * coli*, only 28 interactions were identified, and only two could be modeled with an ipTM score > 0.6. Likely, these non-essential proteins operate in parallel or compensatory pathways instead of interacting directly. These findings lend support to our hypothesis and suggest that our interactome encompasses most essential interactions.
2. Conditional essentiality: While we concur with the reviewer that our study does not address conditional essentiality, we would like to note that exploring conditional essential interactions across all the bacterial species discussed in our manuscript is currently unviable. Just as a matter of example, we checked the overlap in essential genes between Acinetobacter baumannii and Pseudomonas aeruginosa in the lung environment (Wang et al., 2014; Potvin et al., 2003). In that case, there is a minimal overlap between the two species, suggesting that conditional interactions might also be species-dependent. In our manuscript, we aimed to describe the core essential interactions for Gram-negative and Gram-positive bacteria under standard laboratory growth conditions. We agree that further research is needed to incorporate specific, context-dependent interactions to provide a complete, comprehensive view of the interactome. Nonetheless, we define here the first bacteria essential interactome that, in our opinion, marks a significant step towards understanding bacterial cell metabolism and holds relevance in applications such as developing broad-spectrum antibiotics.
3. Confidence of the interaction: All existing methods to predict protein-protein interactions, including those based on coevolution, suffer from poor performance metrics. Most of them generate many false positive interactions while missing important ones. Without the aim of being exhaustive, here we reproduce a table of some of the latest computational methods to predict PPIs. Table 1. Performance of state-of-the-art PPI prediction methods (Huang et al., 2023).

Methods

AUPRCa

*SGPPI *

0.422

Profppikernelb

0.359

PIPRc

0.342

PIPE2b

0.220

SigProdb

0.264

a AUPRC denotes the average AUPRC value of 10-fold cross-validation.

It is clear from the data that such methods are not mature enough to be used as confident predictors. Hence, we decided to resort to validated interactions in the String database, which is one of the most comprehensive PPI databases__. In this revised version, we have expanded our data set to include all experimentally labeled interactions in the String database, even those with a low probability (experimental score > 0.15). The addition of these new interactions __increased the total number of interactions tested from 1089 to 1402 and generated 38 new models for Gram-negative species (13 with high accuracy) and 275 new models for Gram-positive bacteria (18 with high accuracy). All interactions are now included in the Supplementary File 1 and high accuracy models will be deposited on Model Archive after acceptance.

Alphafold (AF2) criterion for complex prediction. Although AF2 has its limitations, its accuracy in predicting bacterial complexes is consistently high. In various benchmarking studies, AF2 Multimer accurately predicted between 70-75% of tested complexes, with almost 90% of them being of medium-to-high quality (Evans et al., Yin et al., 2022). While there might be some minor deviations, AF2 can largely capture the bacterial essential interactome accurately. In the revised version, we compare pDockQ and pDockQ2 metrics with our ipTM criterion to define confident models. We observed that both pDockQ and pDockQ2 metrics were capable of identifying highly reliable complexes, but also disregarded actual complexes (Supplementary Figure 1). Thus, we decided to retain our initial criterion, based on ipTM scores, which is consistent with other authors who used similar ipTM thresholds to model bacterial interactions (e.g., O’Reilly et al., 2023).

In summary, although our methodology has inherent limitations, we believe that our approach is sound and can give a comprehensive and realistic view of the bacterial essential interactome. We hope that these new insights further substantiate our approach.

I don't know of too many studies that use AlphaFold 2 in this way. This was clever. However, there are plenty of studies that use phylogenomic information to infer interactions. In this sense, the core idea of the paper is not intrinsically novel.

We thank the reviewer for valuing our approach. Although other methods have been used to predict interactomes, our study, to the best of our knowledge, provides the first high-quality essential interactome for bacteria. We used experimental data (analysis of single deletion mutants) to define the essential interactions in bacteria. Other methods, either using phylogenomic information and/or deep learning tools to infer interactions, have a poor performance, as illustrated in the preceding table. Often, these methods yield a high number of interactions and, in many cases, show a bias towards overrepresented entries in the positive databases used to train the predictors (Macho Rendón et al., 2022). Also, while other methods lack detailed structural insights into the interactions, we offer structural models for every interaction tested.

Overall, I do feel this would be worth publishing as an expose of AF2 is capable of. I'm not sure of the impact it will have on researchers, however.

We appreciate the reviewer's positive feedback on our manuscript. Using AF2, we identified key interactions using only gene deletion mutant data. __This manuscript reveals new insights into the assembly of essential bacterial complexes, providing specific structural details to understand their stability and function. Additionally, __our work seeks to establish a methodology applicable to all bacterial species, guiding future research in this field. The approach taken in this study may expand drug targeting opportunities and accelerate the development of more effective antibiotics aimed to disrupt these essential interactions. In conclusion, the impact of the paper lies in its novel use of Alphafold2 to understand essential bacterial protein interactions, providing key insights into assembly mechanisms, and identifying new potential drug targets.

Reviewer #3

The selection of "essential" interactions is a bit arbitrary, given that their main criterion for selection is that both proteins are essential. Unfortunately, it's not always clear where the essential protein data is coming from. Authors cite Mateus et al. (ref 15) as source for E. coli, but I don't see an explicit list of essential genes in this paper (nor its supplement). For Pseudomonas the citation doesn't contain author information and for Acinetobacter essentiality only seems to refer to "essentiality" in the lung.

As a minimum, the author should provide a table with summary statistics for the essential proteins they are using, as this is the basis for the whole paper. Such a table should include the names of the species, the number of genes that are considered as essential, a very brief characterization of how essentiality was determined and the source for this information. For instance, are the genes listed in the Supplementary File congruent with the genes in the Database of Essential Genes (DEG) for these organisms? Finally, authors should indicate in that table which (essential) protein pairs are conserved across species, as this is another one of their selection criteria. Conservation is not necessary for an essential interaction, but it certainly makes it more likely.

We understand the reviewer's concerns regarding the selection of essential interactions and the need for a more thorough description of the sources of essential protein data. To address these concerns in the revised manuscript:

1. __We included a clear explanation of the sources for essential protein data, including proper citations for each organism in Supplementary File 1. __The selected studies were primarily sourced from the DEG database. If data was unavailable, we revised the literature for relevant studies. The DEG database's most recent update was on September 1, 2020. __A graphical summary of the datasets has been included in Supplementary Figure 12, __that shows the overlapping between the different studies.
2. We included comprehensive information for the essential proteins used in our study in Supplementary File 1. The file provides two tables detailing genes for both Gram-positive and Gram-negative datasets. Each table lists the gene names and their corresponding Uniprot IDs for every species in our study, as well as their orthologues in other organisms. Also, the reviewer was right in pointing out that for Acinetobacter baumannii, the study was conducted in the lung, which may bias the results as all other studies were performed in the test tube. To solve this, we replaced this study for Bai et al., 2021, that was performed in rich medium.

Author should also state whether they have verified that none of the random pairs are in the positive set.

We thank the reviewer for this comment. We certainly checked that none of the random pairs was present in the positive dataset. This clarification has now been added to the methods section.

This is also relevant because authors "retrieved all high-confidence PPIs between these proteins from the STRING database" which provides compound scores for interactions but that has often little to do with physical interactions (given that the scores factor in co-expression and several other criteria). In fact, I find STRING scores difficult to interpret for that very reason.

We appreciate the reviewer's comment to the use of combined interaction scores from the STRING database. We agree with the reviewer that STRING combined scores are somehow difficult to interpret because they combine different evidence of interaction. We decided to use the STRING combined scores to include interactions that may not have direct experimental evidence but are probable to interact according to other information (e.g., co-expression). However, to further examine the interactome we have also included in the revised version all interactions with experimental evidence in String to complete our interactome. As mentioned in the response to Reviewer 1, __we expanded the tested interactions from 1089 to 1402. This resulted in 38 new models for Gram-negative species, with 13 being highly accurate, and 275 for Gram-positive bacteria, of which 18 were highly accurate. All interactions are now included in the Supplementary File 1 __and high accuracy models will be deposited on the Model Archive after acceptance.

The authors "reasoned that a given interaction would only be essential if and only if both proteins forming the complex are essential" - this sounds reasonable but doesn't capture synthetically lethal (genetic) interactions, that is, interactions between two proteins that are both non-essential but are essential in combination. Admittedly, I don't have a number of how many such cases exist, but there are such cases in the literature (e.g. Hannum et al. 2009, PLoS Genet 5[12]: e1000782, for yeast).

We thank the reviewer for bringing this point into discussion. We acknowledge that our reasoning does not capture synthetic lethality, which occurs when the loss of one of two individual genes has no effect on cell survival, but the simultaneous loss of both leads to cell death. In this case, the two genes or proteins are non-essential individually but become essential in combination. To cover synthetic lethality, we retrieved all synthetically lethal interactions found in Escherichia coli, strain K12-BW25113 from the Mlsar database and included them in our pipeline. We identified 28 synthetically lethal PPIs (involving 45 proteins) and we modeled them with AF2. Only two interactions displayed an ipTM score > 0.6 (nadA-pncB and nuoG-purA). Hence, the number of interactions due to synthetic lethality seems to contribute low to the overall interactome. We believe that synthetic lethal partners often function in parallel or compensatory pathways, rather than directly interacting with each other. For example, in yeast, the genes RAD9 and RAD24 are synthetic lethal. RAD9 is involved in cell cycle checkpoints, while RAD24 is involved in DNA damage response. They function in related pathways but do not encode proteins that directly interact with each other. Hence, finding specific examples of proteins that are both synthetic lethal and directly interact might be challenging as the synthetic lethal relationship often reveals functional rather than physical interactions.

Apart from that, one could question the selection method more generally, given that for a biological process always essential and non-essential proteins work together, so I wonder why the authors didn't include additional proteins known to be involved in specific processes as this could make their predictions much more biologically meaningful.

We agree with the reviewer that accessory proteins are important to understand the biological context of interactions. In fact, in several sections of our manuscript, we included accessory proteins to fully describe the essential complexes. For example, in the cell division complex, we incorporated proteins like MreCD-RodZ from the elongasome to enhance the structural context of the interactions. However, a comprehensive explanation of all identified interactions and accessory proteins would extend beyond the scope of this manuscript and further lengthen an already extensive document. In our study, we sought to describe the fundamental interactions for both Gram-negative and Gram-positive bacteria. We anticipate that our findings will prompt additional research to confirm our hypotheses and enhance knowledge of these protein complexes within the proper cellular context.

In any case, to understand their choice better, authors should provide a table (in the main text) summarizing the proteins they actually analyze and discuss in more detail in their models. This would allow a reader to see which proteins are considered essential and which ones are missing. I would organize this by function / pathway / process, so these proteins are listed in a functional context.

We added Table 1 in the main text, listing all interactions described in the text. Table 1 includes the proteins involved in each complex, the ipTM score of the interaction, whether a PDB code is available for comparison and the functional classification of the interaction.

With regard to docking, please also discuss why you focus on iPTM, as there are other derived metrics from AF2 scores, such as pdockq based on if_plddt (e. g. Bryant et al, 2022), as well as external metrics to AF2 (physics-based methods such as Rosetta). Another option may be a modified versions of AF2 multimer, such as AFSample, which produces a greater diversity of models, allowing for more "shots on goal" and ultimately a higher success rate, assuming one has a reliable QC filter (I wonder how those compares to iPTM).

We did not use AFsample because is a very expensive computational approach that would require too many resources for the batch prediction of more than 1.400 complexes. AFsample generates 240x models, and including the extra recycles, the overall timing is around 1,000x more costly than the baseline. However, we acknowledge that using other metrics can be useful to further evaluate our models. Hence, we investigated how pDockQ and pDockQ2 metrics compare with ipTM score. We observed that pDockQ hardly correlates with ipTM (R = 0.328) whereas the improved metric pDockQ2 correlates much better (R = 0.649). All complexes described in the manuscript, which have an ipTM score higher than our threshold (0.6), have also a pDockQ2 score higher than 0.23, except for six interactions that have a lower pDockQ2 score. However, these scores improve when the interactions are modeled with accessory proteins in the complex. This somehow suggests that the ipTM metric better captures binary interactions when these are excluded from their context. __It is possible however, that pDockQ scores are better in discriminating false positive interactions than ipTM scores. Based on the strong correlation between the two metrics and the observation that ipTM may better capture binary interactions, we decided to keep our method in the manuscript. Other authors have employed analogous ipTM thresholds to model bacterial interactions (e.g., O’Reilly et al., 2023). Notwithstanding, __we also included pDockQ and pDockQ2 metrics in Supplementary File 1, so readers can evaluate complexes based on these metrics.

Minor comments:

1. 1, 3rd last line: "the essential interactome is a potentially powerful strategy to [...] identify new targets for discovering new antibiotics"

2. Figures and figure legends need to be explicit which species is represented (ideally with a Uniprot ID) and which structure was predicted by alphafold and which one has an experimental structure. Known structures should be indicated in a table, as suggested above.

3. Figure 5: LptF is too dark when printed, so a lighter color may be better.

4. Figure 6: The cryoEM and alphafold structures look quite different, so please discuss discrepancies between them (in terms of prediction or cryEM modeling). A schematic may be helpful to illustrate the differences in more clarity.

5. Figure 7: LolC is also too dark when printed. Make lighter.

6. Maybe in some cases it may be worthwhile looking at Consurf structures to see if the predicted inferfaces are indeed more conserved than the non-conserved parts.

We thank the reviewer for his/her insightful feedback on our manuscript. We have addressed all these comments as follows:

1. The statement on page 1 was revised as suggested.
2. We revised all figure legends to include the Uniprot IDs, and distinguish between predicted and experimental structures. We also included Table 1 and Supplementary File 1 for known structures.
3. We adjusted the colors in Figures 5 and 7 to enhance print visibility.
4. We provided a schematic to illustrate discrepancies between cryoEM and AlphaFold structures in Figure 6c.
5. We used Vespa to highlight conserved interfaces in the complexes described in the manuscript, as suggested. The figures displaying the conservation of interfaces in the complexes are now depicted in Supplementary Figure 2. A comparison between interface and surface conservation can be found in Figure 1f.

   The main significance of this study is its potential use for a better understanding of the protein complexes described in more detail (and the fact that alphafold can be applied in a similar fashion to many other complexes). This is why the individual sections need to be evaluated to process-specific experts (disclaimer: I have only worked on some of the complexes, but I am not an expert on any of them). I wonder if it would make more sense to break out some of the sections on individual complexes into separate papers, and then discuss them in more detail and with more context from previous studies. Complexes such as the divisome have a huge body of literature and it may be worth reviewing which structures are known and which ones are not. However, the dynamic and labile nature of these complexes have made it difficult for both crystallography as well as modeling to get a good structural understanding, but some of the models proposed here may be useful for overcoming some of these hurdles.

We appreciate the reviewer's suggestion. While we acknowledge the complexity of some of the individual complexes, such as the divisome, and the wealth of existing literature, we believe that the current manuscript provides a valuable comprehensive view on how AF2 can be used to predict essential protein complexes in bacteria. In our opinion, dividing the manuscript in separate pieces might dilute its scope. Nonetheless, we are exploring in our laboratory the interactions detailed in the manuscript, aiming to further expand the knowledge on these important complexes and their potential as targets for new antimicrobials.

References:

Bai J, Dai Y, Farinha A, et al. Essential Gene Analysis in Acinetobacter baumannii by High-Density Transposon Mutagenesis and CRISPR Interference. J Bacteriol. 2021; 203(12):e0056520.

Evans R, O’Neill M, Pritzel A, et al. Protein complex prediction with AlphaFold-Multimer.

bioRxiv. 2021; 2021.10.04.463034.

Huang Y, Wuchty S, Zhou Y, Zhang Z. SGPPI: structure-aware prediction of protein-protein interactions in rigorous conditions with graph convolutional network. Brief Bioinform. 2023; 24(2):bbad020

Macho Rendón J, Rebollido-Ríos R, Torrent Burgas M. HPIPred: Host-pathogen interactome prediction with phenotypic scoring. Comput Struct Biotechnol J. 2022; 20:6534-6542.

O'Reilly FJ, Graziadei A, Forbrig C, et al. Protein complexes in cells by AI-assisted structural proteomics. Mol Syst Biol. 2023; 19(4):e11544.

Potvin, E., Lehoux, D.E., Kukavica-Ibrulj, I., et al. In vivo functional genomics of Pseudomonas aeruginosa for high-throughput screening of new virulence factors and antibacterial targets. Environmental Microbiology. 2003; 5: 1294-1308.

Wang N, Ozer EA, Mandel MJ, Hauser AR. Genome-wide identification of Acinetobacter baumannii genes necessary for persistence in the lung. mBio. 2014; 5(3):e01163-14.

Yin, R, Feng, BY, Varshney, A, Pierce, BG. Benchmarking AlphaFold for protein complex modeling reveals accuracy determinants. Protein Science. 2022; 31(8):e4379.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Gómez-Borrego & Torrent-Burgas selected and modelled 1089 interactions between "essential" proteins in bacteria and generated 115 what they call "high-accuracy" models (using alphafold2). Some of the models potentially provide new insight into structure-function relationships of various biological processes and thus may serve as basis for further exploration.

Major comments

Methods

The selection of "essential" interactions is a bit arbitrary, given that their main criterion for selection is that both proteins are essential. Unfortunately, it's not always clear where the essential protein data is coming from. Authors cite Mateus et al. (ref 15) as source for E. coli, but I don't see an explicit list of essential genes in this paper (nor its supplement). For Pseudomonas the citation doesn't contain author information and for Acinetobacter essentiality only seems to refer to "essentiality" in the lung.

As a minimum, the author should provide a table with summary statistics for the essential proteins they are using, as this is the basis for the whole paper. Such a table should include the names of the species, the number of genes that are considered as essential, a very brief characterization of how essentiality was determined and the source for this information. For instance, are the genes listed in the Supplementary File congruent with the genes in the Database of Essential Genes (DEG) for these organisms? Finally, authors should indicate in that table which (essential) protein pairs are conserved across species, as this is another one of their selection criteria. Conservation is not necessary for an essential interaction, but it certainly makes it more likely.

Author should also state whether they have verified that none of the random pairs are in the positive set.

This is also relevant because authors "retrieved all high-confidence PPIs between these proteins from the STRING database" which provides compound scores for interactions but that has often little to do with physical interactions (given that the scores factor in co-expression and several other criteria). In fact, I find STRING scores difficult to interpret for that very reason.

The authors "reasoned that a given interaction would only be essential if and only if both proteins forming the complex are essential" - this sounds reasonable but doesn't capture synthetically lethal (genetic) interactions, that is, interactions between two proteins that are both non-essential but are essential in combination. Admittedly, I don't have a number of how many such cases exist, but there are such cases in the literature (e.g. Hannum et al. 2009, PLoS Genet 5[12]: e1000782, for yeast, or Babu et al. 2014 PLoS Genet 10[2]: e1004120, for E. coli).

Apart from that, one could question the selection method more generally, given that for a biological process always essential and non-essential proteins work together, so I wonder why the authors didn't include additional proteins known to be involved in specific processes as this could make their predictions much more biologically meaningful.

In any case, to understand their choice better, authors should provide a table (in the main text) summarizing the proteins they actually analyze and discuss in more detail in their models. This would allow a reader to see which proteins are considered essential and which ones are missing. I would organize this by function / pathway / process, so these proteins are listed in a functional context.

With regard to docking, please also discuss why you focus on iPTM, as there are other derived metrics from AF2 scores, such as pdockq based on if_plddt (e. g. Bryant et al, 2022), as well as external metrics to AF2 (physics-based methods such as Rosetta).

Another option may be a modified versions of AF2 multimer, such as AFSample, which produces a greater diversity of models, allowing for more "shots on goal" and ultimately a higher success rate, assuming one has a reliable QC filter (I wonder how those compares to iPTM).

These details are required to make the study truly transparent and reproducible.

Results

Given the methodological caveats given above, some of the results are certainly convincing and interesting to a broader readership.

However, since their models are predictions, it would be important to provide some guidance on which interactions are the highest-scoring and thus the most promising for further validation. I would thus include a list of interactions for each functional group and their scores. This would be more useful than the rather difficult to interpret Figure 2 (even though it looks nice - or just add a table and leave Figure 2). Such a table could (and should) also include other data, such as references that support those top-ranking (but still unknown) interactions, or which structure are already known.

Minor comments

P. 1, 3rd last line: "the essential interactome is a potentially powerful strategy to [...] identify new targets for discovering new antibiotics"

Figures and figure legends need to be explicit which species is represented (ideally with a Uniprot ID) and which structure was predicted by alphafold and which one has an experimental structure. Known structures should be indicated in a table, as suggested above.

Figure 5: LptF is too dark when printed, so a lighter color may be better.

Figure 6: The cryoEM and alphafold structures look quite different, so please discuss discrepancies between them (in terms of prediction or cryEM modeling). A schematic may be helpful to illustrate the differences in more clarity.

Figure 7: LolC is also too dark when printed. Make lighter.

Maybe in some cases it may be worthwhile looking at Consurf structures to see if the predicted inferfaces are indeed more conserved than the non-conserved parts.

Significance

The main significance of this study is its potential use for a better understanding of the protein complextes described in more detail (and the fact that alphafold can be applied in a similar fashion to many other complexes).

This is why the individual sections need to be evaluated to process-specific experts (disclaimer: I have only worked on some of the complexes but I am not an expert on any of them).

I wonder if it would make more sense to break out some of the sections on individual complexes into separate papers, and then discuss them in more detail and with more context from previous studies. Complexes such as the divisome have a huge body of literature and it may be worth reviewing which structures are known and which ones are not. However, the dynamic and labile nature of these complexes have made it difficult for both crystallography as well as modeling to get a good structural understanding, but some of the models proposed here may be useful for overcoming some of these hurdles.

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Referee #2

Evidence, reproducibility and clarity

This study attempts to identify the 'essential interactome' through combining information in presence/absence genomics across bacteria, information in the STRING database, and predictions from alpha-fold. Overall, the strategy is clear, and I do not have concerns about reproducibility and clarity.

Significance

General Assessment:

Strengths: Clever approach to get at the essential interactome.

Weaknesses: Putative impact. It is clear why understanding which interactions are present are important. But even as the authors suggest, interactions are dynamic and there are plenty of other tools that people could use to find interactions (including AA Coev that the authors themselves cite). The counter argument the authors bring up is the high false positive rate of interactions that is solved by this method. While true, the stringency criteria for what constitutes an interaction in this paper is remarkably high: each protein within the interaction needs to be essential, and needs to have a high confidence score in STRING, and then there is a hyperparameter that dictates the level at which AlphaFold 2 is providing confident answers. In this sense, this is less about an 'essential' interactome, and more about an interactome that is present with the highest true positive rate (trading off with the ability to discover new interactions at a reasonable breadth).

Advance: I don't know of too many studies that use AlphaFold 2 in this way. This was clever. However, there are plenty of studies that use phylogenomic information to infer interactions. In this sense, the core idea of the paper is not intrinsically novel.

Audience: specialized. Overall, I do feel this would be worth publishing as an expose of AF2 is capable of. I'm not sure of the impact it will have on researchers however.

Field of expertise: Statistical genomics.

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Referee #1

Evidence, reproducibility and clarity

The paper provides models of essential complexes formed in bacteria. These models have been predicted by AlphaFold2 and in some of the models, information from existing experimental structures is utilized. The predicted models have been calculated based on standard workflow procedures which are explained in detail and can be reproduced by others. The figures are informative and clear.

Suggestions for improvement:

• a. The PDB accession codes of the experimental structures should be provided
• b. A comparison of the predicted models with the experimental structures should be provided (e.g. same orientation, superposition). In Fig. 6 for example, a figure with superposition or use of the same orientation would be more informative.

Significance

The paper will certainly generate many hypotheses based on the predicted models. In this respect, it would be useful for a wide audience in the bioscience field. However, the discussed models will need experimental verification by various techniques, such as X-ray crystallography, cryo-EM, SAXS, and structural proteomics. A more thorough analysis of the literature may help to improve the paper in this respect.

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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

In the present paper, authors study the effect of the L250P mutation on Fbxo7, leading to a severe infantile onset motor impairment.

They show by co-IP that the mutation selectively ablates the interaction of Fbxo7 with the protesomal adaptor PI31. It induced a reduction in endogenous Fbxo7, which had a reduced half-life, and concomitantly of PI31 levels, without affecting its half-life, and a reduction in the expression of some subunits of the proteasome, and altogether, a reduction in its activity. To identify substrates of SCF Fbxo7 reliant on PI31 they used some databases and proteins arrays and identified MiD49 and MiD51, involved in mitochondrial fission machinery. Authors show PI31 acts as an adaptor and allows SCFfbxo7 ligase to ubiquitinate MiD49, therefore L250P mutation alters its substrate repertoire. It is shown Fbxo7 stabilizes Mid49 and Mid51. Importantly, reduced levels of Fbxo7 (KD) mimic the effect of the mutation.

Despite the affectation of MiD49, mitochondrial network appeared unaffected. However they observed that Fbxo7 L250P mutation led to a general alteration of the mitochondrial function: reduction of the mitochondrial mass, leading to reduced oxygen consumption, lower mitophagy and biogenesis and increased ROS production. Data are well presented, findings are convincing and complete and discussion seems appropriate.

I just have some minor comments:

According to the data showing that Fbxo7 KD mimics the effects of the L250P mutation, it appears that the altered stabilization of Fbxo7 is a key event in the process and results observed. How do the authors explain the reduction of Fbxo7 half-life induced by the mutation?

I would find more appropriate that to estimate the mitochondrial mass, the relative area or volume of Mitotracker green fluorescence is quantified, rather than its average intensity.

It is not accurate to say TMRE is only able to enter mitochondria and fluorescence when there is an intact membrane potential. Rather, its accumulation is dependent on the mitochondrial membrane potential.

Significance

Authors provide a comprehensive study of the effects of the novel mutation L250P in Fbxo7 gene, leading to infantile onset PD. Findings are new and describe the mechanism this mutation changes the substrate repertoire of SCFFbxo7 ligase and affect mitochondrial function. The paper could be of interest to both clinical and basic researchers focused on PD and mitochondrial function.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this article, Sara Al Rawi and colleagues hypothesize that the homozygous L250P FBXO7 mutation identified in an infant with reduced facial and limb movements and axial hypotonia affects the Fbxo7-PI31 interaction domain. The authors used patient fibroblasts carrying the pathogenic mutation to show reduced expression of Fbxo7 and PI31 on those cells, and reduced proteasome levels and activity. Moreover, their data suggest that the L250P mutation affects the mitochondrial function and promotes increased levels of reactive oxygen species (ROS).

Major comments:

• The only thing that be argued is that Supplementary Table 1 containing the list of whole exome sequencing (WES) hits is missing. Please add it to the manuscript to check that the FBXO7 variant is the most plausible one considering the clinical phenotype of the affected individual.

Minor comments:

There are a few minor details that I would modify to improve the general readability of the manuscript: - The authors state that parents of the affected individual are "related", but do not specify the degree of consanguinity that they have. It was only in my second read of the manuscript that I realized that parents were consanguineous, and that the presence of a homozygous mutation made sense. It would help to state the degree of consanguinity between parents so that the reader can understand that a homozygous mutation is plausible. - In the clinical description of the patient, I would add the interpretation of a "developmental quotient (DQ) = 40", such as "a score <75 indicates a developmental delay", since some basic scientists may not be used to interpret those scores and cannot identify right away the degree of clinical impairment. - Many researchers are used to interpret the potential pathogenicity of a "candidate variant" using the CADD score. You can add this score to the paragraph where you mention the predicted pathogenicity of other in silico tests. - In the section "Fbxo7 stabilizes MiD49/51 protein levels", the beginning of the second paragraph: "To test whether knock-down of Fbxo7 levels phenocopies the effect of the L250P point mutation, [...]" is hard to understand. I would rewrite this first sentence in a different way to make it easier to read.

Significance

The manuscript is well written, and the results are coherent and supported by impressively detailed methods. The results of this manuscript are important for the advance of the movement disorders field. It shows how the novel L250P FBXO7 mutation in homozygous status can cause a very early onset (neonatal) movement disorder. Additionally, the functional analyses performed in patients' fibroblasts characterize very well the effect of this mutation on the cellular machinery showing proteasomal dysfunction, mitochondrial dysregulation, and ubiquitination alteration.

The content of the manuscript is interesting for a broad spectrum of individuals: from pediatric movement disorders specialists to basic researchers interested in proteasomal and mitochondrial dysfunction.

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Referee #1

Evidence, reproducibility and clarity

This study reports a human pediatric patient carrying a mutation in the Fbxo7/PARK15 gene. Several previous reports demonstrated that loss of Fbxo7/PARK15 gene function causes early-onset parkinsonian-pyramidal syndrome, but the precise underlying molecular mechanism remains to be elucidated. Based on studies with patient fibroblasts the authors suggest that Fbxo7 and its conserved binding partner PI31 regulate proteasomes and mitochondria, and that PI31 is an adaptor for the SCF Fbxo7 E3 ubiquitin ligase. The observations presented here are potentially interesting, but at this point they lack sufficient experimental evidence to support the main conclusions.

A general weakness of this study is that experiments focus on patient fibroblasts, and not neurons. Fbxo7/PARK15 patients as well as mouse mutants have neurological phenotypes, but no overt defects in skin or connective tissues. Therefore, it is not clear how the reported observations relate to the clinical symptoms. This is of particular concern since a conflicting report (Kraus et al., 2023) has found no change in basal mitophagy in Fbxo7 KO iNeurons.

The authors show that the proteasome regulatory protein PI31 is cleaved in Fbxo7 mutant cells. The cleavage and inactivation of PI31 upon inactivation of Fbxo7 was originally reported in Bader et al., 2011 (Cell 145, 371-82), but this paper is not cited. On the other hand the authors are citing a yet unpublished biorxiv preprint by Sanchez-Martinez et al. (https://www.biorxiv.org/content/10.1101/2022.10.10.511602v3) on the Drosophila Fbxo7 ortholog but another highly relevant preprint showing that transgenic expression of PI31 can extensively compensate for the inactivation of Fbxo7 in mice is not included (https://www.biorxiv.org/content/10.1101/2020.05.05.078832v1). This lack of consistency in citing prior works is concerning and should imperatively be rectified to provide a transparent and more accurate account of the novelty of the presented findings. Therefore, the bibliography of the manuscript is incomplete and relevant citations are missing.

The idea that PI31 is an adaptor for SCF-FBXO7 ubiquitination has not sufficient experimental support. The authors use the correlation of the L250P mutation not interacting with PI31 and not ubiquitinating MiD49 to propose that PI31 is an adaptor needed for MiD49 (and TOMM22 and Rpl23) ubiquitination by FBXO7 - this is an over-interpretation; this claim should be toned down or supported by further investigations.

FBXO7 can ubiquitinate MiD49 in vitro, but in vivo it appears to protect MiD49 from ubiquitination. Moreover, reduced FBXO7 levels (either by L250P mutation or knock down) result in decreased MiD49 and MiD51. There is no mechanistic explanation for these seemingly contradictory findings.

Mitochondrial homeostasis of patient fibroblasts appears aberrant. In particular, there seems a reduction of mitochondrial mass, reduced basal mitophagy and reduced respiration, which contrasts the report by Krauss et al. (2023). A potential explanation for these disparate observation is suggested by the decreased transcription of two mitochondrial transcription factors, PGC1α and PPARγ. How FBXO7 inactivation leads to this decrease in PGC1α and PPARγ or a decrease in basal autophagy is not clear.

In sum, there are some potentially interesting preliminary observations, but the study is not convincing because the results are over-interpreted and the analysis is not sufficiently rigorous.

Specific comments:

Figure 1 panel C has no loading control for total lysates.

Figure 2 panel B. The authors state that this experiment suggests direct interaction of PI31 with MiD49 (in the discussion they drop "suggests"). GST-pulldown with bacterially expressed GST-PI31 with MiD49/51 in vitro transcribed in rabbit reticulocyte lysate, which is less complex than HEK293 lysate, but not a purified system (for example, they contain proteasomes and other UPS components). This does not prove direct interaction. They show a Coomassie gel of the purified GST and GST-PI31, but not the reticulocyte lysate.

Figure 2 panels I and J. In panel I they show a decrease of Mi49 following FBXO7 KD, a main point of the paper that MiD49 is a FBXO7/PI31 substrate. However, in panel J for time zero of their hydrogen peroxide treatment time course it appears that Mi49 from the FBXO7 KD is as abundant if not greater than the Mi49 for the control time zero. Why? Even in the graph in panel K they start at the same level, though that probably is due to the way they normalize the data, which is not stated clearly.

The legend for figure 3 panel C states that the figure shows cells from control and the patient imaged under basal conditions or following treatment with 2-deoxyglucose, yet in the figure there are only two panels!?

For the proteasome activity assay, in the text they state that they use Suc-LLVY-AMC, which releases a fluorescent signal when proteolytically cleaved, but in the Materials and Methods they say that they use the Proteasome-Glo Chymotrypsin-like assay (Promega G8621), which is a two-step luminescent assay. These are not the same assays.

Finally, this ms is very similar to a bioxrchive paper from the Laman-lab, but there are some notable omissions:

1. In their bioxrchive paper they show a very clear decrease in LMP7(beta5i) protein in figure 1 panel D. This would go along with the decrease in other proteasome subunits, but this result is not mentioned in this manuscript. Why?
2. The bioXrchive figure 1 panel E was replaced here with a considerably lower quality Western blot (Figure 1 panel F, using tubulin instead of GAPDH as the loading control). Again, the reason is not clear.

Significance

A better understanding of how mutations in Fbxo7/PARK15 cause juvenile onset neuronal degeneration would be very important and significant. Unfortunately, the current study is not sufficiently rigorous while the results are over-interpreted which will confuse readers.

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Reply to the reviewers

Please see the attached pdf "Response to Reviewer" with all reviewer comments, our responses, and descriptions of the edits in the text supplementary information, and figures.

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Referee #3

Evidence, reproducibility and clarity

This paper by Sharma et al describes ultrastructural changes in the polar tube (PT) of the microsporidian species Varimorpha necatrix upon PT firing. The relationship between cargo transport and the diameter of the PT, as well as the thickness of the PTP coat, are investigated. Moreover, low-resolution sub-tomogram averaging (STA) reveals that ribosome dimers occasionally arrange into spiral-like arrays on the inner surface of the bilayer lining the PTP coat. The data are well presented and, in most parts, appropriately interpreted. I have the following comments that I suggest should be addressed.

Major:

1. The authors suggest that the ribosomes in the arrays are dimers. Yet, figure 2c only shows a STA map of a 70S particle. A map of the dimer should be included to support this significant message of the paper.
2. Do the authors see any 70S particles and if so, how common are they? 3D classification would clarify this.
3. The authors put a lot of emphasis on the finding of array-like ribosomes within PTs. However, these appear to be present in only a minority of the cases. Moreover, similar ribosome arrays have previously not been seen in other microsporidian PTs. This raises the question of how significant these arrays are. Do they only occur in some microsporidia, or only at certain time points? This should be more clearly discussed, for example in lines 232 - 233. Also, do the authors suggest that this is a specific organisation or just a matter of close packing?
4. As the arrays are only occasionally observed, the statement that ribosomes are transported through PTs in a spiral-like fashion should also be toned down in the abstract and throughout the manuscript. The fact that the arrays are only seen sometimes, makes the finding even more interesting, as it may infer a dynamic reorganisation process.
5. The ribosome arrays appear to co-localise with the membrane. If this is the case, does the membrane show up in their STA? If so, it would be essential to show this.
6. How do the ribosomes in the arrays differ from the free-floating ones? Are the latter not associated with the membrane, while the former are not? Can differences be visualised through 3D classification?
7. The difference in the PTP coat in empty vs. filled PTs are very interesting. Can the authors clarify how this was measured and mention the number of measurements, mean, and standard deviation in the main text? Line plots would help substantiate the measurements.
8. Do the authors observe any differences in the regularity of the array? This could be assessed by investigating power spectra of tomograms of STAs.
9. How do the authors suggest such large changes in thickness come about? Is the PT coat "bunched up", as the PT compresses and stretched out, as the PT extends?
10. How often are each of the described PT stages seen as a percentage of all data? Are some observed more often than others or is the distribution equal?
11. Line 125. How do the authors know that they observe nuclei? Can they identify nuclear envelopes? Are nuclear pores evident?
12. Line 168 - 169: How many measurements were taken from each state? What was the mean and SD for membranes and coats? This will be interesting, especially, as the thickness of the PT coat can vary along the length of one PT.

Minor:

1. Line 102 "optimal conditions" sounds obscure, please briefly mention what these are.
2. Line 119. Are membrane-less PTs ever seen?
3. Line 156, the word "remodelling" may be too specific, considering that only differences in thickness were measured.
4. Line157: "Visualising PT sections ...." Sections sounds like physical cryosections were investigated. Perhaps better: "Inspecting tomograms of PT segments in different states..."
5. Line 161: "subtomogram averaging particles picked on the tube wall from both states" better: "subtomogram averaging of the tube wall from both states"
6. Line 162: delete "it be"
7. Line 201: Is organ the right word here?
8. Fig 2: Increase transparency to reveal the atomic model in C more clearly.
9. Fig 2b. I suspect the beige ribosomes are ones that do not follow the array? If so, can you please clearly state it? Also, are these dimers too? And can you tell if they are different?
10. Fig. 3e: The diagonal lines in the schematic infer that the data provide some level of insight into the PT lattice structure. As this is not the case, it would be better to remove these lines.
11. A flow chart highlighting the sub-tomogram averaging workflows employed should be included.

Significance

This paper advances our knowledge of the microsporidian polar tube with regard to its structure, dynamics, and transported content. Ribosome arrays have not been described before in extended PTs, so this is an interesting discovery, which adds to the complexity of ribosome regulation in microsporidia.

Strengths are the novelty of the findings, in particular the ribosome arrays, PT dynamics, and PT composition.

As a weakness, I feel that the tomography data could have been analysed in more depth. For example, at least a low-resolution map of the ribosome dimer would be important to show that the ribosomes in the arrays are indeed dimers. In addition, 3D classification would be useful to understand, if all ribosomes occur as dimers or only a fraction.

The paper is clearly written and well presented and thus suitable for a wider audience, including researchers studying microsporidia, infection biology, host-pathogen interactions, and ribosome biology.

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Referee #2

Evidence, reproducibility and clarity

In this paper Sharma et al. use cryo-electron tomography to study structural properties of the polar tube invasion apparatus from the microsporidian parasite Vairimorpha necatrix. The main conclusions of the paper are related to the unique organization of ribosomes in the polar tube, and the organization of the surface layer of the tube. The cryo-ET data presented in this paper are of high quality, and add new insights into the structure of the polar tube, which have not been reported previously. The authors also purify an endogenous polar tube protein, PTP3, via a native cluster of histidines, and identify co-purifying proteins, which provides new insights into the proteins present in the polar tube that may interact directly or indirectly with PTP3. The endogenous purification was innovative and well carried out, a very nice result.

Major comments:

1. Our biggest comment on this manuscript is that we feel the cryo-ET data are often over-interpreted. We would like to request the authors to ensure that their conclusions are justified by the data. We realize that this is a general weakness of cryo-ET at the moment, and that often features that are observed may not be able to be unambiguously defined. The interpretation of the data does need to reflect this. Below are several of the main examples we found, but we urge the authors to keep this in mind as they revise the whole manuscript.
   • a) Assignment of densities: Ribosomes and lipid bilayer are reasonable to assign, because STA in Fig. S3 supports this. Fig. 1 and through the text, eg. lines 120, 126 - proteasomes, PTPs, assigning the outer layer to PTPs, is not justified based on the data. For these, it would be reasonable to speculate in the discussion, it is a reasonable hypothesis, but currently there are no data that directly support this assignment/interpretation. Statements such as in Line 184 "large-scale remodeling of the PTP layer" - are misleading, and do need to be worded with the appropriate level of certainty, currently it is only a hypothesis that this layer is, in fact, composed of PTPs.
   • b) Definition and classification of Cargo: The authors observe polar tubes with different cargos in them. From the cryo-ET data itself, it is not clear what the cargo is. Based on the timescale of the event, it is unlikely that one would catch a substantial number of tubes in the process of transporting cargo. The data are still valuable, but the authors should take care in how the cargo are interpreted, and what the relationship may be to transport of sporoplasm through the tube.
   • c) Time component in interpretation: The authors discuss data as a function of time, for example one section is entitled, "Remodeling of the polar tube protein layer during cargo transport". These data are simply 45 random snapshots of polar tubes, so currently there is no time component in these data. Such a section could be valuable to add to a discussion section, but since it is quite speculative, it would be misleading to a reader for these to be presented as results. Along these lines, Line 118 correlates a "germination phase" with tube thickness. As these experiments have no time component, there is no basis for this correlation. These data can of course be used to generate a hypothesis, which would be appropriate for the discussion section, or clearly indicated that it is speculative (not a direct conclusion from the data presented)
   • d) Line 156-158 - is an overinterpretation of the data, because in our understanding it is currently not known what is in the tubes, and what state they are in. Please re-word.
2. One of the main conclusions of the paper is the arrangement of ribosomes in the PT. Yet, these are only observed in 5/45 tomograms. What is the authors' interpretation of this observation? Are they just stuck in the tube in some cases?
3. We request the authors to please provide sufficient information in their methods for reproducibility of their experiments, specifically in these sections:
   • a) In the germination section please provide information on reproducibility of the spore preparation, and information on germination rates. Line 104: "with spores consistently displaying high germination efficiencies" - please clarify what "high" means.
   • b) Light microscopy: please specify rates of incomplete and complete germination, how this was evaluated, how many events were analyzed, and any differences between complete (sporoplasm visible) or incomplete (sporoplasm not visible) germination.
   • c) Line 325: please provide detailed information on CNN-based picking and segmentation, for example, parameters used for optimization
   • d) Line 330: please specify number of tomograms
   • e) Line 331: please specify how manual alignment and particle centering was achieved
   • f) Line 332: please provide information on template-matching options / thresholds used
4. Supporting Fig 2c: we found it confusing to understand how Pempty is defined, it does not look empty in some cases, and the 3 shown look very different. On what basis is the tube labeled "empty"? The definition provided in line 131 does not seem to match the figures.

Minor comments:

Fig. 1: The lipid bi-layer in parts a to e seems different, and we found this confusing. Is the pink label in A not pointing to the correct layer? The corresponding segmentation is also confusing - does the lipid bilayer not go all the way around the tube? This would be important to clarify, since a lipid bilayer is one of the major components of the tube.

The following publications have shown cryo-ET of the polar tube, and should be referenced appropriately in the introduction, as well as during interpretation: 1) BioRxiv, https://doi.org/10.1101/2023.05.01.538940 Figure 1 and 2) PMID: 31332877. The second is referenced but should be mentioned around line 70 in the introduction

In the introduction, it would be helpful if the authors mention something about their microsporidia species of interest, and reason for choosing to study this species.

Fig. S1C - please show individual data points

Line 100 - the data presented do not show deformation of the cargo, so please reword to reflect the data being discussed

Line 140: could the authors please outline how they confirmed that the handedness of the reconstructed tomogram is correct?

Line 250: re-word to ensure that appropriate credit is given to previous work in the field; the large-scale rearrangement of the polar tube has been observed for many decades

Line 352: out of curiosity, why could resolution not be determined for PTcargo?

Fig S2a: diagram of the polar tube within the spore shows the polar tube with opposite handedness to what has been previously determined

Supporting table 1 - is missing frames per movie and which mode data were collected in

Fig 2b: We did not follow the rationale for the 3 colors of ribosomes

Sup Fig 3a: please specify in legend and/or workflow software packages used in panel (a)

Fig 2e: it is unclear whether averages presented are from 1 tomogram, or all tomograms where that pattern is visible - Is the measurement coming from all 5 tomograms?

Fig 3 c-e: it is unclear how many tomograms were used for these averages. Was 1 STA per tomogram performed, or 1 STA per type of PT?

Significance

Overall, this paper provides interesting new insights into knowledge of the microsporidian polar tube. We thank the authors for making this paper available to the community on BioRixiv, and we summarize a few main comments below, which we hope will be helpful in preparing a revised version of the manuscript. There is a substantial advance in applying cryo-ET to studying the polar tube of microsporidian parasites. The audience this will be interesting to are those studying microsporidian parasites.

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Referee #1

Evidence, reproducibility and clarity

Summary: Sharma, et al. report the characterization of the polar tube (PT) from the microsporidian species, Vairimorpha necatrix, using a combination of optical microscopy, cryo-ET, and proteomics. The polar tube is a fascinating invasion apparatus which mediates the translocation of the parasite into the inside of a host cell to initiate infection. Similar to results obtained previously in other species, the authors show that PT firing in Vairimorpha necatrix is extremely fast, occurring on the order of 1 sec, and that the extruded PT is over 100 microns long in this species. Using cryo-ET to image the PT at a high resolution, they find that it exists in two major states: both an empty state and a state filled with cargo, and that the thickness of the tube wall changes when cargo is present. Strikingly, the authors observed that one of the cargo components, the ribosomes, are organized ordered array that may have helical symmetry. Finally, the authors took advantage of a naturally occurring "His tag" on PTP3 to affinity purify PTP3-containing protein complexes and analyze the composition using proteomics.

Major comments

ln 139-140: The absolute handedness of something can be very tricky to determine by cryo-ET (but certainly is possible). Variable hardware configurations between microscopes and differing conventions between software packages (e.g., for what direction is a positive tilt angle) can lead to inversion of the apparent handedness in the final tomogram. How certain are the authors that the absolute handedness is indeed right handed, as this seems to vary between the various display items in the manuscript? For example, in Fig 1c, my impression is that ribosome helices are left handed, as they are also in the supplemental movie. If this isn't known with certainty, perhaps it would be sufficient to describe the apparent helical symmetry but state that the handedness is ambiguous.

Minor comments

ln 39-40: Perhaps also cite the E. cuniculi genome paper?

ln 97-98: It is interesting that the PT shortens in V. necatrix as well, and while I can pick this out in some of the individual traces in Sup Fig. 1b, it seems to get washed out in the trend line and isn't super obvious. If it isn't to laborious, it could be nice to add a panel showing the quantification of this (e.g., plotting the final length of each PT as a percentage of the maximum length achieved).

ln 98-100: Strictly speaking, I don't think the referenced figure shows the sporoplasm being transformed into an extended conformation, only that it is spherical upon exit. Simply reword this to make clear that the deformations are inferred to occur but not directly observed.

Because PT firing is so fast, the probability of trapping a PT in the process of transporting cargo would be pretty low. So then why does the PT still contain cellular cargo like ribosomes inside in the tomograms? Should these not have emerged in the sporoplasm which would enter the host cell? Are these "defective" spores that have failed to complete sporoplasm transport? Perhaps this is worth discussing.

ln 118: The authors note an apparent correlation between the phase of germination and the thickness of the tube wall but don't specify what this correlation is. Is it thicker in the early phase and thinner in later phase, or vice versa? One could imagine "empty" tubes existing before or after sporoplasm transport, for example, so I'm not sure I follow how the phase is being inferred from the tomograms.

ln 119-120: What is the evidence that the outer layer is made of PTPs, or that it is even protein (for example, as opposed to cell wall-like carbohydrate polymers)? I think this seems like a very reasonable hypothesis, but I would suggest explaining the logic and ensuring the degree of uncertainty is conveyed clearly. In light of this, I would also suggest changing figure labels, etc, that refer to the PTP layer (e.g., Fig. 3, PTPc and PTPe labels).

ln 121, 123: "sheathed by a thin layer" and "enveloped by a thick outer layer": is this an additional layer being described? Or is this referring to the putative PTP layer, and that its thickness is variable?

ln 125-126: While I understand how some features, like ribosomes, proteasomes, and generic membrane compartments could be identified, it is unclear to me how one would recognize the nucleus when inside the PT, nor are any examples shown. If the data is clear, perhaps the authors could show it in a figure? Otherwise, I suggest removing the claim regarding the nucleus.

The arrangement of the ribosomes in a subset of tubes is really fascinating! While the number of observations is relatively small (n=5), it seems like it should be possible to comment preliminarily on whether there is much variability in their helical arrangement. Do the helical parameters vary much between observations? Does the til, pitch, etc vary much, are the 5 occurrences very similar? Is there any sign that they are associated with a membrane? Also, since the ribosomes form a lattice-like arrangement, it seems like it would be possible to trace ribosome helices in both the left and right handed directions. How did the authors decide between the two possibilities? This doesn't seem to be discussed.

Fig. 2e: Are the two different colors/orientations meant to represent the two protamers of the ribosome dimer? When refined subvolumes are mapped back onto the original tomogram do the authors observe a similar crystalline arrangement of particles as in their segmentation? Are the orientations of the ribosomes correlated, and do the provide any evidence for the dimeric arrangement mentioned? The PlaceObjects plugin for Chimera can be very helpful for visualizing this: https://www.biochem.mpg.de/7939908/Place-Object

Supp figure 4(b-d): Perhaps these models could be colored by pLDDT scores (with a key indicating the color scheme), so the reader can assess the quality of the predictions?

How were the measurements of the membrane thickness and putative PTP layer carried out? On the tomogram projections? STAs? How were the boundaries of the layers established (e.g., map threshholding if STA?)? This information appears to be missing from the methods.

Some tubes that are labeled as 'PTempty' actually contain cargo and look dense (example supp. Fig 2c, left and middle panels). Is it fair to classify these as empty tubes?

Fig. 3d: I am not entirely clear on what is being shown here. Are independent reconstructions of PTcargo and PTempty superposed (aligned on membrane)? The description in the figure legend doesn't clearly say what is being displayed. I think it might be more clear to show these side-by-side instead of superposed (i.e., 4 panels instead of 2).

Sup Fig 1: Define S and SP in legend or just spell out on figure? Missing x-axis label on panel b.

Fig. 4b and Sup Fig 2a: The depictions of the PT in the spore here are left-handed. In a few species, the coil of the PT was found to form a right-handed helix (Jaroenlak, et al.), and it seems plausible that this may be a general feature that would be conserved across microsporidia. I appreciate that it might not be actually known to be right-handed in V. necatrix, but if there is no strong data either way, perhaps it would make sense for these depictions of the PT to be right-handed.

I think all three of us are more or less in consensus about this manuscript, and I largely agree with the other reviewers comments. I think after addressing reviewer suggestions, this will be a pretty nice story.

Significance

Overall, this manuscript from Sharma, et al. presents interesting new findings about the structure and cargo transport function of the microsporidian PT. Microsporidia infect a wide range of hosts, including humans, and how the PT mediates parasite entry into cells is poorly understood. The approaches used in this study are appropriate for tackling the questions at hand, and appear to be generally well executed and interpreted. The observation that ribosomes assemble into an array within the PT is very unexpected and quite fascinating, and may be of broader interest to researchers working on ribosome structure and function, in addition to researchers studying microsporidia. The approach to investigating proteins interacting with PTP3 was quite elegant, and yielded a list of potential interactors that appears to be of very high quality and is highly plausible based on the literature field. We think this work is a substantial advance in the field and provides important new insights into the organization of the PT. - Please define your field of expertise with a few keywords to help the authors contextualize your point of view:

Structural biology, microsporidia - Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

We are not experts in proteomics/mass spectrometry

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Reply to the reviewers

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

The authors describe a broad-scale phylogenetic survey of chemokine-related ligand and receptors from representative vertebrates, invertebrates, and viruses. They collect ligand and receptor sequences from available genome sequences, and use phylogenetic and CLANS analysis to group these into similar gene types. They then overlay these onto a validated species phylogeny in order to evaluate relationships of orthology and paralogy to pinpoint gene duplication and loss events. They carry out these analyses for canonical chemokine ligands receptors and for other closely related protein families. They conclude that the canonical chemokine system is restricted to vertebrates but that closely related ligands and receptors can be found in invertebrate chordates. More divergent but related gene systems are found in more distant invertebrates. They define more limited expansions of some ligand-receptor systems in certain jawed vertebrate groups and specifically in mammals.

Overall, the paper addresses a complex and important system of signaling proteins with a rigorous and comprehensive set of analyses. The finding will be of interest to a diverse group of scientists. My comments listed below mainly consist of suggestions to help clarify the presentation.

1. Pg 2, Lns 21-24: The canonical and non-canonical chemokine subclasses are introduced in the abstract without definition. A very brief explanation would be useful.

We've included a brief description of "non-canonical" components in the abstract (lines 21-24). These non-canonical components fall into at least one of three categories: 1) molecules with sequence similarities to canonical components, 2) those that bind to a canonical component (either ligand or receptor), 3) those involved in chemokine-like functions, such as chemoattraction. More comprehensive explanations and examples of these non-canonical components are provided in the Introduction section.

1. Some general contexts of chemokine functions are listed, including inflammation and homeostasis. A little more detail of how these signals are used and the molecular consequences of signaling may be useful in the introduction to set the biological context of the analysis (e.g., how do the signals regulate homeostasis?).

We have added at the beginning of the introduction (lines 39 – 46) some details of how chemokine signalling typically occurs at a mechanistic level. We also provided few examples of homeostatic functions regulated by chemokine signalling and clarified different expression strategies for inflammatory versus homeostatic chemokines.

It may help to summarize the known chemokine and chemokine-related gene systems in some type of table at the beginning of the results. This could serve as a convenient reference to guide the reader through the more detailed results. The manuscript addresses a complex set of ligands and receptors with names that may be confusing to the non-expert.

We agree with the reviewer on this and moved Table S1 to the main text (now Table 1). This table contains all the information on ligands, receptors, and relative citations (lines 741-744).

Pg 5, Ln 98: Fig 1C is introduced before Fig 1B. Can the panels be switched or the descriptions be rearranged?

We have switched the panels in Figure 1. Now, Figure 1A and 1B refer to CLANS analyses and Figure 1C and 1D refer to phylogenetic trees of ligand groups. We have corrected all the references in the main text and in Figure 1 caption. Now the panels are mentioned in the correct alphabetical order within the text.

Cytokine and chemokine ligands are small proteins that diverge quickly in different species and are difficult to identify in divergent genomes even within vertebrates. Conclusions about the absence of these types of factors are notorious for being disproven in subsequent analyses. Some discussion of what may have been missed in the survey for homologs (or reasons to think that ligands were not missed) would be useful in the Discussion.

We concur with the reviewer's observation, and we used three distinct strategies to address the issue:

1. E-value Threshold Adjustment: Initially, we utilized a relatively low e-value threshold of These three strategies collectively contribute to a more robust and comprehensive approach to address the challenges associated with the bioinformatic identification of canonical and non-canonical chemokines. We briefly mentioned the technical difficulty of working with short sequences in our Introduction (lines 75-76).

Reviewer #1 (Significance (Required)):

This paper presents a thorough analysis of chemokines and related gene systems across a wide phylogenetic landscape. The authors have expertise in these gene families and in the techniques that they use to identify and relate family members. The chemokines are an important set of signals that are used across several biological systems. These findings will be of wide interest to immunologists, neurobiologists, developmental and evolutionary biologists.

We thank reviewer 1 for their comments – they have been very valuable to improve our manuscript.

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

This paper applies phylogenetic clustering methods to a large taxonomical sampling to interrogate the relationship between canonical and non-canonical chemokine ligands and receptors. The results suggest that 1) unrelated proteins evolved "chemokine-like" ligand function multiple times independently; and 2) all the canonical and non-canonical chemokine receptors (except ACKR1) originated from a single duplication in the vertebrate stem group, which also gave rise to many GPCRs. In addition, the authors characterized the complement of canonical and non-canonical components in the common ancestor of vertebrates and identified several other ligands and receptors with potential chemokine related properties.

Comments: 1. There are many places in the paper, too many to list, where the authors refer to chemokine receptors but call them 'chemokines'.

We have corrected this oversight throughout the manuscript.

In Figure 1, CX3CL is referred to as 'X3CL'

We have corrected this. Now CX3CL is referred to correctly in Figure 1. We also found that it was incorrectly spelt in Figure 2 as well and corrected it there too.

1. CXCL17 was originally reported to be chemokine-like based on sequence threading methods. The authors refer to a 2015 paper indicating that it has chemokine-like activity at GPR35, which had been renamed provisionally CXCR8. To my knowledge that result was not based on direct binding data but inferred from a functional response. Moreover, to my knowledge it has not been independently confirmed. Instead there is a recent paper in JI from the Pease lab showing extensive experimental results that fail to demonstrate CXCL17 activity at GPR35. This uncertainty regarding a potential mistake in the literature should be addressed and integrated in the points made about CXCL17 being an outlier.

We thank the reviewer for pointing this out. To account for this suggestion, we have modified the text as follows:

Lines 105-108: “The distinction between CXCL17 and all other canonical chemokines is consistent with our receptor results showing that the potential receptor for CXCL17, GPR35 (41), is also not within the canonical chemokine receptor group (see below). Although it is important to note that recent studies fail to demonstrate CXCL17 activity at GPR35 (42, 43).”

Lines 240-241: “Another orphan GPCR, GPR35, had been proposed as a potential chemokine receptor (41); however, this was later questioned (42, 43) and GPR35 is still generally considered orphan (55–57).”

Lines 312-315: “CXCL17 is mammal-specific and likely unrelated to canonical chemokines (similar to its controversial putative receptor, GPR35 (41-43), that is not a canonical chemokine receptor).”

References: [41] J. L. Maravillas-Montero, et al., Cutting Edge: GPR35/CXCR8 Is the Receptor of the Mucosal Chemokine CXCL17. The Journal of Immunology 194, 29–33 (2015).

[42] S.-J. Park, S.-J. Lee, S.-Y. Nam, D.-S. Im, GPR35 mediates lodoxamide-induced migration inhibitory response but not CXCL17-induced migration stimulatory response in THP-1 cells; is GPR35 a receptor for CXCL17? British Journal of Pharmacology 175, 154–161 (2018).

[43] N. A. S. B. M. Amir, et al., Evidence for the Existence of a CXCL17 Receptor Distinct from GPR35. The Journal of Immunology 201, 714–724 (2018).

[55] S. Xiao, W. Xie, L. Zhou, Mucosal chemokine CXCL17: What is known and not known. Scandinavian Journal of Immunology 93, e12965 (2021).

[56] S. P. Giblin, J. E. Pease, What defines a chemokine? – The curious case of CXCL17. Cytokine 168, 156224 (2023).

[57] J. Duan, et al., Insights into divalent cation regulation and G13-coupling of orphan receptor GPR35. Cell Discov 8, 1–12 (2022).

Can the authors use alpha fold to address whether any of these non-canonical molecules actually is predicted to fold like a chemokine? More generally, based on the paper's analysis, how do the authors propose to define a chemokine? It is well-accepted that chemokines are defined by structure, not function (e.g. limited truncation of any chemokine abrogates activity, but it is still a chemokine structurally, not semantically, folds like a chemokine, aligns with other chemokines).

In response to the recommendation from reviewer 2 to incorporate AlphaFold data, we leveraged AFDB Clusters (foldseek.com), a recently developed tool that clustered over 200 million Uniprot proteins based on their predicted AlphaFold structures (as described in this Nature paper: https://www.nature.com/articles/s41586-023-06510-w). We utilised this pre-computed dataset of clustered proteins to query with representative human proteins, both canonical and non-canonical chemokine ligands, and the results are summarised in the table below. Notably, we observed that canonical chemokines were distributed across different AlphaFold clusters, each corresponding to different ligand types (e.g., CC and CXC). Interestingly, despite this, all these clusters exhibited similar descriptions (e.g. CC or CXC), indicating that the method effectively recovers well-characterized chemokines. Conversely, when analysing non-canonical chemokine ligands, none of them were classified within the canonical chemokine clusters. This observation strongly suggests that canonical and non-canonical ligands do not share the same protein fold. Additionally, we identified intriguing correlations between these structure-based clusters and the results from our phylogenetic analyses. For instance, CXCL14 was clustered within a CC-type group, consistent with our reconciled tree positioning it within the broader CC-type clade (as shown in Figure 2A). Similarly, CXCL16 formed its own unique cluster, which aligns with our CLANS analysis, where it is the last group to connect with canonical chemokines (illustrated in Figure 1A and Figure S1). Furthermore, TAFA5 was found in a distinct cluster, mirroring our phylogenetic analyses that place it as the most basal TAFA clade (as depicted in Figure 2A and Figure S19). While these findings are intriguing, we acknowledge that additional in-depth analyses, beyond the scope of this paper, will be necessary to confirm these results.

In response to the reviewer's inquiry regarding how to define a chemokine, it is essential to recognise that many proteins can exhibit similar 3D structures without being considered homologous. A notable example is the opsins, which are present in both bacteria and animals. Despite sharing a common 3D structure that is characterised by seven transmembrane domains (TMDs) and serves similar functions, they are not regarded as homologous, as highlighted in this study (https://doi.org/10.1186/gb-2005-6-3-213). Considering these findings, we propose that, like various other gene families, the primary criterion for assessing protein homology should be rooted in shared evolutionary ancestry and common origin, and this should take precedence over structural similarities.

Human gene

Uniprot Accession

AFDB Cluster

Accession

Description

Canonical CKs

CXCL14

O95715

A0A3Q3M453

C-C motif chemokine

CCL24

O00175

A0A4X1T574

C-C motif chemokine

CX3CL1

P78423

A0A7J8CF84

C-X3-C motif chemokine ligand 1

CXCL1

P09341

A0A1S2ZIJ4

C-X-C motif chemokine

CXCL13

O43927

A0A1S2ZIJ4

C-X-C motif chemokine

CXCL8

P10145

A0A1S2ZIJ4

C-X-C motif chemokine

CCL20

P78556

A0A6P7X7F3

C-X-C motif chemokine

XCL1

P47992

A0A6P7X7F3

C-X-C motif chemokine

CXCL16

Q9H2A7

A0A6P8SIS6

C-X-C motif chemokine 16

CCL27

Q9Y4X3

A0A1L8GBB9

SCY domain-containing protein

CCL1

P22362

A0A3B4A358

SCY domain-containing protein

CCL5

P13501

A0A3B4A358

SCY domain-containing protein

CCL28

Q9NRJ3

A0A3Q0SB19

SCY domain-containing protein

CXCL12

P48061

A0A401SMI2

SCY domain-containing protein

CXCL17

CXCL17

Q6UXB2

No cluster found

No cluster found

TAFA

TAFA1

Q7Z5A9

Q96LR4

Chemokine-like protein TAFA-4

TAFA2

Q8N3H0

Q96LR4

Chemokine-like protein TAFA-4

TAFA3

Q7Z5A8

Q96LR4

Chemokine-like protein TAFA-4

TAFA4

Q96LR4

Q96LR4

Chemokine-like protein TAFA-4

TAFA5

Q7Z5A7

A0A7M4EYY1

TAFA chemokine like family member 5

CYTL

CYTL1

Q9NRR1

A0A673GVE4

Cytokine-like protein 1

CKLFSF

CMTM5

Q96DZ9

A0A4W2H069

CKLF like MARVEL transmembrane domain containing 5

CMTM8

Q8IZV2

U3IR50

CKLF like MARVEL transmembrane domain containing 7

CMTM7

Q96FZ5

A0A6G1PQK5

CKLF-like MARVEL transmembrane domain-containing protein 7

CMTM6

Q9NX76

A0A814ULI9

Hypothetical protein

CKLF

Q9UBR5

A0A3M0K8M7

MARVEL domain-containing protein

CMTM1

Q8IZ96

A0A3M0K8M7

MARVEL domain-containing protein

MAL

P21145

A0A402F5Z5

MARVEL domain-containing protein

CMTM2

Q8TAZ6

A0A6G1S7Y0

MARVEL domain-containing protein

PLP2

Q04941

A0A667IJ27

Proteolipid protein 2

CMTM3

Q96MX0

A0A3B1ILJ1

Zgc:136605

CMTM4

Q8IZR5

A0A3B1ILJ1

Zgc:136605

PLLP

Q9Y342

A0A3B1ILJ1

Zgc:136605

Chemokine genes are found on many human chromosomes with large clusters on chromosome 2 and 17. Can the authors address the syntenic relationships phylogenetically?

There are cases where synteny data have been used to infer the relationship between species (e.g. https://doi.org/10.1038/s41586-023-05936-6); however, to our knowledge, they cannot be used to infer the pattern of gene duplications and losses, as we have done here with gene tree to species tree reconciliations. However, the two approaches are extremely powerful combined and compared as they provide independent evidence. For example, with our phylogenetic analysis of chemokine ligands, we found that CXCL1-10 plus CXCL13 form a monophyletic clade (Figure 2A); this is consistent with their location on the human chromosome 4 (Zlotnik and Yoshie 2012). Similarly, most of the CC-type chemokines, that we find monophyletic in our trees, are located in a locus in human chromosome 17. Likewise, chemokine receptor phylogenetic relationships are largely consistent with macro and micro syntenic patterns. Most of the chemokine receptors are on human chromosome 3 (Zlotnik and Yoshie 2012) and they all belong to a large monophyletic clade in our tree (Figure 4A). Smaller clusters also maintain correspondence, such as the mini cluster of CXCR1 and CXCR2 on human chromosome 2 corresponding to a monophyletic clade in our phylogenetic analysis (Figure 4A).

We have incorporated the above considerations in our manuscript at the lines:

• Lines 140-148 (ligands)

• Lines 256-272 (receptors)

• Lines 375 – 483 (discussion)

The authors indicate that 'CXCL8 is present in all jawed vertebrates except in the cartilaginous fishes lineage'. However, they should point out that CXCL8 is not represented in mice. The notion that the repertoire of chemokine and chemokine receptor genes can be different in even closely related species as well as in individuals of the same species is well-documented but not mentioned here.

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We thank the reviewer for these suggestions, and we have modified the text in lines 137-138.

The analysis suggests that chemokine gene repertoires start small and grow non-linearly to 45 in mammals. However DeVries et al (JI 2005) published that zebrafish have the most chemokines, 63, and chemokine receptors, 24. Do the authors disagree? This should be addressed.

The significant increase in the number of ligands and receptors in zebrafish, compared to their last common mammalian ancestor, can be attributed to an additional round of whole-genome duplication (WGD) (https://doi.org/10.1016/S0955-0674(99)00039-3).

Concerning ligands, the count in zebrafish varies from 63 in DeVries et al. 2005 to 111 in Nomiyama et al. 2008, and to 35 in our study. This variation can be attributed to several factors:

1. Genome Versions: The disparities may arise from the use of different versions of the zebrafish genome. We utilised an improved version known for its higher contiguity and reduced fragmentation (https://www.nature.com/articles/nature12111). It is possible that the additional ligands identified by DeVries, Nomiyama, and others were partial sequences.
2. Methodology: Methodological differences are at play. DeVries et al. employed tblastN, while we opted for BLASTP. Nomiyama et al. do not specify the type of BLAST performed.
3. Stringency: We collected our sequences based on a BLASTP search using as query sequences only manually curated sequences from UniProt. This additional precaution allowed us to identify sequences with high-confidence chemokine ligand characteristics.
4. Sequence Characteristics: Ligands typically have shorter sequences and exhibit less sequence conservation compared to receptors. Zebrafish represents a case in which working with short sequences may lead to missed homologs.
5. Species-Specific Nature: Our approach successfully recovered the complete set of ligands in other species, such as humans and mice. Zebrafish appears to be an exception rather than the norm. When it comes to receptors, which typically have longer sequences, making it easy to identify distant homologs, our results closely mirror those of DeVries in 2005. In our study, we identified 28 canonical receptors, compared to their count of 24. However, it is worth highlighting that within our dataset, four of these receptors appear as species-specific duplications, potentially indicating that they are actually isoforms or related variants.

Nonetheless, it is essential to emphasise that our work does not aim to precisely reconstruct the entire complement of ligands and receptors in zebrafish or other species. Achieving this would require further validation, including the expression analysis of potential transcripts.

Did the authors find any species in which a chemokine/chemokine receptor pair are not found together? That is, if the system is irreducibly complex, requiring both a ligand and receptor, the probability of both genes arising simultaneously is essentially zero. So how do the authors theorize that such a system actually arose, and is there any evidence in their data set for convergence of separately evolved ligand and receptor?

Our data strongly support the hypothesis that the canonical chemokine system originated within the stem group of vertebrates, likely as a consequence of two rounds of genome duplication. This likely accounts for the simultaneous emergence of both ligands and receptors. While the receptors (both canonical and non) can be traced back to a single-gene duplication event (with the exception of ACKR1), the evolution of ligand families capable of interacting with chemokine receptors occurred independently, although further experiments are required to validate this in vivo in a broader set of organisms. In our study, we successfully identified the complete set of receptors and ligands in well-established model systems like humans and mice. However, when it comes to interactions between ligands and receptors outside these model organisms, the picture becomes less clear. Similarly, the exact pairings of non-canonical components are also not fully clarified (see lines 404-406). As a result, speculating about evolutionary conservation in these contexts requires caution and further investigation. It's worth noting that chemokines and their corresponding chemokine receptors do not necessarily evolve in tandem. Since they are encoded by different genes, they evolved from separate duplication events occurring at different points in evolutionary history. In certain instances, due to the system's flexibility, chemokines binding orthologous receptors may not be orthologous themselves but may have independently acquired the ability to activate the same receptor in various species.

Line 180, 181 and elsewhere: GPCR1 and GPCR33 should be GPR1 and GPR33

We have corrected this throughout the manuscript.

Line 185: ACKR1 exceptionalism is noted, but there is no discussion of the remarkable structure-function paradox that the most distantly related chemokine receptor is also the most highly promiscuous receptor, binding many but not all CC and CXC chemokines with high affinity.

We added in the discussion section this consideration regarding the wide binding of ACKR1 (Lines 341-343) and its ability to bind both CC and CXC chemokines (DOI: 10.1126/science.7689250 and 10.3389/fimmu.2015.00279), highlighting the intriguing contrast with the fact that it is the most distantly related receptor.

Line 196: the viral receptors cluster with the vertebrate receptors, suggesting that the viruses captured the receptor gene from the host. Authors might mention this obvious point regarding origins, and discuss how it relates to the monophyly and paraphyly that emerges from the phylogenetic analysis.

We added a comment to the discussion section (Lines 348-352) regarding the potential origins of the viral chemokine receptors.

Any discussion of chemokine-like convergent evolution presupposes that the activity is real and actually occurs in vivo. The authors should make clear to what extent the existing literature supports this. As mentioned above, CXCL17 interaction with GPR35 has been challenged in vitro and has never been demonstrated to occur in vivo. To what extent is the same limitation a problem in considering co-evolution of the other non-canonical chemokines? I agree that classification based solely on function is inappropriate, but so is phylogenetic analysis without direct knowledge of in vivo function. It is no feasible to address this in a phylogenetic analysis, but there ought to be at least one species in which the non-canonicals have been rigorously shown to act at specific receptors in vivo before grouping them with the canonicals in a co-evolutionary sense.

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We agree with the referee that evidence of real chemokine-like activity is important to consider the activity in vivo.

In our work, the molecules examined were chosen based on previous evidence of chemokine-like sequence similarity, ability to bind canonical components and/or chemokine-like function. For example, CKLF (also called CKLF1) has been shown, through calcium mobilisation and chemotaxis assays using the human cell line HEK293, to bind CCR4 and to induce cell migration via CCR4 respectively (https://doi.org/10.1016/j.lfs.2005.05.070). Numerous papers are studying the in vitro and in vivo effects of CKLF in murein and human models (https://doi.org/10.1016/j.cyto.2017.12.002), therefore, we found it compelling to investigate its evolutionary relationship with canonical chemokines. Similarly, CYTL1, that had been predicted to possess an IL8-like fold (https://doi.org/10.1002/prot.22963), has been found to bind CCR2 (https://doi.org/10.4049/jimmunol.1501908) and in vitro and in vivo studies showed chemotactic activity for neutrophils (https://doi.org/10.1007/s10753-019-01116-9). Ongoing research into this molecule are focusing on a wide array of immune functions (https://doi.org/10.1007/s00018-019-03137-x).

We mentioned these considerations in our introduction to explain why we were interested in investigating these molecules (lines 50-57). We have also added a line in the Discussion (lines 323-324) where we reinforce the idea that in vitro and in vivo experiments for all chemokine-like molecules are required to validate computation predictions.

The discussion of homeostatic vs inflammatory chemokine/receptors in the last section of the Discussion would be enhanced by pointing out that the chemokine specificities are numerically totally different for these two groupings, homeostatics tending to have monogamous ligand-receptor relationships and inflammatories being highly promiscuous.

To account for the reviewer’s comment, we have added this consideration in a paragraph of the discussion (see Line 389-394).

Reviewer #2 (Significance (Required)):

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Much of the paper's results are confirmatory of previous work based on less extensive sequence analysis. One could say more generally that unrelated chemical forms, not just unrelated proteins, have chemokine-like ligand function. For example leukotriene B4 is a powerful leukocyte chemoattractant for neutrophils working through a GPCR. That proteins might also independently evolve common functions does not add insight beyond what is already appreciated. The notion that chemokine receptors have a common ancestor is also generally accepted and that ACKR1 is an outlier is already appreciated. The present work adds phylogenetic and statistical precision to these points.

Our discoveries clarify various aspects of the chemokine system's evolution, and we are confident that the "phylogenetic and statistical precision" of our findings will provide a solid cornerstone for future research aimed at unravelling the function and evolution of the system. Specifically, our work clarified:

1. The presence only in Vertebrates: We have confirmed, through a comprehensive taxonomic sampling (we use many more species than previous works), that the chemokine system is exclusive to vertebrates. However, intriguingly, we identified a TAFA chemokine-like family in urochordates.
2. Relationships between Ligands: We conducted a thorough examination of the relationships between canonical and non-canonical ligands and suggested that several unrelated molecules might have evolved independently their ability to interact with the chemokine receptors. We appreciate the comment of the reviewer regarding the fact that unrelated chemical forms such as leukotriene B4 may have chemokine-like functions. However, in our work all the non-canonical components examined are proteins and as such could have an evolutionary relationship with chemokines. Furthermore, we chose to consider only proteins that showed multiple lines of evidence implicating them in the chemokine system and that are currently the topic of interest in the field (see replies to reviewer 1’s comment #5 and to reviewer 2’s comment #12). Seeing the general interest in the topic, and especially seeing as this had never been clarified before, in this work, we set ourselves the goal to investigate the evolutionary relationship amongst these non-canonical ligands and canonical chemokines.
3. Duplication Events: We pinpoint the specific gene duplication events responsible for the emergence of chemokine receptors.
4. Atypical Receptor Paraphyly: Our work highlights the paraphyletic nature of atypical receptors, in contrast to previous research (see https://doi.org/10.1155/2018/9065181).
5. Viral Receptor Phylogenetics: To our knowledge, this is the first work to investigate the phylogenetic affinities of viral receptors.
6. GPCR182 and Atypical Receptor Affinities: We clarify the affinity of GPCR182 with atypical receptor 3, offering different insights compared to prior studies (see figure S3C in https://doi.org/10.1038/s41467-020-16664-0).
7. Additionally, our study represents the first analysis of the chemokine system in the basal vertebrate hagfish and provides insights into the ancestral form of the chemokine system.
8. Ultimately, our research identifies numerous molecules and receptors with potential chemokine functions. In conclusion, we contribute to resolving uncertainties surrounding the system's origin, including the complex duplication events that have shaped receptor evolution. As evident from the extensive comments provided by the reviewer, our work addresses various controversies in the field (e.g. the inclusion of CXCL17 as a chemokine). Nonetheless, like any new set of findings, our work amalgamates confirmatory results (as highlighted in point 1) with innovative discoveries (as outlined in points 2-8). However, the latter category significantly outweighs the former, underscoring the richness of novel insights.

Finally, we would like to thank reviewer 2 for their comments, as these have contributed to greatly improve our manuscript.

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Referee #2

Evidence, reproducibility and clarity

This paper applies phylogenetic clustering methods to a large taxonomical sampling to interrogate the relationship between canonical and non-canonical chemokine ligands and receptors. The results suggest that 1) unrelated proteins evolved "chemokine-like" ligand function multiple times independently; and 2) all the canonical and non-canonical chemokine receptors (except ACKR1) originated from a single duplication in the vertebrate stem group, which also gave rise to many GPCRs. In addition, the authors characterized the complement of canonical and non-canonical components in the common ancestor of vertebrates and identified several other ligands and receptors with potential chemokine related properties.

Comments:

1. There are many places in the paper, too many to list, where the authors refer to chemokine receptors but call them 'chemokines'.
2. In Figure 1, CX3CL is referred to as 'X3CL'
3. CXCL17 was originally reported to be chemokine-like based on sequence threading methods. The authors refer to a 2015 paper indicating that it has chemokine-like activity at GPR35, which had been renamed provisionally CXCR8. To my knowledge that result was not based on direct binding data but inferred from a functional response. Moreover, to my knowledge it has not been independently confirmed. Instead there is a recent paper in JI from the Pease lab showing extensive experimental results that fail to demonstrate CXCL17 activity at GPR35. This uncertainty regarding a potential mistake in the literature should be addressed and integrated in the points made about CXCL17 being an outlier.
4. Can the authors use alpha fold to address whether any of these non-canonical molecules actually is predicted to fold like a chemokine? More generally, based on the paper's analysis, how do the authors propose to define a chemokine? It is well-accepted that chemokines are defined by structure, not function (e.g. limited truncation of any chemokine abrogates activity, but it is still a chemokine structurally, not semantically, folds like a chemokine, aligns with other chemokines).
5. Chemokine genes are found on many human chromosomes with large clusters on chromosome 2 and 17. Can the authors address the syntenic relationships phylogenetically?
6. The authors indicate that 'CXCL8 is present in all jawed vertebrates except in the cartilaginous fishes lineage'. However, they should point out that CXCL8 is not represented in mice. The notion that the repertoire of chemokine and chemokine receptor genes can be different in even closely related species as well as in individuals of the same species is well-documented but not mentioned here.
7. The analysis suggests that chemokine gene repertoires start small and grow non-linearly to 45 in mammals. However DeVries et al (JI 2005) published that zebrafish have the most chemokines, 63, and chemokine receptors, 24. Do the authors disagree? This should be addressed.
8. Did the authors find any species in which a chemokine/chemokine receptor pair are not found together? That is, if the system is irreducibly complex, requiring both a ligand and receptor, the probability of both genes arising simultaneously is essentially zero. So how do the authors theorize that such a system actually arose, and is there any evidence in their data set for convergence of separately evolved ligand and receptor?
9. Line 180, 181 and elsewhere: GPCR1 and GPCR33 should be GPR1 and GPR33
10. Line 185: ACKR1 exceptionalism is noted, but there is no discussion of the remarkable structure-function paradox that the most distantly related chemokine receptor is also the most highly promiscuous receptor, binding many but not all CC and CXC chemokines with high affinity.
11. Line 196: the viral receptors cluster with the vertebrate receptors, suggesting that the viruses captured the receptor gene from the host. Authors might mention this obvious point regarding origins, and discuss how it relates to the monophyly and paraphyly that emerges from the phylogenetic analysis.
12. Any discussion of chemokine-like convergent evolution presupposes that the activity is real and actually occurs in vivo. The authors should make clear to what extent the existing literature supports this. As mentioned above, CXCL17 interaction with GPR35 has been challenged in vitro and has never been demonstrated to occur in vivo. To what extent is the same limitation a problem in considering co-evolution of the other non-canonical chemokines? I agree that classification based solely on function is inappropriate, but so is phylogenetic analysis without direct knowledge of in vivo function. It is no feasible to address this in a phylogenetic analysis, but there ought to be at least one species in which the non-canonicals have been rigorously shown to act at specific receptors in vivo before grouping them with the canonicals in a co-evolutionary sense.
13. The discussion of homeostatic vs inflammatory chemokine/receptors in the last section of the Discussion would be enhanced by pointing out that the chemokine specificities are numerically totally different for these two groupings, homeostatics tending to have monogamous ligand-receptor relationships and inflammatories being highly promiscuous.

Significance

Much of the paper's results are confirmatory of previous work based on less extensive sequence analysis. One could say more generally that unrelated chemical forms, not just unrelated proteins, have chemokine-like ligand function. For example leukotriene B4 is a powerful leukocyte chemoattractant for neutrophils working through a GPCR. That proteins might also independently evolve common functions does not add insight beyond what is already appreciated. The notion that chemokine receptors have a common ancestor is also generally accepted and that ACKR1 is an outlier is already appreciated. The present work adds phylogenetic and statistical precision to these points.

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Referee #1

Evidence, reproducibility and clarity

The authors describe a broad-scale phylogenetic survey of chemokine-related ligand and receptors from representative vertebrates, invertebrates, and viruses. They collect ligand and receptor sequences from available genome sequences, and use phylogenetic and CLANS analysis to group these into similar gene types. They then overlay these onto a validated species phylogeny in order to evaluate relationships of orthology and paralogy to pinpoint gene duplication and loss events. They carry out these analyses for canonical chemokine ligands receptors and for other closely related protein families. They conclude that the canonical chemokine system is restricted to vertebrates but that closely related ligands and receptors can be found in invertebrate chordates. More divergent but related gene systems are found in more distant invertebrates. They define more limited expansions of some ligand-receptor systems in certain jawed vertebrate groups and specifically in mammals.

Overall, the paper addresses a complex and important system of signaling proteins with a rigorous and comprehensive set of analyses. The finding will be of interest to a diverse group of scientists. My comments listed below mainly consist of suggestions to help clarify the presentation.

1. Pg 2, Lns 21-24: The canonical and non-canonical chemokine subclasses are introduced in the abstract without definition. A very brief explanation would be useful.
2. Some general contexts of chemokine functions are listed, including inflammation and homeostasis. A little more detail of how these signals are used and the molecular consequences of signaling may be useful in the introduction to set the biological context of the analysis (e.g., how do the signals regulate homeostasis?).
3. It may help to summarize the known chemokine and chemokine-related gene systems in some type of table at the beginning of the results. This could serve as a convenient reference to guide the reader through the more detailed results. The manuscript addresses a complex set of ligands and receptors with names that may be confusing to the non-expert.
4. Pg 5, Ln 98: Fig 1C is introduced before Fig 1B. Can the panels be switched or the descriptions be rearranged?
5. Cytokine and chemokine ligands are small proteins that diverge quickly in different species and are difficult to identify in divergent genomes even within vertebrates. Conclusions about the absence of these types of factors are notorious for being disproven in subsequent analyses. Some discussion of what may have been missed in the survey for homologs (or reasons to think that ligands were not missed) would be useful in the Discussion.

Significance

This paper presents a thorough analysis of chemokines and related gene systems across a wide phylogenetic landscape. The authors have expertise in these gene families and in the techniques that they use to identify and relate family members. The chemokines are an important set of signals that are used across several biological systems. These findings will be of wide interest to immunologists, neurobiologists, developmental and evolutionary biologists.

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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

There is mounting evidence pointing towards an association of HSV with ApoE and Alzheimer's disease. Although it has been shown that ApoE impacts HSV-1 spread in animal models in an isoform specific fashion, the molecular relationship between the virus and ApoE is unclear. The present study probes the role of ApoE on the viral life cycle, clearly an important aspect if one is to better understand how the virus may influence the disease. Using assays monitoring various steps of viral replication, the authors report that ApoE perturbs the interaction of the virus with the cell surface, both during the initial binding and following viral release. Furthermore, they show that ApoE 3 and 4 exert a proviral effect, with a smaller impact with ApoE 2.

General Comments

The comprehensive study addresses an important point that may help clarify the interaction between HSV-1 and Alzheimer's disease. It major strength is that it is systematic and elegantly performed. The paper convincingly shows that ApoE impact cell adhesion at the cell surface. In general, the data have properly been analyzed statistically. Some aspects are however enigmatic. First of all, how can ApoE be proviral if it prevents the initial binding of the virus to the cells? Second, less viral binding should mean less entry (as shown in figure 2) and subsequently fewer genome copies, but that is not what is reported in figure 3. This is not clearly stated in the discussion (lines 457-459 and again in lines 490-491). Finally, if ApoE is unstable as indicated on lines 495-497, how can it be active later on at 24 hpi and prevent viral release? How do the authors reconcile these observations? Of interest, ApoE 3 has a slightly greater impact on viral growth than other isoforms (fig 1), which is not quite fitting the model that ApoE4 is the main culprit for Alzheimer's disease. Could the authors comment? Where are the ApoE proteins normally expressed in cells? At the cell surface or intracellularly? This may provide a hint as to where the virus picks it up when incorporating it. Immunofluorescence would be a great addition (e.g., Huh-7 cell line). Similarly, does the virus impact the expression level of ApoE? One could resolve the dilemma that ApoE blocks the initial binding of the virus but stimulates viral release at later time points if the virus induces ApoE at those late times. Furthermore, if the Vero or SH-SY5Y cells don't normally express ApoE, then it should not be important for the virus in that context. How about keratinocytes, the normal host of the virus? These considerations should be addressed in the manuscript by Western blotting at different time points.

Significance

This study adds an interesting twist and advances the infectious etiology model of Alzheimer's disease and should appeal to a broad authorship ranging from the neurobiology to virology.

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Referee #2

Evidence, reproducibility and clarity

In the manuscript "Recruitment of apolipoprotein E facilitates Herpes simplex virus 1 release", by Liu et al, the authors investigate the effect of ApoE protein on HSV-1 replication. Treatment of infected cultures with ApoE proteins appeared to increase the production of infectious titer. The authors perform several experiments to determine which steps of the virus replication cycle are affected. ApoE proteins reduce virus attachment, but subsequent reductions in entry are explained by the reduction in attachment, suggesting that the efficiency of entry is not affected. Viral DNA replication and cell-surface virus amounts appear to be unaffected, but the release of virus titer to the supernatant is increased. These results suggest that ApoE effects virus replication in two ways: reduces attachment if inoculum, but subsequently increases release of progeny. To determine whether this is the case, the authors then measure the release of attached virus particles from native membranes in the presence or absence of ApoE4, and derived from cells inducibly expressing ApoE4.

The manuscript is generally well written and the experiments generally appear to be performed well. However, the importance and impact of this manuscript are limited by two major weaknesses:

1. It seems that effects are only seen with high concentrations of ApoE. How does this concentration compare to what would be found in blood plasma/tissues/secreted by Huh-7 cells? Thus, these results may not be biologically relevant. It is difficult to determine what concentrations of ApoE are used in some cases, e.g. Fig 6. Please provide this information in the figure or figure caption.
2. While there are some interesting results here, this manuscript does not get to the point of establishing mechanism. In the discussion, it is speculated that ApoE functions via GAGs/HSPGs, which are known to affect HSV-1 attachment/release. It would make the manuscript much stronger to include experiments adding soluble heparin or treating cells with heparinase, or producing gC-null virus particles, to see if this abolishes the attachment/release effects of ApoE.

Minor points:

Fig. 3B: It is difficult to compare virus genomes by qPCR to virus titer of supernatants. If ApoE is promoting release of cell surface virus, why does an increase in titer in the supernatants not show a corresponding decrease in cell surface virus?

Fig. 6B: "Spdi I" term is not used in the results section or figure legend. I do not know what "Spdi I" means.

Fig. 6E, Fig 7: Normalized values can be misleading. Please provide raw values. Please show dissociation curves, as in Fig. 6D, for Fig.7.

It would be nice to perform the same analysis of supernatant vs. cell surface vs. intracellular virus as in Fig. 3B, and the release on ice measures as in Fig 4, using the inducible expression HEK cell line.

Discussion: Degradation of ApoE (line 495-500). The degradation of ApoE in these infection experiments could be measured by e.g. western blot of cell supernatants. This suggestion is a bit troubling: If the ApoE is degraded during the first replication cycle, how is it able to have an ongoing effect? How can ApoE simultaneously be present to promote release of progeny, while being degraded so as not to prevent attachment to subsequent cells.

I do not see that "GMK AH-1" cells are available from ATCC, as stated in the methods. Is this a synonym for Vero cells?

Although I understand what is meant, "dissolvent" is not a common term. "diluent" or "vehicle" is more common.

Significance

General assessment: The manuscript is generally well written and the experiments generally appear to be performed well. However, the significance of this manuscript are limited by two major weaknesses:

1. It seems that effects are only seen with high concentrations of ApoE. How does this concentration compare to what would be found in blood plasma/tissues/secreted by Huh-7 cells? Thus, these results may not be biologically relevant. It is difficult to determine what concentrations of ApoE are used in some cases, e.g. Fig 6. Please provide this information in the figure or figure caption.
2. While there are some interesting results here, this manuscript does not get to the point of establishing mechanism. In the discussion, it is speculated that ApoE functions via GAGs/HSPGs, which are known to affect HSV-1 attachment/release. It would make the manuscript much stronger to include experiments adding soluble heparin or treating cells with heparinase, or producing gC-null virus particles, to see if this abolishes the attachment/release effects of ApoE.

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Referee #1

Evidence, reproducibility and clarity

This manuscript attempts to identify the molecular basis for the reported interactions between apolipoprotein E (ApoE) and herpes simplex virus 1 (HSV1), known to be a significant marker for Alzheimer's disease. The authors employ a combination of cellular and in vitro assays designed to assess the effect of ApoE on different stages of the HSV1 life cycle. These experiments reveal an effect of ApoE on virus binding to and detachment from cell membranes, but not in other aspects of the viral life cycle. Further, the isoform ApoE4 was found to be the most effective in exerting these changes, possibly due to competitive binding with cell surface receptors that can associate with both ApoE and HSV1. Prior studies were referenced appropriately. For the most part, sufficient details about the data acquisition and analysis workflow were included in the study, although a couple of exceptions have been noted. More information about number of data sets for each panel and statistical analysis need to be included in the manuscript (figure legends and a separate section in Materials & Methods). Some of the key conclusions from the data require additional context and information to justify their interpretation in the present form. The additional experiments suggested are reasonable in terms of time and resources and are critical for strengthening the key conclusions in the manuscript. These have been noted below. Comments on evidence, reproducibility and clarity

Major Comments:

1. The authors mention in the Discussion section that they have ruled out interaction of ApoE with HSV1 glycoproteins B, C, D, and E based on immunoprecipitation data that is not included in the manuscript. In view of this, how do they justify using HSV1 gC as a marker for checking for association of HSV1 with ApoE (Fig 5)? Further, the authors should consider including said immunoprecipitation data in the manuscript, since those would be of immense value in further studies looking for other interaction partners of ApoE (as the authors have stated in the Discussion section).
2. How strong are the interactions between ApoE and HSV-1? In other words, what fraction of the available ApoE could be expected to associate stably with HSV1? Can ApoE or ApoE-associated complexes act as a trap for the virus and therefore represent latent virus pools in cells? How were possible contributions to HSV1 detachment from other cellular factors associated with ApoE ruled out?
3. The Discussion section of the manuscript clearly places the detected interaction of ApoE with HSV1 in the context of previous literature on related facets of the crosstalk between ApoE and viral infections. The authors may also consider including a paragraph on the more physicochemical attributes of ApoE interaction with HSV1, which would make the Discussion section more well-rounded and provide some background for understanding the biophysical experiments reported here (Fig. 6, 7). For example, how do the dissociation rates they report in Fig. 6 compare to those reported earlier for viruses on SLBs or cellular membranes? Could these dissociation rates be readily converted to (at least semi-quantitative) estimates of the thermodynamics of ApoE binding to HSV1 or would other factors need to be explicitly considered for such analytical exercises? Would it be difficult to measure binding affinities using HSV1 and purified ApoE by complementary approaches such as calorimetry or surface plasmon resonance? On a related note, what kind of ApoE concentration could HSV1 encounter in a cellular milieu and would it be in the range (5 μM) at which they report significant effects of ApoE on HSV1? What could be expected to happen at even higher concentrations of ApoE (reported for other cellular pathologies)?<br /> Why is the isoform dependence of ApoE effects observed predominantly in case of HSV1? Could this be related to the more complex fusion machinery available to this virus?
4. It is strongly recommended that details about ApoE purification and characterization are included in the manuscript, along with appropriate references. It is also not clear how a 4h period was deemed to be sufficient for incubation with ApoE (Fig. 2).
5. The data in Fig 4 is not entirely sufficient to support claims of ApoE enrichment in virus particles released into the supernatant. The authors may consider including additional experiments to check for (and quantify, if possible) ApoE levels in these virus fractions (since these conditions are drastically different than that used for reporting co-sedimentation of ApoE and HSV-gC in Fig. 6B).
6. Fig 5: It is not clear why the authors tested only for gC (especially when they note that co-immunoprecipitation experiments have ruled out gC as a possible interaction partner for ApoE; also see comment 1). Is the shift in the ApoE band to higher kD values from fraction 1 to 6 significant? What do the error bars in Fig 5B represent, if data was generated from two independent replicates? How do you reconcile the very high viral titer of fraction 3 (Fig 5C) with the moderate level of gC_HSV-1 in the same fraction (Fig 5B)? Does this indicate heterogeneity in gC content across seemingly equivalent viral titers (fractions 1-3, based on Fig 5C) ?
7. Several inconsistencies were noted in figures and figure legends that could affect a clear understanding of the data by readers. For all figures, please indicate clearly if no notation for statistical tests denote an absence of significance (ns) or that significance was not tested (such as for Fig. 2B, C). Please include sufficient information regarding number of independent replicates for each panel (i.e., what do error bars represent). For t-tests, please indicate clearly the reference data sets used for testing statistical significance and define symbols used for different p-values only for that specific figure. For example, a p-value corresponding to * is defined in the legend to Fig. 2, although that p-value is not indicated in the figure.

Minor Comments:

1. P. 4: abbreviation HSPG is not defined
2. Inconsistent figure formatting noted in terms of non-uniform axis labels, color coding, inclusion of error bars, clear label of all lanes in blots. These should be reviewed and modified as appropriate.
3. Fig 1A: The authors may consider reverting the order of ApoE concentration (ascending, instead of descending) in X-axis label to make it more intuitive.
4. Line 167: please specify that data in Fig S1b refers only to SH-SY5Y cells.
5. In Fig 2A, value for dissolvent should be set to 100%, since rest of the data are normalized with respect to that.
6. Line 279 refers to Fig. 3C (not present in the manuscript).
7. Ladders not clearly visible in some blots, such as that for 50 kD in Fig S1 and Fig 5A (HSV1 infected panel).
8. Please indicate clearly in the Materials & Methods if ApoE induction (Fig. 7) is performed in HEK cells or HEK-293T cells.

Significance

This study sheds light on the molecular basis of the interaction between HSV1 and ApoE and represents a conceptual advance in the field. Since such interactions have been reported to be a marker for patients at high risk of developing Alzheimer's disease, these findings would be important in designing future clinical studies on prognostic and diagnostic advances in neurodegenerative diseases. As such, this manuscript would be of interest to a broad spectrum of scientists and clinicians including virologists, biochemists, and biophysicists.

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Reply to the reviewers

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

Hermanns et al. report a robust biochemical and structural characterization of the TSSM virulence effector of Burkholderia pseudomallei, the causative agent of melioidosis, with TSSM being the only USP-type deubiquitinase of bacterial origin. The authors demonstrate ubiquitin specificity, and the capacity of the DUB to cleave most Ubiquitin chain types in vitro. By solving crystal structures of TSSM in isolation as well as in covalent complex with Ubiquitin, the authors rationalize how the truncated fold (compared to all other eukaryotic USPs) is capable of binding ubiquitin. The most surprising finding is the conformation of the so-called little finger loop, unique to TSSM, which engages the distal Ubiquitin in a manner not seen in any other DUB. These findings are convincingly validated by point mutations in biochemical assays and bioinformatic analyses. The structures also yielded information on the fold an N-terminal Ig-like domain with unknown function.

The authors are encouraged to address the following main points before publication can be supported:

• On page 6, the authors state "the little finger loop contacts hydrophobic residues around Ile-44 of ubiquitin, an important interaction interface that is not observed in USP7 and is not part of the canonical USP: ubiquitin interface". The latter statement I believe is simply wrong as Ile44 is at the centre of the large canonical USP:ubiquitin interaction interface observed in all structurally studied USP proteins so far (the recognition is through varying residues, that are not always strictly hydrophobic, but it is always contacted). This is occurring at the hinge between thumb and fingers. In USP7, this is for example occurring through the hydrophobic part of Arg301. The authors are referred to O'Dea et al. Nat Chem Biol 2023, where same conformation of the equivalent residue in USP36 is discussed in the context of Ile44-Ubiquitin vs. Fubi recognition.

We thank reviewer #1 for this detailed explanation. Initially we made this statement based on the fact that in other USPs, the interaction is not always hydrophobic. However, we now agree with reviewer #1 and have removed this statement from the manuscript.

• This should also be phrased very precisely, as Ile44 itself is not actually contacted by the little finger loop (see Fig. 3c), but other hydrophobic residues commonly included in the Ile44 patch are. However, also those are always in the Ubiquitin:USP interface.

These section was removed in line with the previous point. Additionally, we added the information that Ile44 itself is not contacted to the main text.

• It appears as if the little finger loop takes up the exact position of what is commonly referred to as blocking loop 1 (terminology introduced by Hu et al EMBO J 2005, which the authors could also use when referring to canonical USPs). The connectivity in the domain is not equivalent to BL1 though (this could be shown with topology diagrams of a canonical USP and of TSM), but the relative position is. Importantly, BL1 in USPs typically engage the Ile36 patch with a large aromatic residue (e.g., a Trp in USP30 or a Tyr in USP7), however, in TSSM Ubiquitin is rotated such that the Ile44 patch is recognised at the exact spot where normally Ile36 is engaged. Can the authors comment on this interpretation? This reviewer would also find a comparison to the canonical USP recognition mode in the main figures beneficial (however one that is less crowded than in the SI) to make this very important finding come across well. Even if the loop is more like a BL1 (which is highly diverse in the USP family, see reference above), it can still be called "little finger", but the analogies should be carefully phrased throughout the text (e.g., page 9: "functionally but not structurally analogous" would not be correct if it does not replace the fingers which contact Phe4 as BL1 is not part of the fingers).

The reviewer is correct. The positioning of BL1 from canonical USPs and the TssM Littlefinger loop is superficially similar. Since the Littlefinger is derived from a different part of the sequence (Fig 1a) and contacts a different patch of ubiquitin, it is still distinct from the BL1. We have incorporated this information into the main text and generated a new superposition to show the structural similarities (Supplementary Fig 3c). Additionally, we highlighted BL1 and Littlefinger in Fig1a to show the different position within the amino acid sequence. Since BL1 and Littlefinger are distinct from each other we still classify the Littlefinger as functionally (but not structurally) analogous to the fingers domains. Both serve as the main contacts to ubiquitin and (partially) interact with the Ile44 patch, while BL1 contacts the Ile36 patch.

• The assessment of the molecular weight of apo TSSM in solution by SEC is flawed in its current form (page 7, Fig. 4b). There are only two, seemingly randomly chosen, comparison proteins, and the GST-Ub is unsuitable for 36 kDa because it is an obligate dimer (due to the GST) and as a fusion protein has a much higher hydrodynamic radius than a globular protein. There are commercial reference proteins that can be used which have defined oligomerisation states and are (reasonably globular) so that the retention times can be quantitatively analysed. Such a reference, which also includes proteins of smaller sizes, must be used. Alternatively, the authors should use light-scattering (SEC-MALS or SEC-RALS) to unequivocally demonstrate the molecular weight / oligomeric state of TSSM.

The experiment has been re-done using commercially proteins routinely used for the calibration of SEC columns. Additionally, a 75pg column was used to achieve a better resolution of the proteins. The new data confirm the original conclusion that TssM behaves like a monomer in solution.

• The abstract ends with speculation on the presence of the strand-swapping in live cells and of the role of the Ig-fold domain, but not a proper conclusion. The same applies to the ending of the results section (page 8), where it is not clear where the structural analysis of the Ig-like domains is leading. The authors then speculate about sugar binding (page 10) in the discussion. The latter could be substantiated by an analysis of the residues in the possible sugar binding site (if present in their TSSM), and the text be more rounded off at these regions.

We admit that our manuscript does not reveal the function of the Ig-like domain and the strand swap observed in the apo structure. To really address these questions, an infection model would be required, which is outside the scope of our manuscript focussing on the TssM mechanism. As have showed that deletion of the Ig-domain does not alter the DUB properties, the remaining questions cannot be addressed in vitro. To address the concerns of the reviewer, we have changed the ending of the result section (page 8) to summarize our in vitro data on the Ig-like domain. We have also clarified the paragraph discussing the possibility of sugar binding on pages 10/11. In brief, this speculation was not based on the identification of a possible sugar binding site, but rather on the presumed positioning of the Ig-like domain relative to the bacterial surface and its evolutionary relationship to other sugar-binding domains.

• The authors show in Fig. 1b TSSM reactivity with both Ubiquitin and Nedd8 probes but then qualify the Nedd8-reactivity with the assays shown in Figs. 1cd, which currently looks like it is an issue with the comparison of probe to substrate. However, their probe assay is very long with 18 h. It should be repeated at shorted times (for Ub and Nedd8-PA only) to test if the strong Ub preference seen in the kinetic assay can also be visualized with the probes.

We measured the requested time curve and added the data to the newly generated Supplementary Figure 1. Using very short time points of 3 – 20min, a preferential reactivity with the ubiquitin probe became visible, which supports the AMC results.

• Moreover, the authors prepare Ubl-PA probes by aminolysis of C-terminal thioesters but at very different stoichiometries as reported for Ub-PA (e.g., in Gersch et al. NSMB 2017). The precise amounts should be cross-checked. This reviewer would not be surprised if the conditions of only 2-fold excess of propargylamine over Ubl thioester and the high amount of NaOH led also to hydrolysis of the C-terminus, which by size exclusion chromatography would not be separated. For all probes, intact mass spectra of the used aliquots must be shown to demonstrate the identity of the used reagents. The presence of other species of course does not per se disqualify the assay in Fig. 1b.

Our protocol for generating the Ub-PA probe follows exactly the one described in Gersch et al 2017. While this publication describes the amounts and concentrations of the individual reagents, our description of the protocol documents their final concentration in the reaction mixture. We double-checked the data and found them to be identical. Thus, there is no reason to assume elevated amounts of hydrolysis products. Moreover, the purity of our probes is regularly controlled by intact mass spectrometry (shown below for Ub-PA). The observed ~5% of hydrolysis product should not pose a problem for the assays, which routinely involve a 10x excess of probe over DUB. As documented in the Materials section, the Nedd-PA probe was obtained from Monique Mulder in Leiden.

In addition, the following minor points should be addressed:

• On page 2, the authors state that the 1-2 DUBs typically present in bacteria either target K63-chains or lack specificity (without reference), but on page 10 they state that bacteria typically only have 1 DUB with little specificity. This is contradicting and should be fixed.

We have rephrased the introductory sentence on page 2 and added a reference. The issue on page 10 has been corrected

• On page 3, the authors make the case for TSSM from B. pseudomallei by calling it representative. This reviewer would appreciate if the authors could expand on this towards the end of the manuscript and comment on whether they expect the identified Ubiquitin recognition mode to be present also in all (!) other DUB-TSSM proteins, at least all analysed bioinformatically. Importantly, they should include the sequence of TSSM of B. mallei (the only in vitro studied TSSM so far) into their analyses in the SI.

We have expanded the paragraph (page 9) where we discuss the conservation of the Littlefinger-based ubiquitin recognition mode. Among the TssM-like DUBs that we identified, only those from other Burkholderia species contain the Littlefinger conservation and are predicted (by alphafold) to use this region for S1-ubiquitin recognition. The two non-Burkholderia TssM-like DUBs (one from Chromobacterium sinusclupearum, the other from an unidentified bacterial metagenome) lack the Littlefinger region and the associated ubiquitin recognition mode. This is documented in Supplementary Fig 4. We also added B. mallei to the alignment in Supplementary Fig 4a, although it is almost identical to the B. pseudomallei sequence.

• On page 4, the authors start with TSSM (193-490) but do not comment on the role of the first 192 residues. What was the rational for these boundaries?

The N-terminal 192 amino acids are predicted to be unstructured (by alphafold, IUPRED, etc). We therefore decided to use the entire folded part of TssM for the first experiments. The information has been added to the manuscript and a domain scheme was added to the supplementary data (Supplementary Figure 1a).

• On page 4, the authors introduce the use of the fluorogenic AMC substrates with "more quantitative analysis", however, the experiments are rather minimalistic. Only one substrate concentration, and two enzyme concentrations (at least for one substrate) are used, and the data are not really analysed in a quantitative manner. Through curve fitting of the existing data (with fixed restraints) the authors may be able to determine an estimate of the Ub/Nedd8-specificity factor. Moreover, negative controls should be shown in Figure 1c to demonstrate that the Nedd8-curve is above a possible baseline drift.

Following this reviewer’s suggestion, we estimated a 116x better cleavage of ubiquitin-AMC by determination of the initial velocities using the linear range of the data presented in Figure 1c.

For ensuring better clarity, we have omitted the negative control data from Fig 1 panel c (comparing Ub-AMC and Nedd8-AMX) but are showing them in panel 1d (comparing Nedd8-AMC to negative control). This figure clearly shows that Nedd8-AMC is really cleaved, whereas no baseline drift is visible.

• On page 4, the authors mention a possible relationship with the Josephin family (which they later disprove through structural comparisons, page 6). It may be helpful to briefly explain the rational (i.e., why one would even consider a relationship with the Josephin family DUB given the higher homology to the USP fold).

The rationale for considering a relationship to the Josephin family is explained at the end of the introduction section (page 3). We never considered TssM to be closer related to Josephins than to USPs. We rather speculated that the entire USP and Josephin families are distantly related to each other, and that TssM-like USPs might form a kind of missing link. This latter aspect has been disproved (page 6), since the TssM structure is no more Josephin-like than that of any other USP.

• On page 5, the "shortened C-terminus" compared to USP7 is mentioned. This is misleading, as USP7 has an elongated C-terminus compared to most other USPs, and so the TSSM C-terminus is the canonical ending of the USP fold.

The section has been rephrased and now points out that TssM shares the canonical USP C-terminus.

• On page 6, "ubiquitin has multiple specific contacts" - why are the contacts named "specific"?

We have removed the word ‘specific’

• On page 10, the TSSM from C. sinusclupearum appears without any context. Chromobacterium should be spelled out, and it should be discussed if this is the odd one out. It would also be appreciated if the authors could state whether their bioinformatic analysis is comprehensive (i.e., do only the known or all Burkholderia strains have TSSM with a DUB profile). And why is there a A0A1J5... sequence included in Supp Fig. 3a without any context?

We agree that this part of the text was confusing. We have now bundled all information on other TssM-like sequences on page 9. There, we explain that TssM-like DUBs are only found in selected Burkholderia lineages, and spell out some examples. We also introduce Chromobacterium sinusclupearum with its full name and explain that the remaining non-Burkholderia TssM homolog is from an unidentified metagenomic sequence. This is also the reason why we refer to this sequence by its Uniprot accession number.

• Some minor polishing in the methods would increase consistency (cloning is only mentioned for pOPIN-K, but TSSM is also expressed from pOPIN-S; mutants are only mentioned for the 292-490 construct, but Fig. 2d shows one in the 193-490 construct; Hampton Additive Screens I-III are likely an internal name and not used by Hampton itself; "different TSSM concentrations (as indicated in the figure legends" are mentioned in the methods, but e.g. in the caption to Fig. 1 no concentration is given).

We have added the pOPIN-S cloning method and corrected the name of the additive screen. We now provide all mutant data in the 292-490 background (Figure 2d was updated accordingly). We made sure that all figure captions mention the enzyme concentrations.

• Likewise, Table 1 needs polishing as commas and points are used interchangeably.

Table 1 has been corrected

• In Fig. 2c, it looks like the catalytic His is built such that there is no hydrogen bonding between Cys and Asp - is there a particular reason for this? If not, the side chain should be flipped so that the nitrogens are positioned for ideal hydrogen bonding.

Fig 2c had been accidentally exported from an early version of the structure. It has now been replaced by a panel that uses the final and deposited version of the structure. Here, the His position is correct.

• In Fig. 3, dotted lines are introduced as "hydrophobic interactions" as per the captions, but some are clearly hydrogen bonds (e.g., from the amide backbone), and for some others one does not see as they emerge from a cartoon.

In Fig 3, dotted lines are not generally introduced as "hydrophobic interactions". Instead, the individual panels have their own definition for the dotted lines. c) hydrophobic d) hydrogen bonds e) hydrophobic.

• In Fig. 4, context should be given to "3VYP" and why it is used here.

We have added an explanation of 3VYP to the figure legend (The reason for showing it is also explained in the main text)

**Referees cross-commenting**

Reviewer comments appear to be fair, balanced and complementary.

Re Reviewer 2's comment on the pre-print: It includes a structure of TSSM bound to ubiquitin (but not of the apo protein). I am not sure if it is appropriate to follow up on the esterase activity. Firstly, there are no tools for it commercially available or readily made in vitro, and secondly it would appear a bit "copycat"-like. Especially since the molecular determinants of what makes a DUB a good esterase are still elusive. A narrower focus of this manuscript, but done very well (also according to what reviewer 3 suggested), might be a more fitting option.

Reviewer #1 (Significance (Required)):

The findings are novel and of high relevance to the broad ubiquitin and bacterial pathogen communities as the study addresses an enigmatic USP-type deubiquitinase which, as the authors reveal, recognizes Ubiquitin in an entirely different way than its eukaryotic counterparts. This is basic research of pronounced conceptual and mechanistic advance, as it demonstrates that the USP domain can be much more diversified than previously assumed. The structural analysis is very thorough, the data are scholarly presented, and interactions/mechanisms carefully validated by mutations.

The strongest point is clearly the structural analysis of Ubiquitin recognition by this extremely truncated USP fold, and the introduction of the little finger motif. The manuscript does not provide cellular validation of the findings, which is fine to this reviewer for the DUB catalysis part. For the part of the N-terminal domain, the manuscript would benefit from a cellular validation or some localisation studies, however, this is beyond what is established in the authors' lab, and therefore has not been asked. This in turn limits the study to a very thorough in-vitro analysis of this DUB for TSSMs with DUB activity, using conventional substrates like polyUb chains and fluorogenic substrates, and providing convincing conclusions.

My expertise lies in DUBs, biochemistry, and structural biology, and I this believe to have sufficient expertise to evaluate the majority of the findings except the bioinformatic algorithms used which are however not an emphasis in this manuscript.

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

In this manuscript, the authors solved crystal structures of apo-TssM and its complex with Ubiquitin. Together with the biochemical assays, the authors highlighted the differences of TssM from other USP family. TssM do not contain the classical finger domain while it has little finger domain that authors defined. The Ile44 patch on the ubiquitin is mainly used for interacting with TssM.

For the clarity of there findings several points should be edited.

1) In Fig 2d, the authors used different constructs for testing catalytic residues. It will be better to be consistent. Though the authors showed that the deletion of Ig-like domain does not affect the catalytic activity of TssM by showing the AMC assay, it does not guarantee that the effect of mutation on catalytic sites is same for both construct.

The experiment has been repeated with TssM292-490 C308A and the panel in Fig 2d has been replaced

.

2) In fig 2d, authors need to put the label to indicate which linkage of di-Ub is used. Authors did it for figure 2f.

Chain type was already stated in the legend, but was now also added to the respective panel.

3) By showing AMC assay (fig 2e) and K63 Ub2 cleavage assay (fig 2f), authors concluded that the deletion of Ig-like domain does not affect the activity of TssM. However, as authors found that the Ig-like domain forms dimer at least in their crystallization condition, one cannot exclude the possibility of the role of Ig-like domain in recognising different ubiquitin chains. I would clarify the words by saying "The Ig-like domain does not affect the cleavage K63-Ub2), or authors can expand the cleavage assay with all the linkages.

We agree with reviewer #2 and rephrased the corresponding sentence.

4) In the apo structure, authors found a domain swapped dimer. One can expect that this dimer is crystallographic artifact and not found in the nature. Indeed, authors could not observe this dimer in the solution when they performed SEC analysis and there was no effect on the catalytic activity when the Ig-like domain is deleted. Because there is no clear evidence of functional importance of this dimer in the manuscript, authors need to clarify about this dimer.

We agree with reviewer #2 that there is no evidence for functional importance of the dimer. We had already addressed this issue in our discussion section, where we hypothesized a potential in vivo function. We have now rephrased this section of the discussion in order to make it more precise.

**Referees cross-commenting**

Agree with Reviewer #1's comment on my points.

Reviewer #2 (Significance (Required)):

The structure of TssM is recently reported in a preprint ( https://doi.org/10.21203/rs.3.rs-2986327/v1) from Pruneda (OHSU). In this preprint, they suggested the role of TssM as Ubiquitin esterase which is not explored in the this manuscript. As it is already published and freely available, authors can explore the role of TssM in that direction as well. Because the preprint do not contain the complex structure of TssM with Ubiquitin, authors can also examine the roles of Ile44 patch-interacting residues on the catalytic activities.

Said preprint contains the TssM~Ub complex structure, but not the structure of the apo form. The role of the Ile44-patch contacting residues is also already analysed in regards of esterase activity. As explained in the ‘general points’ at the top of the rebuttal letter, the two manuscripts were meant to be submitted simultaneously. Due to a delay in our PDB deposition/validation, we submitted our version two weeks later. Thus, we share the opinion of reviewer #1 that it would be inappropriate to use our competitors’ data and analyse esterase activity in our manuscript. Instead, we added a reference to the competing preprint to our discussion section and briefly compare the key findings. The authors of the preprint have agreed to reciprocate and reference our preprint in their revised manuscript.

Also, authors can compare their little finger structure with the preprint.

See point above.

In general, this manuscript is providing several interesting points to the readers working on the ubiquitin, structures of proteins, host-pathogen interactions and especially those who studying deubiquitinases.

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

In this study, Hermanns et al. have examined the Burkholderia TssM deubiquitinase (DUB) for its ubiquitin chain cleavage specificity using in vitro analyses and for a structural rationalization of its specificity by solving crystal structures with and without covalently bound ubiquitin. TssM was previously shown to be a DUB of the USP family capable of cleaving several ubiquitin chain types. From bioinformatic comparisons, the authors inferred that TssM lacks the 'fingers' domain of classic USP enzymes, and this was shown in the co-crystal structure to be replaced by a 'Littlefinger' loop. The work here is well described and appears to be overall technically solid.

My enthusiasm is reduced for several reasons. First, there is no analysis in an (infected) cell model to evaluate the significance of the TssM mutations, for example, the mutations in ubiquitin-interacting surfaces that are not seen in classic USPs. Second, there is very little quantitation of cleavage rates; while I would not demand derivation of kinetic values for all mutants, the qualitative treatment was not always convincing. For example, Y443A was said to cause "strongly reduced cleavage" (Fig. 4h) whereas E378A was said to "only mildly affect cleavage" (Fig. 4i): to my eye, these cleavage rates are only slightly different (2-3 fold?).

In order to support the findings of our gel based assay and to get more quantitative data, we tested all mutants against Ub-AMC. The results are depicted in supplementary figures 3d/f/g and correspond to results of the chain cleavage assays.

Finally, there is a preprint available on Research Square (doi: 10.21203/rs.3.rs-2986327/v1) that shows a potent esterase activity of TssM against ubiquitinated LPS, which is probably its key role in avoiding surveillance and elimination by the host. This paper, although still a preprint, is far more quantitative, includes similar crystallographic data as in the current paper, and describes cellular assays of function. Even without the RS preprint, the Hermanns et al. study provides a fairly modest advance in our knowledge of TssM function; with the preprint, its novelty is, unfortunately, severely reduced.

As explained in the ‘general points’ at the top of the rebuttal letter, the two manuscripts were meant to be submitted simultaneously. Due to a delay in our PDB deposition/validation, we submitted our version two weeks later. The competing work is currently under review at a top-tier journal and far from being accepted. We therefore ask to consider the significance of our own manuscript based on the peer-reviewed state-of-the-art.

In our revised manuscript, we have added a brief discussion of the pre-published results. The authors of the preprint have agreed to reciprocate and address our data in their revised manuscript.

Minor comments:

Full genus names should be spelled out when they first appear in the text (such as Burkholderia and Chromobacterium).

Genus names are now spelled out.

Fig. 3a is described out of sequence.

A reference to figure 3a was missing in the beginning of the chapter. The reference was added and the figure is now described in sequence.

In Fig 4a, there still seem to be extensive contacts between monomers but the viewing angle could be misleading.

There are no extensive contacts between the two DUB monomers in the right panel (complex structure). We slightly changed the viewing angle in Fig 4a to make this clearer.

**Referees cross-commenting**

I also agree with Reviewer #1's comments

Reviewer #3 (Significance (Required)):

Even without the Research Square preprint (doi: 10.21203/rs.3.rs-2986327/v1), the Hermanns et al. study provides a fairly modest advance in our knowledge of TssM function; but with the preprint, its novelty is, unfortunately, severely reduced.

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

In this study, Hermanns et al. have examined the Burkholderia TssM deubiquitinase (DUB) for its ubiquitin chain cleavage specificity using in vitro analyses and for a structural rationalization of its specificity by solving crystal structures with and without covalently bound ubiquitin. TssM was previously shown to be a DUB of the USP family capable of cleaving several ubiquitin chain types. From bioinformatic comparisons, the authors inferred that TssM lacks the 'fingers' domain of classic USP enzymes, and this was shown in the co-crystal structure to be replaced by a 'Littlefinger' loop. The work here is well described and appears to be overall technically solid.

My enthusiasm is reduced for several reasons. First, there is no analysis in an (infected) cell model to evaluate the significance of the TssM mutations, for example, the mutations in ubiquitin-interacting surfaces that are not seen in classic USPs. Second, there is very little quantitation of cleavage rates; while I would not demand derivation of kinetic values for all mutants, the qualitative treatment was not always convincing. For example, Y443A was said to cause "strongly reduced cleavage" (Fig. 4h) whereas E378A was said to "only mildly affect cleavage" (Fig. 4i): to my eye, these cleavage rates are only slightly different (2-3 fold?). Finally, there is a preprint available on Research Square (doi: 10.21203/rs.3.rs-2986327/v1) that shows a potent esterase activity of TssM against ubiquitinated LPS, which is probably its key role in avoiding surveillance and elimination by the host. This paper, although still a preprint, is far more quantitative, includes similar crystallographic data as in the current paper, and describes cellular assays of function. Even without the RS preprint, the Hermanns et al. study provides a fairly modest advance in our knowledge of TssM function; with the preprint, its novelty is, unfortunately, severely reduced.

Minor comments:

Full genus names should be spelled out when they first appear in the text (such as Burkholderia and Chromobacterium).

Fig. 3a is described out of sequence.

In Fig 4a, there still seem to be extensive contacts between monomers but the viewing angle could be misleading.

Referees cross-commenting

I also agree with Reviewer #1's comments

Significance

Even without the Research Square preprint (doi: 10.21203/rs.3.rs-2986327/v1), the Hermanns et al. study provides a fairly modest advance in our knowledge of TssM function; but with the preprint, its novelty is, unfortunately, severely reduced.

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

In this manuscript, the authors solved crystal structures of apo-TssM and its complex with Ubiquitin. Together with the biochemical assays, the authors highlighted the differences of TssM from other USP family. TssM do not contain the classical finger domain while it has little finger domain that authors defined. The Ile44 patch on the ubiquitin is mainly used for interacting with TssM.

For the clarity of there findings several points should be edited.

1. In Fig 2d, the authors used different constructs for testing catalytic residues. It will be better to be consistent. Though the authors showed that the deletion of Ig-like domain does not affect the catalytic activity of TssM by showing the AMC assay, it does not guarantee that the effect of mutation on catalytic sites is same for both construct.
2. In fig 2d, authors need to put the label to indicate which linkage of di-Ub is used. Authors did it for figure 2f.
3. By showing AMC assay (fig 2e) and K63 Ub2 cleavage assay (fig 2f), authors concluded that the deletion of Ig-like domain does not affect the activity of TssM. However, as authors found that the Ig-like domain forms dimer at least in their crystallization condition, one cannot exclude the possibility of the role of Ig-like domain in recognising different ubiquitin chains. I would clarify the words by saying "The Ig-like domain does not affect the cleavage K63-Ub2), or authors can expand the cleavage assay with all the linkages.
4. In the apo structure, authors found a domain swapped dimer. One can expect that this dimer is crystallographic artifact and not found in the nature. Indeed, authors could not observe this dimer in the solution when they performed SEC analysis and there was no effect on the catalytic activity when the Ig-like domain is deleted. Because there is no clear evidence of functional importance of this dimer in the manuscript, authors need to clarify about this dimer.

Referees cross-commenting

Agree with Reviewer #1's comment on my points.

Significance

The structure of TssM is recently reported in a preprint ( https://doi.org/10.21203/rs.3.rs-2986327/v1) from Pruneda (OHSU). In this preprint, they suggested the role of TssM as Ubiquitin esterase which is not explored in the this manuscript. As it is already published and freely available, authors can explore the role of TssM in that direction as well.

Because the preprint do not contain the complex structure of TssM with Ubiquitin, authors can also examine the roles of Ile44 patch-interacting residues on the catalytic activities.

Also, authors can compare their little finger structure with the preprint.

In general, this manuscript is providing several interesting points to the readers working on the ubiquitin, structures of proteins, host-pathogen interactions and especially those who studying deubiquitinases.

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

Hermanns et al. report a robust biochemical and structural characterization of the TSSM virulence effector of Burkholderia pseudomallei, the causative agent of melioidosis, with TSSM being the only USP-type deubiquitinase of bacterial origin. The authors demonstrate ubiquitin specificity, and the capacity of the DUB to cleave most Ubiquitin chain types in vitro. By solving crystal structures of TSSM in isolation as well as in covalent complex with Ubiquitin, the authors rationalize how the truncated fold (compared to all other eukaryotic USPs) is capable of binding ubiquitin. The most surprising finding is the conformation of the so-called little finger loop, unique to TSSM, which engages the distal Ubiquitin in a manner not seen in any other DUB. These findings are convincingly validated by point mutations in biochemical assays and bioinformatic analyses. The structures also yielded information on the fold an N-terminal Ig-like domain with unknown function.

The authors are encouraged to address the following main points before publication can be supported:

• On page 6, the authors state "the little finger loop contacts hydrophobic residues around Ile-44 of ubiquitin, an important interaction interface that is not observed in USP7 and is not part of the canonical USP: ubiquitin interface". The latter statement I believe is simply wrong as Ile44 is at the centre of the large canonical USP:ubiquitin interaction interface observed in all structurally studied USP proteins so far (the recognition is through varying residues, that are not always strictly hydrophobic, but it is always contacted). This is occurring at the hinge between thumb and fingers. In USP7, this is for example occurring through the hydrophobic part of Arg301. The authors are referred to O'Dea et al. Nat Chem Biol 2023, where same conformation of the equivalent residue in USP36 is discussed in the context of Ile44-Ubiquitin vs. Fubi recognition.
• This should also be phrased very precisely, as Ile44 itself is not actually contacted by the little finger loop (see Fig. 3c), but other hydrophobic residues commonly included in the Ile44 patch are. However, also those are always in the Ubiquitin:USP interface.
• It appears as if the little finger loop takes up the exact position of what is commonly referred to as blocking loop 1 (terminology introduced by Hu et al EMBO J 2005, which the authors could also use when referring to canonical USPs). The connectivity in the domain is not equivalent to BL1 though (this could be shown with topology diagrams of a canonical USP and of TSM), but the relative position is. Importantly, BL1 in USPs typically engage the Ile36 patch with a large aromatic residue (e.g., a Trp in USP30 or a Tyr in USP7), however, in TSSM Ubiquitin is rotated such that the Ile44 patch is recognised at the exact spot where normally Ile36 is engaged. Can the authors comment on this interpretation? This reviewer would also find a comparison to the canonical USP recognition mode in the main figures beneficial (however one that is less crowded than in the SI) to make this very important finding come across well. Even if the loop is more like a BL1 (which is highly diverse in the USP family, see reference above), it can still be called "little finger", but the analogies should be carefully phrased throughout the text (e.g., page 9: "functionally but not structurally analogous" would not be correct if it does not replace the fingers which contact Phe4 as BL1 is not part of the fingers).
• The assessment of the molecular weight of apo TSSM in solution by SEC is flawed in its current form (page 7, Fig. 4b). There are only two, seemingly randomly chosen, comparison proteins, and the GST-Ub is unsuitable for 36 kDa because it is an obligate dimer (due to the GST) and as a fusion protein has a much higher hydrodynamic radius than a globular protein. There are commercial reference proteins that can be used which have defined oligomerisation states and are (reasonably globular) so that the retention times can be quantitatively analysed. Such a reference, which also includes proteins of smaller sizes, must be used. Alternatively, the authors should use light-scattering (SEC-MALS or SEC-RALS) to unequivocally demonstrate the molecular weight / oligomeric state of TSSM.
• The abstract ends with speculation on the presence of the strand-swapping in live cells and of the role of the Ig-fold domain, but not a proper conclusion. The same applies to the ending of the results section (page 8), where it is not clear where the structural analysis of the Ig-like domains is leading. The authors then speculate about sugar binding (page 10) in the discussion. The latter could be substantiated by an analysis of the residues in the possible sugar binding site (if present in their TSSM), and the text be more rounded off at these regions.
• The authors show in Fig. 1b TSSM reactivity with both Ubiquitin and Nedd8 probes but then qualify the Nedd8-reactivity with the assays shown in Figs. 1cd, which currently looks like it is an issue with the comparison of probe to substrate. However, their probe assay is very long with 18 h. It should be repeated at shorted times (for Ub and Nedd8-PA only) to test if the strong Ub preference seen in the kinetic assay can also be visualized with the probes.
• Moreover, the authors prepare Ubl-PA probes by aminolysis of C-terminal thioesters but at very different stoichiometries as reported for Ub-PA (e.g., in Gersch et al. NSMB 2017). The precise amounts should be cross-checked. This reviewer would not be surprised if the conditions of only 2-fold excess of propargylamine over Ubl thioester and the high amount of NaOH led also to hydrolysis of the C-terminus, which by size exclusion chromatography would not be separated. For all probes, intact mass spectra of the used aliquots must be shown to demonstrate the identity of the used reagents. The presence of other species of course does not per se disqualify the assay in Fig. 1b.

In addition, the following minor points should be addressed:

• On page 2, the authors state that the 1-2 DUBs typically present in bacteria either target K63-chains or lack specificity (without reference), but on page 10 they state that bacteria typically only have 1 DUB with little specificity. This is contradicting and should be fixed.
• On page 3, the authors make the case for TSSM from B. pseudomallei by calling it representative. This reviewer would appreciate if the authors could expand on this towards the end of the manuscript and comment on whether they expect the identified Ubiquitin recognition mode to be present also in all (!) other DUB-TSSM proteins, at least all analysed bioinformatically. Importantly, they should include the sequence of TSSM of B. mallei (the only in vitro studied TSSM so far) into their analyses in the SI.
• On page 4, the authors start with TSSM (193-490) but do not comment on the role of the first 192 residues. What was the rational for these boundaries?
• On page 4, the authors introduce the use of the fluorogenic AMC substrates with "more quantitative analysis", however, the experiments are rather minimalistic. Only one substrate concentration, and two enzyme concentrations (at least for one substrate) are used, and the data are not really analysed in a quantitative manner. Through curve fitting of the existing data (with fixed restraints) the authors may be able to determine an estimate of the Ub/Nedd8-specificity factor. Moreover, negative controls should be shown in Figure 1c to demonstrate that the Nedd8-curve is above a possible baseline drift.
• On page 4, the authors mention a possible relationship with the Josephin family (which they later disprove through structural comparisons, page 6). It may be helpful to briefly explain the rational (i.e., why one would even consider a relationship with the Josephin family DUB given the higher homology to the USP fold).
• On page 5, the "shortened C-terminus" compared to USP7 is mentioned. This is misleading, as USP7 has an elongated C-terminus compared to most other USPs, and so the TSSM C-terminus is the canonical ending of the USP fold.
• On page 6, "ubiquitin has multiple specific contacts" - why are the contacts named "specific"?
• On page 10, the TSSM from C. sinusclupearum appears without any context. Chromobacterium should be spelled out, and it should be discussed if this is the odd one out. It would also be appreciated if the authors could state whether their bioinformatic analysis is comprehensive (i.e., do only the known or all Burkholderia strains have TSSM with a DUB profile). And why is there a A0A1J5... sequence included in Supp Fig. 3a without any context?
• Some minor polishing in the methods would increase consistency (cloning is only mentioned for pOPIN-K, but TSSM is also expressed from pOPIN-S; mutants are only mentioned for the 292-490 construct, but Fig. 2d shows one in the 193-490 construct; Hampton Additive Screens I-III are likely an internal name and not used by Hampton itself; "different TSSM concentrations (as indicated in the figure legends" are mentioned in the methods, but e.g. in the caption to Fig. 1 no concentration is given).
• Likewise, Table 1 needs polishing as commas and points are used interchangeably.
• In Fig. 2c, it looks like the catalytic His is built such that there is no hydrogen bonding between Cys and Asp - is there a particular reason for this? If not, the side chain should be flipped so that the nitrogens are positioned for ideal hydrogen bonding.
• In Fig. 3, dotted lines are introduced as "hydrophobic interactions" as per the captions, but some are clearly hydrogen bonds (e.g., from the amide backbone), and for some others one does not see as they emerge from a cartoon.
• In Fig. 4, context should be given to "3VYP" and why it is used here.

Referees cross-commenting

Reviewer comments appear to be fair, balanced and complementary.

Re Reviewer 2's comment on the pre-print: It includes a structure of TSSM bound to ubiquitin (but not of the apo protein). I am not sure if it is appropriate to follow up on the esterase activity. Firstly, there are no tools for it commercially available or readily made in vitro, and secondly it would appear a bit "copycat"-like. Especially since the molecular determinants of what makes a DUB a good esterase are still elusive. A narrower focus of this manuscript, but done very well (also according to what reviewer 3 suggested), might be a more fitting option.

Significance

The findings are novel and of high relevance to the broad ubiquitin and bacterial pathogen communities as the study addresses an enigmatic USP-type deubiquitinase which, as the authors reveal, recognizes Ubiquitin in an entirely different way than its eukaryotic counterparts. This is basic research of pronounced conceptual and mechanistic advance, as it demonstrates that the USP domain can be much more diversified than previously assumed. The structural analysis is very thorough, the data are scholarly presented, and interactions/mechanisms carefully validated by mutations.

The strongest point is clearly the structural analysis of Ubiquitin recognition by this extremely truncated USP fold, and the introduction of the little finger motif. The manuscript does not provide cellular validation of the findings, which is fine to this reviewer for the DUB catalysis part. For the part of the N-terminal domain, the manuscript would benefit from a cellular validation or some localisation studies, however, this is beyond what is established in the authors' lab, and therefore has not been asked. This in turn limits the study to a very thorough in-vitro analysis of this DUB for TSSMs with DUB activity, using conventional substrates like polyUb chains and fluorogenic substrates, and providing convincing conclusions.

My expertise lies in DUBs, biochemistry, and structural biology, and I this believe to have sufficient expertise to evaluate the majority of the findings except the bioinformatic algorithms used which are however not an emphasis in this manuscript.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript Salvador-Garcia et al. examine how several mutations in the Dynein heavy chain (DHC) influence Dynein function in an in vitro reconstituted system and in Drosophila embryos. Most importantly, they identify a novel substitution mutation (S3372C, generated as a by-product of a targeted CRISPR mutagenesis screen) that leads to a novel phenotype specifically in early Drosophila embryos (metaphase arrest) and that only impairs DHC function under load in vitro. Most surprisingly, the metaphase arrest in embryos does not appear to be due to a failure to inactive the spindle-assembly-checkpoint (SAC), a known DHC function. This suggests that DHC has a hitherto unappreciated function in allowing spindles in the Drosophila embryo to progress from metaphase-to-anaphase.

The manuscript is generally well written and conveys the major conclusions clearly and concisely. The data is generally of high quality, and largely supports the main conclusions, although there is one set of relatively straight-forward experiments that I think would be an important addition (see major comment #1, below).

Major Comments

1. The observation that the S3372C mutation causes a mitotic arrest that is not SAC dependent (i.e. it still largely occurs even in a Mad2 mutant background) is very surprising, and is the basis of the authors claim of a new, DHC-dependent, mechanism that allows embryo spindles to progress into anaphase. I think it would be important to assess whether the SAC components are still localising to the kinetochores in these S3372C, Mad2 double mutants (e.g. is Rod still recruited to high-levels in the double mutant?). If the SAC components are still being recruited to the spindle (suggesting that they are still detecting that the spindle is not ready to go into anaphase), is it worth considering that Mad2 may not be essential for SAC function in these embryos? I say this because I find it hard to imagine how any, presumably mechanical, failure at the kinetochore that leads to the improper metaphase/anaphase transition in the S3372C mutants, would signal to the rest of the spindle to not transition to anaphase if the SAC is truly inactivated. Do the authors think these embryos have a completely unrelated surveillance system that detects the S3372C-dependent error (whatever that is) and arrests the spindles specifically in embryos? Or is the error itself sufficient to cause a spindle-wide arrest, which seems improbable?
2. I was surprised the authors made no attempt to quantify the level of over-accumulation of Dlic (Figure 6) or Rod (Figure 7) (and the lack of over-accumulation in other regions of the spindle). The images are convincing, so I don't doubt that this is the case, but I think some sort of quantification would be useful and I don't think it would be hard to come up with a way to do this (even just drawing a ROI around the approximate areas of interest). It would also be interesting to know whether other proteins like Spc25 (Figure 6) and Cdc20 (Figure S6) are recruited to normal levels at kinetochores.

Minor Comments

1. In the Discussion the authors state: "Our discovery of a missense mutation that strongly affects nuclear divisions in the embryo without disrupting other dynein functions offers a unique tool to study the mitotic roles of the motor". This should be reworded, as it suggests that the mutation effects all mitotic functions of DHC, which is clearly not the case (and also applies only to the embryo).
2. I think it worth more explicitly stating that there is no evidence that the defects the S3372C mutation lead to in the in vitro reconstituted system are the cause of the in vivo defects observed in the embryo. The authors are careful not to directly claim this, and I agree with their assertion that this is the most "parsimonious explanation" for their data, but I'm sure they would agree that this is far from proven, and it might be worth emphasising this point a little more.

Significance

This is a well conducted study that significantly extends the author's previous work on how mutations in DHC (initially indentified in human patients) effect DHC function (Hoang et al., PNAS, 2017). The paper reports the striking central finding that the S3372C mutation produces a very unusual mitotic arrest phenotype specifically in Drosophila embryos, and the authors link this to the also striking finding that this mutation only disrupts DHC function in vitro when DHC is working under load. As mentioned above, this link is not proven here, but this is a solid working hypothesis that is potentially of significant interest to those working on molecular motors and their role in fundamental cell biology and human disease.

I am a cell biologist with expertise in the cytoskeleton, particularly during early Drosophila embryogenesis.

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Referee #2

Evidence, reproducibility and clarity

In the manuscript by Salvador-Garcia et al., the authors assess the physiological consequences of dynein mutations in flies and in vitro. In addition to characterizing the manner by which disease causing mutations affect fly development and some aspects of their cell physiology, the authors focus on sporadic mutations that arose during the course of generating their mutant fly lines. Of particular interest was a mutation in the dynein MTBD: S3722C. This mutation caused very interesting phenotypes in flies (e.g., infertility in females likely due to mitotic arrest) as well as in reconstituted motility assays (e.g., reduced stall force). The authors posit that the mitotic arrest phenotype is a consequence of a dynein's role in initiating anaphase onset, and that this role is distinct from its well established role in silencing the spindle assembly checkpoint.

The paper is very well written, and the data are of high quality. Most of the claims - with one major exception (described below) - are well supported by the data. I have a few comments that might help to strengthen the conclusions.

Major comment:

1. In brief, I'm not convinced the mitotic arrest phenotype is not a consequence of impaired SAC silencing by the mutant dynein. The main tool the authors use to support their claim is a Mad2 mutant. They use this to determine if preventing SAC function (with the mutant Mad2) can override the ability of S3722C cells to progress into anaphase. The Mad2 mutant does in fact increase the proportion of cells exiting mitosis (from 0.8 to 14% of cells); however, the low number (14%) suggests that an inability to silence the SAC is not the reason the cells are not entering anaphase (i.e., it is SAC silencing-independent). My question is how penetrant the Mad2 mutant is? For example, how many cells with this Mad2 mutant would exit mitosis if the authors perturbed mitosis some other way (e.g., treatment with high concentrations of nocodazole)? If the number is still low (~14%), then this might be why the mutant can't rescue the mitotic exit phenotype for S3722C cells, and would challenge the following statements: "...it suggests that this can make, at best, a minor contribution to the mitotic arrest phenotype"; and "Remarkably, the MTBD mutation does not appear to block anaphase progression in embryos by preventing the well-characterized role of kinetochore-associated dynein in silencing the SAC, as the defect persists when the checkpoint is inactivated by mutation of Mad2. Collectively, these observations indicate that kinetochore dynein has a novel role in licensing the transition from metaphase to anaphase." Although previous studies might have assessed the penetrance of this mutant in other cell types, given the cell specificity of the mitotic arrest phenotype for S3722C (in embryonic cells, but not L3 neuroblasts), it will be important to provide such additional evidence in embryonic cells (e.g., nocodazole treatment of embryonic cells) to support these statements, especially in light of the bold conclusions and hypotheses they are making (e.g., "For example, the apparent variability in tension between sister kinetochores in S3372C embryos, which could reflect abnormal force generation by the mutant motor complex, might prevent APC/C activation through the complex series of signaling events that respond to chromosome biorientation."). Although it would be fascinating if the authors are correct that dynein provides another role in licensing anaphase onset, the well-established role for dynein in checkpoint silencing currently seems like the most parsimonious explanation.

Minor comments:

1. The S3722C mutant appears to accumulate to higher-than-normal levels at KTs and to some extent along the spindle MTs. In addition to the representative images, it would be helpful to see a quantitation of this phenomenon for WT, S3722C, and S3722C/+ along with statistics.
2. Although the mean inter-KT distance was unchanged between WT and S3722C cells, the authors note that the deviation from the mean was higher. Could this simply be a consequence of more highly dynamic oscillations of KT pairs (similar to that seen with Hec1-S69D in DeLuca et al., JCB 2018)? More dynamic oscillations could potentially lead to more variable distances between KT pairs.
3. It is interesting that the S3722C/Mad2-mutant cells are enriched in telophase (Fig. 7G). Does this not suggest another arrest point for these cells?
4. The authors state: "Immunostaining revealed that whereas α1-tubulin was present throughout the spindle apparatus, α4-tubulin was enriched at the spindle poles (Figure S7A)." Although I agree the a4-tubulin appears somewhat enriched at the poles with respect to a1-tubulin, a quantitation (with statistics) would be needed to support this claim. That being said, I agree the isotype is unlikely to account for the S3722C phenotype.
5. Trapping data show reduced stall force, yet increased stall time at low resistive forces for the mutant. This finding could potentially account for the reduced velocity of GFP-Rod noted in cells; however, I wonder if the authors noted altered velocity for dynein-driven bead movement under load in their trapping assays? This information would be useful to include in their manuscript.
6. Is there a defocused spindle pole phenotype in the mutant cells? The cells in Video 1 and Fig. S6c appear to show as much, although other cells do not.
7. The authors state: "This may reflect the relatively short length of Drosophila neurons making them less sensitive to partially impaired cargo transport." Could the extent of the phenotypes also be related to the lifespan of the flies? Do any of the diseases caused by these mutations have late-onset in patients? I wonder if a subtle defect in dynein behavior might not manifest for numerous years due to only minor changes in motility?

Referees cross-commenting

I wanted to reiterate my skepticism regarding the possibility that their data strongly support a SAC-independent role for dynein in the metaphase-to-anaphase transition (it seems Reviewer #3 might agree with me). I don't think it's impossible, but I'm not convinced they've made a very strong case for this model, which is noted in the title. The fact that proteins are accumulating at aligned kinetochores in the mutant cells (e.g., Rod and DLIC) in fact are consistent with a SAC silencing defect. Along these lines, I think reviewer #1's point regarding RZZ is a good one (that the mutant dynein is incapable of evicting RZZ specifically from aligned KTs), and should be tested prior to publication.

My primary concern is that their conclusion is based entirely on the fact that the Mad2 mutant does not fully restore mitotic exit to the dynein mutant cells. Given the cell-specificity of their dynein phenotype (in embryonic cells, but not L3 neuroblasts), I think testing the penetrance of their Mad2 mutant in the embryonic cells would need to be assessed. In my review I suggested nocadazole, when I realized I meant to say reversine (oops!).

Significance

The manuscript by Salvador-Garcia et al. is a very interesting study dissecting the physiological consequences of dynein mutations in flies and in vitro. This study will be of high interest to those in the dynein/molecular motor field, as well as those that study mitosis and kinetochore function. One of the most interesting findings in the study is the identification of a mutation in dynein that specifically impacts its motility in conditions of high load. This mutant provides a novel tool to dissect load-dependent transport for dynein in other systems. Moreover, the study suggests a novel role for dynein in promoting anaphase onset; if the authors can provide additional support for this claim, the impact of this study would be greater.

Field of expertise: molecular motors, kinetochore function

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Referee #1

Evidence, reproducibility and clarity

The authors start out by examining the cellular and organismal effects of 6 human disease-linked mutations, as well as the mouse legs-at-odd-angles (Loa) mutation, after introducing the mutations into the D. melanogaster dynein heavy chain (Dhc) by genome editing. This reveals an overall correlation between the severity of the effect on dynein motor activity in vitro (determined in a previous study) and the penetrance of the corresponding mutant phenotype in the fly, with a couple of interesting exceptions that illustrate the value of performing structure-function analysis of dynein in animal models. The authors then focus on an additional missense mutation in the Dhc microtubule binding domain, fortuitously generated by imprecise editing, that results in a striking phenotype. The S3372C mutation supports normal development, including normal axonal transport of mitochondria and asymmetric mitosis of larval neuroblasts, but female flies are infertile. Through elegant genetics, ectopic disulfide bond formation with a nearby residue is ruled out as the cause of the maternal effect. S3372C results in metaphase arrest of early embryonic divisions, characterized by over-accumulation of dynein light intermediate chain (Dlic) and the dynein recruitment factor Rod at kinetochores, as well as by reduced poleward streaming of Rod along spindle microtubules. Surprisingly, the S3372C-induced metaphase arrest cannot by bypassed by inhibiting the spindle assembly checkpoint, implying that dynein promotes the metaphase-to-anaphase transition not solely through its known function in spindle assembly checkpoint silencing. In vitro motility and optical trapping experiments show that the mutant motor performs normally in a load-free regime but exhibits reduced peak force production and excessive pausing under load. Furthermore, molecular dynamics simulations reveal how the mutation affects dynein's interaction with microtubules, including a change in the positioning of the stalk. The authors conclude that the S3372C mutation specifically perturbs high-load functions of dynein, explaining the selective phenotype observed in vivo.

The experiments are technically on a very high level, the results are presented in a clear manner, and the conclusions are fully supported by the data.

Minor suggestions (optional):

• In the first part of the paper, where Dhc mutations associated with neurological disease are examined, the H3808P and F579/Loa mutations are shown to cause mis-accumulation of synaptic vesicles in axons. The authors may want to perform this assay for the K129I, R1557Q, and K3226T mutations, as this would strengthen the comparative analysis of in vitro versus in vivo effects, summarized in Figure 1C. For example, K129I has a more severe effect in vitro than the Loa mutation, but the Loa mutation has a more pronounced phenotype on the organismal level. Would this also be the case in a cell-based assay?
• The observation that the metaphase arrest of S3372C mutant embryos cannot be alleviated by the checkpoint-defective Mad2 mutant is very intriguing, as is the observation that Dlic and the RZZ subunit Rod over-accumulate at/near kinetochores. As discussed by the authors, one possibility is that the arrest is a consequence of dynein's failure to disassemble the corona by stripping, but, surprisingly, in a manner unrelated to dynein's role in SAC silencing. In this regard, it is interesting to note that fly RZZ mutants do not undergo metaphase arrest in the early embryo (Williams and Goldberg, 1994; Défachelles et al., 2015), whereas knockdown of Spindly, which functions in dynein recruitment downstream of RZZ, does lead to arrest (see Figure 2 in Clemente et al., 2018; PMID 29615558). Taken together, this raises the possibility that it is the failure to remove RZZ (and other associated corona components) from kinetochores that inhibits anaphase onset in S3372C embryos. It would therefore be interesting to test whether the metaphase arrest in S3372C embryos is alleviated in RZZ mutants.

Referees cross-commenting

The Mad2 mutant the authors use is a P-element insertion that was described by Buffin et al 2007 as a null mutant with regards to SAC signaling (it also does not produce any detectable protein by Western blot; Figure 1b). Nevertheless, since the analysis in Buffin et al was restricted to larval brains, I agree with reviewer #2 that it remains to be formally demonstrated that this Mad2 mutant fully abolishes the SAC in the early embryo. Unfortunately, as far as I am aware, reversine does not work well in Drosophila. An alternative would be to combine Dhc(S3372C) with the other Mad2 mutant used by Buffin et al, which (besides not producing detectable protein) lacks the Mad1 binding domain and can therefore be expected to be a definitive checkpoint null in all tissues.

Significance

The cytoplasmic dynein 1 motor complex participates in a multitude of cellular processes that require microtubule minus-end-directed motility. Whereas in vitro reconstitution efforts have led to a detailed understanding of the motor's motile properties, the essential requirement of dynein for development has made it challenging to dissect how the motor contributes to specific aspects of intracellular organization and cell division in vivo. The need for a mechanistic understanding of how dynein motility is used for diverse functions in vivo is underscored by missense mutations in the motor subunit that cause human neurological disease. In this interesting and insightful study, Salvador-Garcia and colleagues characterize several missense mutations in dynein heavy chain (Dhc) using biochemical assays and genetic approaches is the fly, which reveals the distinct effects of disease-causing mutations in vivo and uncovers an unanticipated novel function of dynein in regulating mitotic progession.

This beautifully executed study has important implications for dynein's role in mitosis, in particular its role at the kinetochore, and is of broad interest to cell biologists studying the cytoskeleton, as it demonstrates that examining motor mutants with altered mechanical properties in vivo can reveal specific motor functions.

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Reply to the reviewers

Response to Reviewers

We are grateful to the Reviewers for their insightful thoughts and suggestions for improving the manuscript for publication. We have addressed all Reviewers’ comments, and detailed responses have been provided below (in blue font). We have uploaded a revised manuscript version, and have made a few small improvements to the text to improve readability. Line and figures numbers refer to the revised version of the manuscript.

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

In this study, Wenner et al. used various in vitro methods, including transposon mutagenesis, screening of known regulatory proteins and isolation of spontaneous mutants to discover 11 mutations in genes that promote bacterial growth under succinate-mediated inhibition. Through additional experiments, the manuscript provides evidence for factors that underlie several layers of succinate regulation. These layers include sRNAs, OxyRS, succinate transport antibiotics and rRNA. The study then characterized the molecular mechanisms regulating succinate utilization by these mutations, revealing a RpoS-independent mechanism for succinate uptake via the dctA transporter and mechanisms for RpoS regulation.

Overall, the manuscript is very unfocused and uneven in the level of details of each of these factors and could be much more compelling if more focus was given to several factors and providing more mechanistic insight of these factors.

We thank Reviewer #1 for the constructive criticism and suggestions. We do recognize the limitations of our study, clearly more work is required to unravel the complex phenomenon of the inhibition of succinate utilisation by Salmonella. We welcome Reviewer #1’s suggestions to shorten the manuscript, which has allowed us to focus the paper on our key findings.

Major comments

1. The authors discuss virulence-mediated succinate but disregard some important features of succinate utilization, only referring to dctA and disregarding the overlap with other C4-dicaroxy transporters (Spiga, wolf, PMID). Furthermore, the study found that a mutation in the IscR binding site on the DctA promoter region reversed the effects of succinate-dependent growth inhibition generated under aerobic conditions but other succinate transporters are expressed under different physiological conditions (Janausch et al. 2002, Spiga et al. 2017). Does the IscR binding site motif can be found in promoters of other succinate transporters? Analysis of IscR in aerobic/ anaerobic conditions can be useful. Do mutations in IcsR lead to increased expression of other succinate transporters in aerobic or anaerobic conditions?

The Reviewer’s question of the regulatory role of IscR on anaerobic C4-dicarboxylate transporters is particularly relevant in the context of the role of succinate catabolism in pathogenesis and could be studied in a follow-up investigation. However, further analysis of the influence of mutations that modulate the expression or activity of IscR are beyond the scope of our study. Here, we have focused on succinate utilisation under in vitro, aerobic conditions: under these conditions, growth upon succinate is robustly repressed, allowing the selection of Succ+ mutants. To emphasise that our study was done under aerobic conditions, we have rephrased the Introduction (line 93).

Transposon screen - There is no comprehensive description of the results and it is not clear why mutations found in the evolution experiments or regulatory proteins that were shown to allow bacteria growth under succinate treatment were not detected in the transposon screening?

Different selection protocols were used to isolate the Succ+ mutants and the experimental approaches are detailed in the Methods and in the strain list for each mutant (Supplementary_Resource_Table S1). Selection was performed in liquid M9+Succ for Tn5 mutagenesis (in the rpoS2X background), or in solid and liquid M9+Succ media for the spontaneous mutants (the mutations are all listed and detailed in Table 1).

Therefore, the different selection conditions and the presence of an extra rpoS copy may have favored certain mutants, especially when the pools of Tn5 mutants were grown with succinate together (mutants in competition).

We recognize that our experimental approach had limitations, and that a Tn-seq methodology would have been more comprehensive. However, the robustness of the phenotypes of the mutants (all re-constructed and complemented, when possible) demonstrated that the genes of interest had direct impact upon the control of succinate metabolism with novel implications for the field.

Figure 4: The authors claim: "that the fast growth of the Δhfq and Δpnp strains reflected both the dysregulation of the sRNA-mediated repression of sdh and the activation of rpoS translation". However, they provide no evidence for SDH regulation. The experiment is correlative, the activity of pnp regulating rpoS was done with overexpression without the proper controls. The authors should look at rpoS expression in Δpnp. It does not seem reasonable that transcription of SDH mRNA can explain lack of succinate utilization. What about the SDH protein? is it at all changed? The authors claim "none of the sRNA mutants tested displayed the same fast-growing pattern of the Δhfq mutant" but they action can involve completely different mechanisms, that the authors do not study. This part does not seem to contribute any novel information on Δhfq and Δpnp on Succ+ with the sRNAs seem not to provide any clear mechanism. The authors should consider removing this part or moving to supplementary.

We appreciate this comment, and agree that this section does not provide critical novel insight. However, our findings provide valuable data concerning the role that Hfq, PNPase and sRNAs play in succinate utilisation. Therefore, we have briefly mentioned the role of Hfq, PNPase and sRNAs in the main text (Lines 333-338) and moved the original Figure 4 to the Supplementary (Figure S5), with a supplementary text section (Supplementary Text T1).

If OxyS, an Hfq-binding sRNA, is related to Succ+ in Δhfq, then why all the other sRNAs are relevant? This is not clear. The authors could have focused here on the oxyS instead of other sRNAs. "The same plasmid did not stimulate the growth of the ΔoxyR strain indicating that a functional OxyR is required for growth in M9+Succ (Fig 5D)" - is it because of other targets of OxyR?

The reviewer’s interpretation is correct. To clarify this point, we have rephased the sentence (Lines 274-276) to “The same plasmid did not stimulate the growth of the ∆oxyR strain indicating that other OxyR-dependent genes are required to grow under this condition”

It seems that an RNA-seq analysis in the conditions of succinate growth with OxyRmut vs. WT could hint towards this.

Indeed, it would be very interesting to compare the transcriptomic landscape of the WT and of the oxyRmut mutant and other Succ+ mutants in succinate minimal medium. However, the lack of growth of S. Typhimurium WT in M9+Succ, would make these experiments unlikely to succeed.

"We previously showed that Hfq inactivation boosted succinate utilization (Fig 4A), but in the oxyRmut genetic background the same Hfq inactivation dramatically reduced growth and extended the duration of lag time in M9+Succ (Fig 5 E)"

The reviewer is correct, we had hypothesised that Hfq is necessary to stimulate succinate utilisation by OxyS. Therefore, we have rephrased to: “We previously showed that Hfq inactivation boosted succinate utilisation, but in the oxyRmut genetic background the same Hfq inactivation dramatically reduced growth and extended the duration of lag time in M9+Succ (Fig 4E). Collectively, our findings show that the OxyS sRNA orchestrates the de-inhibition of succinate utilisation in concert with Hfq” (Lines 278-281)

• this seems like an interesting finding, but the authors don't offer any follow-up? Is it related to oxyS activity?

The role of Hfq on succinate utilisation appeared to be dual, we have added a sentence to this effect (Lines 335-338).

Figure 6: "OxyS acts as an indirect repressor of RpoS expression, probably via the titration of Hfq". the yobF::sfgfp activity was significantly lower in the oxyRmut strain (~2-fold repression), confirming that OxyS represses the expression of the yobF cspC operon in Salmonella - can the authors show this directly with oxyS in succinate?

Because Salmonella WT and ∆oxyS strains do not grow in succinate media (M9+Succ), we had to investigate the regulation of yobF-cspC operon with a translational gene fusion in non-selective LB media.

Why use OxyRmut here? This is indirect.

In Figure 5C we first used the oxyRmut Succ+ strain to demonstrate that this mutation leads to the repression of yobF-cspC. In Figure 6F, we used the oxyRmut allele to allow a constitutive expression of oxyS WT or oxySGG : allele oxySGG was introduced into the chromosome and relies on an active OxyR to be transcribed. The direct role of OxyS is demonstrated in Figure 5 E &F.

The authors already show that OxyRmut does not act solely via Oxys...can the authors directly show RpoS and SDH levels by qRT-PCR in ΔcspC? Again - the appropriate control for RpoS overexpression in the WT was not done (Fig. 6G). Furthermore, expression analysis of the sdhCDAB operon over the background of the oxyR mutant will confirm the author suggestion for the mechanism by which the OxyS-driven inhibition of CspC expression impacts upon the catabolism of succinate.

The reviewer’s comments are valid, more work is required to understand how OxyS stimulates succinate utilisation via the repression of cspC. The fact that Salmonella WT does not grow with succinate as a sole carbon source makes such comparisons technically challenging. Yes, the repressive role of CspC remains enigmatic. However, RNA-seq data following growth in LB media have already been provided by others, suggesting that CspEC may repress TCA cycle genes in Salmonella (PMID: 28611217), consistent with the repression of succinate catabolism by CspC.

The fact that the plasmid-borne overexpression of rpoS completely represses growth upon succinate in the ∆rpoS background (Figure S3 B) validated the usage of the prpoS plasmid in other genetic backgrounds, in order to reveal whether the other Succ+ mutations were stimulating succinate utilisation via rpoS repression or not. Because WT Salmonella does not grow in M9+Succ, presenting the growth curve of the WT strain carrying the prpoS plasmid would not be informative here, and would make the figure overly complex.

Figure 7: the authors check growth in M9+succ in the absence of DctA - but the experiment duration should be carried out for longer, as previous experiments with WT (intact dctA in Fig. 2A) and check if in the absence of dctA there are mutations that allow succinate growth.

We agree with the reviewer’s comment and we have performed a new growth curve (over 65 hours) of the ∆dctA strain to clarify that DctA is the only succinate transporter involved in Salmonella growth under our experimental conditions (Figure S8).

It seems that the results here contradict some of the previous - if succinate uptake through dctA is intact then there is no repression of SDH? rpoS? In figure 7E - is this difference only through dctA activity?

The reviewer is raising an important point and it is possible that the de-repression of succinate uptake via DctA could impact upon the expression of the succinate catabolic genes and more work is required to understand this phenomenon. We have discussed this possibility in the main text (Lines 424-432) and in Figure 8C.

It seems that icsR is not repressing dctA expression to WT levels - are there other factors? Can the authors show that dctA repression by IscR is direct?

We agree with the reviewer, we have not shown that IscR represses dctA directly. Electrophoretic mobility shift assays could be performed to prove that IscR interacts with the dctA promoter region, but this would be beyond the scope of the paper. We have clearly stated in the discussion that indirect effects of iscR on dctA expression cannot be ruled out (Lines 419-422).

Figure 9 is very descriptive and does not provide any evidence to support the authors hypothesis. The authors should either provide more substantial evidence connecting ribosomal RNA levels and succinate utilization and similarly Cm concentrations or either remove this part or move it to the supplementary.

We agree that the data do not conclusively support the hypothesis, but we believe that the impact of anti-SD mutation and chloramphenicol on Salmonella carbon metabolism are valuable observations for the community. Therefore, we have moved the data to supplementary Figures S11 and S12 in the revised version, with a supplementary text section (Supplementary Text T2). We also removed this aspect from the model Figure (Figure 8) and only mentioned the phenomenon briefly in the main text, Lines 482-485.

Can any of the mutations characterized in this work be found in the genome of Newport or LT2 strains that can grow with succinate as a sole carbon source? (Fig 1)

Very good questions. Yes, S. Typhimurium strain LT2 has an altered rpoS allele that attenuates virulence of the strain in the murine infection model (PMID: 8975913) and promotes growth with succinate (PMID: 33593945). We have added a sentence and cited the reference at Lines 129-131.

To address the S. Newport question, we performed an analysis of the genome of the S. Newport strain LSS-48, and did not identify any mutations in regulatory or catabolic genes that could explain the faster growth on M9+succinate. However, in comparison with fast-growing enteric bacteria (i.e. E. coli MG1655) or Succ+ S. Typhimurium mutants, S. Newport LSS-48 grows much slower on succinate and has an intermediate growth phenotype. It remains unclear why S. Newport does grow better than other serovars.

Although the author suggested that regulation of succinate uptake is critical for Salmonella colonization and virulence in various metabolic conditions, the study lacks sufficient evidence to support these claims and further research is necessary to establish these statements.

We agree that our findings are not directly linked to Salmonella host colonisation or virulence. However, we do believe that our study will contribute to a better understanding of Salmonella metabolic control, in the context of pathogenesis. To address Reviewer #3’s comment, we have moderated our claims about the likely impact of our findings on the understanding of Salmonella pathogenesis in the Perspective section.

Minor comments

1. Table summarizing the growth curves lag phase of the different mutants might help in the data interpretation.

We appreciate the Reviewer’s suggestion and have prepared a supplementary figure (Figure S4) indicating the average lag time of the Succ+ mutants and of the complemented mutants.

In lines 245-248 the author describes the eleven novel Succ+ mutations however in this gene list only ten gene names are mentioned. DctA is missing from this list.

We appreciate the Reviewer’s comment and we have modified the sentences in the revised manuscript (Line 244).

** Referees cross-commenting**

I agree with both reviewer that there is a large amount of data in the paper, and willing to accept their point that asking for further experiments would exceed the scope of the paper. In that case, the authors should address the mechanistic options in the discussion

Reviewer #1 (Significance (Required)):

In this work, Wenner et al. characterized the molecular mechanisms regulating Salmonella growth inhibition when succinate is the sole carbon source in the culture. This work revealed new layer of regulations for rpoS activation, the sigma factor previously characterized to control this growth inhibition mechanism. In addition, this work revealed novel RpoS-independent mechanisms for succinate utilization and highlighted the crucial role of succinate processing in Salmonella physiology.

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

In the manuscript titled "Salmonella succinate utilisation is inhibited by multiple regulatory systems", Wenner et al., explored how Salmonella regulates the utilization of succinate, an important carbon source for Salmonella gut colonization as well as a molecule that regulates intracellular adaptation in the SCV. As Salmonella exhibits a slow growth rate when succinate is provided as the sole carbon source, the authors explored the underlying genetic regulation by isolating fast-growing mutants (Succ+) using an experimental evolution approach. By combining the screen for mutants lacking key regulatory proteins, an elegantly designed Tn5 transposon mutagenesis, and selection of spontaneous Succ+ mutants, the authored identified a library of mutations that led to the Succ+ phenotype. Using classical bacterial genetics, Wenner et al characterized how Hfq, PNPase and cognate sRNA inhibit succinate utilization. They went on to show, clearly and convincingly, that IscR inhibits growth upon succinate by repressing DctA expression, and succinate utilization can also be repressed by RbsR and FliST via RpoS. Lastly, they provided evidence supporting that anti-Shine-Dalgarno mutations and low concentrations of chloramphenicol can boost succinate utilization. Overall, this paper is well written, and the experiments were rigorously designed and executed. This is a beautiful example of deciphering complex regulatory nodes in the succinate utilization using elegant genetics approaches. Very nicely done!

We thank the Reviewer #2 for the very positive evaluation of our work and the constructive comments.

Minor issues:

1. While rpoS2X strain is an clever way to avoid the selection of Succ+ rpoS mutants, it is unclear why "identified an iraP::Tn5 mutant was an effective validation of the use of the rpoS2X genetic background". IraP stabilizes Rpos, and this mutant could have been selected in the wild-type background (rpoS1X).

The reviewer’s comment is helpful, we have removed this sentence from the revised manuscript.

The description between line 356-357 is confusing as it reads like the author constructed a "oxyRmut oxySGG pPL-OxySGG" strain, while the experiments that followed actually used a " ∆oxyS, yobF::sfgf, pPL-OxySGG" strain.

We have modified these sentences in the revised manuscript (Lines 303-308).

An alternative explanation for the Succi+ phenotype in aSD mutant and bacteria treated with low Cm is the reduced translation fidelity, which leads to selectively degradation of inhibitors of succinate utilization.

We thank Reviewer #2 for the suggestion. This phenomenon is really enigmatic and as previously discussed in Reviewer #1’s section, we have now moved Figure 9 to supplementary data. Further discussion of how the aSD mutations and chloramphenicol can affect Salmonella succinate metabolism would require a lot more experimental data.

** Referees cross-commenting**

Most of the comments from Reviewer 1 are valid but excessive. Most of the experiments presented in this paper were rigorously controlled and executed. While some parts of the paper could be more mechanistic but they could also leave room for future studies. Also, some of the points raised, the 1st major concern, for example, may have exceeded the scope of the paper.

We agree. We have performed a new experiment (Figure S8) to address Reviewer #1’s comments.

Reviewer #2 (Significance (Required)):

Overall, this paper is well written, and the experiments were rigorously designed and executed. This is a beautiful example of deciphering complex regulatory nodes in the succinate utilization using elegant genetics approaches.

We appreciate Reviewer #2’s feedback that the quality of the text and our experiments was viewed so highly.

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

In this work, Wenner and colleagues use experimental evolution to define a range of spontaneous mutations in Salmonella that allow it to overcome its aversion to using succinate as a carbon source in vitro.

This work cites the literature extensively and the scholarship is very very good. I appreciate the effort they put into the manuscript, which made it easy to read. Quite a relief to get a paper in this good of shape compared to most.

We appreciate Reviewer #3’s positive comments on our work and the constructive suggestions.

Shortcomings - although I don't think they are necessary for *this* paper to be published include:

• not defining what could be 'bad' about eating succinate in the wrong place. The fact that succinate import is a problem (dctA is what is being regulated ant its a transporter) suggests one of the following: (1) excess succinate would block the utilization of fumarate by fumarate reductase, (2) succinate is a powerful buffer and, if protonated, would acidify the cytoplasm of Salmonella if it were brought in - note that there is a lot of work on RpoS controlling cytoplasmic acidification, (3) a drop in succinate (because Salmonella eats it) would allow more flux by macrophages or the microbiota in a bad way...maybe the Salmonella 'wants' macrophages to have lots of succinate *because* its pro-inflammatory (and therefore more tetrathionate for its friends...etc), (4) it could be the transporter that also bring in antimicrobial itaconate?...so the succinate phenotype is a red herring and really this is about preventing taconite from getting into the cell?

We thank the reviewer for all these suggestions and for highlighting the reasons why the avoidance of Salmonella utilising succinate is a key point. We have emphasized this key question to conclude our manuscript (Lines 500-501). Whilst all the hypotheses are valid, we believe that further speculation should not be added to the “Perspective” section.

• no proof that any of this is relevant in infection except citing old papers. Again - this work is already VERY expansive and we could propose experiments until the end of time. Next paper should take the dctA and other mutations and put them into mice to see if they fail in either germ free mice (no microbial produced succinate around) or in systemic infections.

The reviewer’s comment is welcomed. As discussed in our response to Reviewer #1, we have scaled back our discussion of the impact of our findings for the understanding of Salmonella pathogenesis*. *

Most of the mutations they find are 'regulatory' and the only proximal effector of succinate utilization seems to be dctA...suggesting that dctA expression is the 'rate limiting' or 'blocked' step that decides whether succinate is being used or not.

We agree that dctA regulation is a central element of the story. As discussed in Reviewer #1 comments, it is not clear how de-repression of dctA leads to the increased catabolism of succinate in the presence of RpoS (particularly because RpoS represses several succinate catabolic genes, PMID: 24810289 and PMID: 25578965). We also discovered other Succ+ mutants that did not affect DctA expression but stimulated growth on succinate as a sole carbon source. Consequently, it is uncertain whether the uptake of succinate is really the limiting factor. We have added sentences about this paradox, Lines 424-432.

The data is extensive and generally well controlled. Where appropriate they either complement mutations or reconstruct them denovo. The findings of the various genes range in novelty but many are new.

** Referees cross-commenting**

I agree that the work was valid and well controlled. The 'story' was a bit disjointed at times primarily because the range of mutations identified were diverse and pleiotropic. Given the large amount of data already in the paper and the nature of the mutations identified I worry about embarking on an endless cycle of new experiments. I think it's at a publishable stopping point.

In response to Reviewer #3 & #1’s comments, we have now improved the flow of the manuscript.

Reviewer #3 (Significance (Required)):

This seemingly mundane phenotype (Salmonella 'choosing' to not use succinate even though it's perfectly capable of doing so) has been known for years but only recently has its potential relevance become more clear in the context of infection and microbiota metabolism.

The authors propose that succinate utilization is to be used at the right time and right place.

I sympathize with the authors that they keep hitting very pleiotropic regulators (RpoS has ten million upstream inputs and outputs. The ribosome? How is that going to be figured out in one or two simple experiments?). My money is on figuring out exactly how dctA is regulated and whether there's differences in the dctA regulation between E. coli and Klebsiella/Salmonella.

So I think the work is extensive and generally well done. I think the paper will be well cited...and I think it's importance will grow over time and it will continue to be relevant years from now. I can't say that about most work in the field.

We agree with Reviewer #3’s assessment that other scientists in the Salmonella field are likely to cite our paper, and to perform experiments that will build on our findings in the future.

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

In this work, Wenner and colleagues use experimental evolution to define a range of spontaneous mutations in Salmonella that allow it to overcome its aversion to using succinate as a carbon source in vitro.

This work cites the literature extensively and the scholarship is very very good. I appreciate the effort they put into the manuscript, which made it easy to read. Quite a relief to get a paper in this good of shape compared to most.

Shortcomings - although I don't think they are necessary for this paper to be published include:

• not defining what could be 'bad' about eating succinate in the wrong place. The fact that succinate import is a problem (dctA is what is being regulated ant its a transporter) suggests one of the following: (1) excess succinate would block the utilization of fumarate by fumarate reductase, (2) succinate is a powerful buffer and, if protonated, would acidify the cytoplasm of Salmonella if it were brought in - note that there is a lot of work on RpoS controlling cytoplasmic acidification, (3) a drop in succinate (because Salmonella eats it) would allow more flux by macrophages or the microbiota in a bad way...maybe the Salmonella 'wants' macrophages to have lots of succinate because its pro-inflammatory (and therefore more tetrathionate for its friends...etc), (4) it could be the transporter that also bring in antimicrobial itaconate?...so the succinate phenotype is a red herring and really this is about preventing taconite from getting into the cell?
• no proof that any of this is relevant in infection except citing old papers. Again - this work is already VERY expansive and we could propose experiments until the end of time. Next paper should take the dctA and other mutations and put them into mice to see if they fail in either germ free mice (no microbial produced succinate around) or in systemic infections.

Most of the mutations they find are 'regulatory' and the only proximal effector of succinate utilization seems to be dctA...suggesting that dctA expression is the 'rate limiting' or 'blocked' step that decides whether succinate is being used or not.

The data is extensive and generally well controlled. Where appropriate they either complement mutations or reconstruct them denovo. The findings of the various genes range in novelty but many are new.

** Referees cross-commenting**

I agree that the work was valid and well controlled. The 'story' was a bit disjointed at times primarily because the range of mutations identified were diverse and pleiotropic. Given the large amount of data already in the paper and the nature of the mutations identified I worry about embarking on an endless cycle of new experiments. I think it's at a publishable stopping point.

Significance

This seemingly mundane phenotype (Salmonella 'choosing' to not use succinate even though it's perfectly capable of doing so) has been known for years but only recently has its potential relevance become more clear in the context of infection and microbiota metabolism.

The authors propose that succinate utilization is to be used at the right time and right place.

I sympathize with the authors that they keep hitting very pleiotropic regulators (RpoS has ten million upstream inputs and outputs. The ribosome? How is that going to be figured out in one or two simple experiments?). My money is on figuring out exactly how dctA is regulated and whether there's differences in the dctA regulation between E. coli and Klebsiella/Salmonell.

So I think the work is extensive and generally well done. I think the paper will be well cited...and I think it's importance will grow over time and it will continue to be relevant years from now. I can't say that about most work in the field.

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

In the manuscript titled "Salmonella succinate utilisation is inhibited by multiple regulatory systems", Wenner et al., explored how Salmonella regulates the utilization of succinate, an important carbon source for Salmonella gut colonization as well as a molecule that regulates intracellular adaptation in the SCV. As Salmonella exhibits a slow growth rate when succinate is provided as the sole carbon source, the authors explored the underlying genetic regulation by isolating fast-growing mutants (Succ+) using an experimental evolution approach. By combining the screen for mutants lacking key regulatory proteins, an elegantly designed Tn5 transposon mutagenesis, and selection of spontaneous Succ+ mutants, the authored identified a library of mutations that led to the Succ+ phenotype. Using classical bacterial genetics, Wenner et al characterized how Hfq, PNPase and cognate sRNA inhibit succinate utilization. They went on to show, clearly and convincingly, that IscR inhibits growth upon succinate by repressing DctA expression, and succinate utilization can also be repressed by RbsR and FliST via RpoS. Lastly, they provided evidence supporting that anti-Shine-Dalgarno mutations and low concentrations of chloramphenicol can boost succinate utilization. Overall, this paper is well written, and the experiments were rigorously designed and executed. This is a beautiful example of deciphering complex regulatory nodes in the succinate utilization using elegant genetics approaches. Very nicely done!

Minor issues:

1. While rpoS2X strain is an clever way to avoid the selection of Succ+ rpoS mutants, it is unclear why "identified an iraP::Tn5 mutant was an effective validation of the use of the rpoS2X genetic background". IraP stabilizes Rpos, and this mutant could have been selected in the wild-type background (rpoS1X).
2. The description between line 356-357 is confusing as it reads like the author constructed a "oxyRmut oxySGG pPL-OxySGG" strain, while the experiments that followed actually used a " ∆oxyS, yobF::sfgf, pPL-OxySGG" strain.
3. An alternative explanation for the Succi+ phenotype in aSD mutant and bacteria treated with low Cm is the reduced translation fidelity, which leads to selectively degradation of inhibitors of succinate utilization.

** Referees cross-commenting**

Most of the comments from Reviewer 1 are valid but excessive. Most of the experiments presented in this paper were rigorously controlled and executed. While some parts of the paper could be more mechanistic but they could also leave room for future studies. Also, some of the points raised, the 1st major concern, for example, may have exceeded the scope of the paper.

Significance

Overall, this paper is well written, and the experiments were rigorously designed and executed. This is a beautiful example of deciphering complex regulatory nodes in the succinate utilization using elegant genetics approaches.

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 study, Wenner et al. used various in vitro methods, including transposon mutagenesis, screening of known regulatory proteins and isolation of spontaneous mutants to discover 11 mutations in genes that promote bacterial growth under succinate-mediated inhibition. Through additional experiments, the manuscript provides evidence for factors that underlie several layers of succinate regulation. These layers include sRNAs, OxyRS, succinate transport antibiotics and rRNA. The study then characterized the molecular mechanisms regulating succinate utilization by these mutations, revealing a RpoS-independent mechanism for succinate uptake via the dctA transporter and mechanisms for RpoS regulation.

Overall, the manuscript is very unfocused and uneven in the level of details of each of these factors and could be much more compelling if more focus was given to several factors and providing more mechanistic insight of these factors.

Major comments

1. The authors discuss virulence-mediated succinate but disregard some important features of succinate utilization, only referring to dctA and disregarding the overlap with other C4-dicaroxy transporters (Spiga, wolf, PMID). Furthermore, the study found that a mutation in the IscR binding site on the DctA promoter region reversed the effects of succinate-dependent growth inhibition generated under aerobic conditions but other succinate transporters are expressed under different physiological conditions (Janausch et al. 2002, Spiga et al. 2017). Does the IscR binding site motif can be found in promoters of other succinate transporters? Analysis of IscR in aerobic/ anaerobic conditions can be useful. Do mutations in IcsR lead to increased expression of other succinate transporters in aerobic or anaerobic conditions?
2. Transposon screen - There is no comprehensive description of the results and it is not clear why mutations found in the evolution experiments or regulatory proteins that were shown to allow bacteria growth under succinate treatment were not detected in the transposon screening?
3. Figure 4: The authors claim: "that the fast growth of the Δhfq and Δpnp strains reflected both the dysregulation of the sRNA-mediated repression of sdh and the activation of rpoS translation". However, they provide no evidence for SDH regulation. The experiment is correlative, the activity of pnp regulating rpoS was done with overexpression without the proper controls. The authors should look at rpoS expression in pnp. It does not seem reasonable that transcription of SDH mRNA can explain lack of succinate utilization. What about the SDH protein? is it at all changed? The authors claim "none of the sRNA mutants tested displayed the same fast-growing pattern of the Δhfq mutant" but they action can involve completely different mechanisms, that the authors do not study. This part does not seem to contribute any novel information on Δhfq and Δpnp on Succ+ with the sRNAs seem not to provide any clear mechanism. The authors should consider removing this part or moving to supplementary.
4. If OxyS, an Hfq-binding sRNA, is related to Succ+ in Δhfq, then why all the other sRNAs are relevant? This is not clear. The authors could have focused here on the oxyS instead of other sRNAs. "The same plasmid did not stimulate the growth of the ΔoxyR strain indicating that a functional OxyR is required for growth in M9+Succ (Fig 5D)" - is it because of other targets of OxyR? It seems that an RNA-seq analysis in the conditions of succinate growth with OxyRmut vs. WT could hint towards this. "We previously showed that Hfq inactivation boosted succinate utilization (Fig 4A), but in the oxyRmut genetic background the same Hfq inactivation dramatically reduced growth and extended the duration of lag time in M9+Succ (Fig 5 E)" - this seems like an interesting finding, but the authors don't offer any follow-up? Is it related to oxyS activity?
5. Figure 6: "OxyS acts as an indirect repressor of RpoS expression, probably via the titration of Hfq". the yobF::sfgfp activity was significantly lower in the oxyRmut strain (~2-fold repression), confirming that OxyS represses the expression of the yobF cspC operon in Salmonella - can the authors show this directly with oxyS in succinate? Why use OxyRmut here? This is indirect. The authors already show that OxyRmut does not act solely via Oxys...can the authors directly show RpoS and SDH levels by qRT-PCR in ΔcspC? Again - the appropriate control for RpoS overexpression in the WT was not done (Fig. 6G). Furthermore, expression analysis of the sdhCDAB operon over the background of the oxyR mutant will confirm the author suggestion for the mechanism by which the OxyS-driven inhibition of CspC expression impacts upon the catabolism of succinate
6. Figure 7: the authors check growth in M9+succ in the absence of DctA - but the experiment duration should be carried out for longer, as previous experiments with WT (intact dctA in Fig. 2A) and check if in the absence of dctA there are mutations that allow succinate growth. It seems that the results here contradict some of the previous - if succinate uptake through dctA is intact then there is no repression of SDH? rpoS? In figure 7E - is this difference only through dctA activity? It seems that icsR is not repressing dctA expression to WT levels - are there other factors? Can the authors show that dctA repression by IscR is direct?
7. Figure 9 is very descriptive and does not provide any evidence to support the authors hypothesis. The authors should either provide more substantial evidence connecting ribosomal RNA levels and succinate utilization and similarly Cm concentrations or either remove this part or move it to the supplementary.
8. Can any of the mutations characterized in this work be found in the genome of Newport or LT2 strains that can grow with succinate as a sole carbon source? (Fig 1)
9. Although the author suggested that regulation of succinate uptake is critical for Salmonella colonization and virulence in various metabolic conditions, the study lacks sufficient evidence to support these claims and further research is necessary to establish these statements.

Minor comments

1. Table summarizing the growth curves lag phase of the different mutants might help in the data interpretation.
2. In lines 245-248 the author describes the eleven novel Succ+ mutations however in this gene list only ten gene names are mentioned. DctA is missing from this list.

** Referees cross-commenting**

I agree with both reviewer that there is a large amount of data in the paper, and willing to accept their point that asking for further experiments would exceed the scope of the paper. In that case, the authors should address the mechanistic options in the discussion

Significance

In this work, Wenner et al. characterized the molecular mechanisms regulating Salmonella growth inhibition when succinate is the sole carbon source in the culture. This work revealed new layer of regulations for rpoS activation, the sigma factor previously characterized to control this growth inhibition mechanism. In addition, this work revealed novel RpoS-independent mechanisms for succinate utilization and highlighted the crucial role of succinate processing in Salmonella physiology.

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

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Reply to the reviewers

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

The manuscript investigates the role of PAT1 gene family in Arabidopsis thaliana. Though the PAT1 protein has been previously investigated and displayed immune-related and developmental phenotypes, the other two members of the family, PATH1 and PATH2, have not been well studied. The authors set out to understand the role of these proteins in relation to the role of PAT1. They thus generated single, double, and triple mutants of the possible combinations of PAT1 genes and examined their phenotypes. As the study focused on the developmental effects of PAT1, the mutants were generated on the background of the summ2 mutant to avoid phenotypes related to immune response. The authors notice a developmental difference between the pat1 mutant combinations, suggesting that PAT1 acts differently than PATH1 and PATH2 and that the PATH proteins serve a redundant function. They also performed RNA-seq analysis to identify differentially-regulated genes in the mutant combinations. The study is interesting and well-executed, yet I believe some questions should still be addressed:

__Our response: __We thank the reviewer for acknowledging the significance of our findings. Please see our detailed answers to the reviewer’s suggestions in the following.

1. The research mainly focuses on the developmental phenotype of pat mutants but also tests the interaction of PATH proteins with RNA decapping enzymes to check their function and localization during different treatments. I found it a bit confusing since Figure 1 also shows the developmental phenotype of the mutants. I think editing the order of the figures would make the overall story more coherent.

__Our response: __We agree with the reviewer thus we moved old Fig 1C to new Fig 3A, we believe the new figure orders make the overall story more coherent.

My main concern is the correlation between the developmental phenotype of the mutants and the gene expression. Leaf samples for RNA extraction were taken when the plants were 6 weeks old, and the developmental phenotype is very evident. It is thus not possible to tell whether the differences in gene expression are a cause or effect of the developmental phenotype. I think performing qPCR of selected candidates at earlier developmental times might help solve this issue, as well as the characterization of younger plants for the developmental phenotypes (such as leaf number).

__Our response: __We followed the reviewer’s suggestions and performed qRT-PCR on IAA19, IAA29, SAUR23 and PIL2 in pats mutants under different developmental stages (Line 162, 169; Fig S4), we also characterized leaf number of pats mutants from younger stages (Line 109; new Fig 3C).

Overall, the manuscript is missing data regarding replicate numbers in the IP and confocal microscopy experiments.

__Our response: __We thank the reviewer for pointing this it out, the replicate numbers are provided now in our new figure legends.

Minor comments:

1. Figure 1C - the authors should add a picture of Col0 plants as well as the mutants.

Our response: To be reader friendly, the picture of Col-0 plant is added in Fig S1A. For the reviewer’s information, plant pictures in FigS1A and old Fig1C (new Fig 3A) were taken at the same time. 2.

Figure 3 - Calculating the leaf-to-petiole ratio in the different mutants would be good.

Our response: We now calculate PBR (petiole blade ratio) of all pats mutants in Fig3F (Line 121).

Figure 4 - the details in the figure are very unclear, especially in the PCA. It would be good to display the data in 2D for PC1 and PC3 and change the colors a bit.

Our response: We agree with the reviewer; thus, we remade the PCA plot from RNA-seq reads data in a 2D style and also changed the colors for each mutant (Fig 4A). We need to point out that the PCs number also changed because the old PCA plot were made by mistake from expression data.

Reviewer #1 (Significance (Required)): Both PATH proteins have been less investigated than PAT1, and in that sense, the work is novel. However, it seems that most of the phenotype is attributed to PAT1 rather than the other family members, limiting the interest to the broad plant science community.

Our response: We appreciate the reviewer think our work is novel. We agree that PAT1 plays the main role during plant development (old Line 171), however the pat triple mutant exhibit the most severe dwarfism as well as the most mis-regulated genes compared to any single or double mutants, indicating all 3 PATs are essential for development.

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

Zuo et al., characterize the role of three cytoplasmic mRNA-decay activator proteins PAT1, PATH1 and PATH2 in the context of plant development and leaf morphology in Arabidopsis thaliana and Nicotiana benthamiana. The authors show that the triple pat mutant displays the most severe dwarfism of all combinatorial mutants. Through treatment with different stimulants the authors found that only IAA treatment induces the three homologues to form condensates (possibly PBs), while PAT1 forms condensates upon every tested stimulus. An extensive RNA seq experiment revealed miss-regulation of several hundred genes in the higher order mutants, several of which were involved in auxin responsive and leaf morphology determinant genes.

__Our response: __We thank the reviewer for the peer review. Please see our detailed answers to the reviewer’s suggestions in the following.

Major points: 1.Title is not meaningful as is and, in my opinion, does not reflect the main findings in the manuscript.

Our response: We now changed our title into “PAT mRNA decapping factors are required for proper development in Arabidopsis”.

The results section could benefit from improved flow between the paragraphs and more reasoning for the next steps taken to help readers understand the aims of the authors.

Our response: We followed the reviewer’s suggestion and modified the wording in our result part(Line 79,81,94,146-151).

L46: "So far little is known about the functions of these three PATs in plant development.", The authors themselves have studied these proteins in the context of seed germination and ABA control, as well as apical hook formation and auxin responses. Should at least be mentioned and the results discussed in this context.

Our response: We thank the reviewer for noticing our other work and we now included this information in the new introduction and discussion part (Line56&237).

What are the expression levels and patterns of PATH1 and PATH2 compared to PAT1? Is anything known about spatial or temporal regulation of these proteins?

Our response: All three PATs are expressed in roots, stems, leaves, flowers, siliques, and seeds during the whole developmental stages, PAT1 has higher expression level in leaves but lower expression levels in petals. (Klepikova et al., 2016;

https://www.arabidopsis.org/servlets/TairObject?id=138009&type=locus for PAT1; https://www.arabidopsis.org/servlets/TairObject?id=38646&type=locus for PATH1 and https://www.arabidopsis.org/servlets/TairObject?id=128694&type=locus for PATH2).

Figure 1:

o I do not agree that the authors have shown that "PATH1 and PATH2 are also mRNA decapping factors", rather that these proteins can co-localize (and possibly interact) with LSM1. Decapping assays for example with the known PAT1 de-capping targets from their previous work and their extensive mutant collection could be used to test this.

Our response: We thank the reviewer for pointing it out and reminding us about the characterized mRNA decapping target from our previous work, we now include the decapping assays in new Fig5 (Line 197).

From the BiFC experiment (Figure 1B) it looks like PATs are mostly soluble in the cytoplasm (like LSM1) and might be stress-induced components of PBs (like LSM1). Do PATs co-localize with other canonical PB markers that are more prone to condensation, like DCPs or VCS? BiFC could be performed after IAA treatment to confirm that the cytoplasmic foci are indeed LSM1-positive PBs.

Our response: We agree with the reviewer that PATs behave more like LSM1. Given time limit of the project, we unfortunately are not able to check the colocalization of PATs with DCPs or VCS. However, we performed BIFC after IAA treatment, and the cytoplasmic foci are indeed LSM1-positive foci (new Fig1B).

A: please provide uncropped images of all Western blots in supplemental data.

Our response: To be reader friendly, we decide to show the original western blots here (see in the file named "RC-Full-revision"), instead of in supplemental data. However, we will leave the final decision to the editor.

I applaud the authors for establishing this great higher order mutant collection that will be very useful for researchers in the field. However, I am confused about the description of these mutants. If I understood it correctly, these mutants were already used in a previous study by the authors, namely “Zuo, Z., et al., Molecular Plant-Microbe Interactions, 35(2), 125-130.” & Zuo, Z., et al., (2021). FEBS letters, 595(2), 253-263.” In this study the authors refer to a BioRxiv “Zuo, Z., et al., (2019).” As the reference for these Arabidopsis lines. Is this current manuscript a continuation of the BioRxiv? Please elaborate whether these lines have been used and described In previous studies.

Our response: We truly appreciate the reviewer for acknowledging the significance of our work. These pats mutants have been used in the FEBS letters paper (2021), MPMI paper (2022), and the new published paper in Life Science Alliance (2023, but preprinted in BioRxiv 2019 and 2022). However, they have not been fully described or characterized in any of the mentioned published stories. Characterization of these pats mutants were originally only included in preprint 2019 which was cited in FEBS letters paper (2021) and MPMI paper (2022).

L72: Is the strong developmental phenotype of the higher order mutants persistent under long day conditions? Considering the strong developmental phenotypes of the mutants, the flowering transition and morphology could be an interesting trait to study. Why did you choose short day conditions for this study?

Our response: The pat triple mutant also has strong developmental phenotype under long day condition and exhibits early flowering phenotype. We are currently preparing a manuscript regarding mRNA decay and flowering. We did not “choose” short day condition, we just started with short day condition and observed phenotypical differences hence we kept this condition.

L78: This statement is hard to see in Figure 1C and best described for Figure 3A.

Our response: We now change this statement for Fig 3.

L82: Please include a reasoning for testing PATs localization after hormone treatment. Do you have any indication that other PB proteins behave similar to either PAT1 or the PATHs after hormone treatment to substantiate that these foci observed are indeed PBs? What is known about PBs after hormone treatment in planta?

Our response: We were interested in investigating if all three PAT proteins may also form PBs in Arabidopsis thus we tested PATs localization with/without hormone treatment (old Line 84, new line 81). For the reviewer’s interest we also observe LSM1 localization after hormone treatment (Fig 2). PBs have been published to respond to light, cold treatment, PAMPs, ABA, ACC and auxin (Line 39-42).

Figure 2:

o How does the localization of LSM1 change under the same treatments? Does ist behave like PAT1 or the homologues?

Our response: Please see our new Fig 2 for LSM1 localization, and it behaves more like PAT1.

Which part of the root was imaged for this experiment? Is it possible that the observed foci are ARF-condensates as reported by Jing et al., 2022? Do you observe a gradual change in numbers or morphology along the root?

Our response: We use root elongation zone for this experiment. We don’t know if the foci are ARF-condensates, but it’s possible to study in the future. If the reviewer is interested, we are happy to share our materials. We do observe more foci in the cell division zone and less in the mature zone.

How did the authors decide on the concentrations for the stimulant treatments? Have you tried different doses, and could the responses be dose-dependent?

Our response: We did not try different doses; we searched for and applied the commonly used concentrations for different hormones.

A representative image is not sufficient for quantitative responses, like RNA granule condensation. Please provide a quantification of stimulant-induced foci after the different treatments.

Our response: Please see the quantification in our new Fig 2.

L91: Does that mean that most co-precipitated signal comes from the soluble fraction and not PB-localized? Would an RNAse treatment step eliminate the co-precipitation (optional)?

Our response: We believe it means LSM1 and PATs are in the same complex regardless of PB localization.

L92/93: Or alternatively that PAT1 localizes to PBs independent of the stress, while PATHs are signal-specific PB components?

Our response: We think PAT1 aggregates upon broad stimuli/stress, while PATHs respond to specific/limited stimuli, for example, auxin.

Figure 3:

o I wonder if these results fit better in conjunction with Figure 1, either as a combined figure or move before Figure 2.

Our response: We agree with the reviewer thus we moved old Fig 1C into Fig 3.

It is interesting that path2/pat1, while being dwarfed, is less serrated compared to pat1 or path1/pat1. Can you find any indications in your RNAseq set which genes might be involved?

Our response: ANAC016 might be involved, but more research needs to be done to confirm it and this is not the focus of the current project.

Indicate statistical test used to determine p-value

Our response: We now indicate the statistic test in Materials and Methods part (Line 369).

L116/L117: Doesn't the result in Figure 3E indicate that PATH1 and PATH2 are not fully redundant, but that PATs have specific and narrow roles in leaf development? L116 goes against your statement in L150 & L160. What is known about the expression patterns of PAT1, PATH1 and PHATH2?

Our response: We agree and thus modified our statement (Line 137). All three PATs are expressed in roots, stems, leaves, flowers, siliques, and seeds during the whole developmental stages. Please also see our answer to major comment #4.

L123: PC3 only explains 0.55% of the variance, so differences along this axis will be overinflated. In my interpretation the pat1/path2 mutant is clustering apart from the other higher order mutants, which is also reflected in the leaf phenotypes. A 2D PCA would be sufficient to describe most of the variation.

Our response: We agree and thus we changed the PCA plot into a 2D style, please also see our response to reviewer 1 minor comment #3.

Figure 4: o A: The 3D-PCA inflates the differences between higher order mutants along PC3, even though this axis explains only 0.55% of the variance, maybe a 2D-PCA would more intuitively cluster the samples together?

Our response: Please see our new PCA plot in Fig4A.

B: Please explain the scale in the figure legend and which genes were included? Only DEGs between triple mutant and summ2-8 or DEGs that were different in at least one higher order mutant?

Our response: We now explained more details in the figure legends. The genes which were included in Fig4B were DEGs that were differently expressed in at least one of the pat mutants.

C: several comparisons are missing from the upset-plot. Please show the complete plot, also is there a white box laid over the second bar in the upper graph? It would help the reader, if the results section would explain the plots and the comparisons took. Which differences are the authors interested in?

Our response: We covered all the comparisons we wanted to show, but we thank the reviewer for suggesting a more detailed explanation and we therefore explain Fig4C more in detail in Line 146. There is no white box over the second bar, it’s only 1 gene mis-regulated specifically by PATH1 (mis-regulated in plants with path1 mutation).

From Figure 4B, the triple mutant has an almost inverted expression of mis-regulated genes. High expression genes are now lowly expressed and vice-versa. Has this been reported for other RNA decay mutants before?

Our response: Our RNA-seq data indicate the pat tripe mutant has more than 1000 mis-regulated genes and based on microarray data on 2-week-old lsm1alsm1b plants (Perea-Resa et al, 2012), more than 600 genes are misregulated in lsm1alsm1b mutant.

How do you explain that mutants in RNA decay have a large group of repressed transcripts and a large group of enriched transcripts? Wouldn't you suspect a general higher expression in RNA decay mutants or which kind of feedback loop would you propose is happening here? Also, since both kinds of expression changes are recorded in your RNA seq can you speculate on the specificity? Why are some genes up- and others downregulated? Would you suspect that transcription factors are under PATs control?

Our response: We assume that the mRNA decapping machinery target genes should accumulate in mRNA decapping mutants, pat mutants in our case. On the other hand, the down-regulated genes could be target genes of other mRNA degradation pathways such as exosome pathway (Line 257); We agree with the reviewer that the down regulated genes in pat triple could also be negatively regulated by the mRNA decapping targets which could be transcription factor genes. For example, our previous research indicates the transcription factor gene ASL9/LBD3 is mRNA decapping targets under PATs control.

Where is the sequencing data deposited? This dataset can be of great value for researchers in the field, but the raw data needs to be made commonly available.

Our response: We thank the reviewer for acknowledging the significance of our work. The raw data has been submitted to NCBI, accession number is PRJNA1006171(Line 307)

Minor points:

1. Check order and nomenclature for protein / gene names in Abstract and Introduction

Our response: We now carefully double check the order and nomenclature for protein / gene names in abstract and introduction (Line 8,11,14,18,19,24)

L26 / L83 "aggregate" implies non-functionality, I would use "concentrate", "condensate" or "accumulate".

Our response: We thank the reviewer for pointing it out, we now use “concentrate” (Line 29&80)

L35, L45 & L54 all state the same. Maybe remove at least one mention to reduce redundancy?

Our response: We modified these statements hopefully in a satisfactory way. (Line 56)

L211: Did you use the same imaging settings for all lines?

Our response: We used the same settings for all the lines and treatment (Line 284)

L217: RNA quality "control" word missing?

Our response: The word “control” is added in Line 296

L477: Authors should cite the newest version of their BioRxiv: Zuo, Z., Roux, M. E., Chevalier, J. R., Dagdas, Y. F., Yamashino, T., H�jgaard, S. D., ... & Petersen, M. (2022). The mRNA decapping machinery targets LBD3/ASL9 to mediate apical hook and lateral root development in Arabidopsis. bioRxiv, 2022-07.

Our response: The latest version is cited in our new manuscript (Line 42)

Figure 3B-F, Figure 4C: check spelling on the axis titles.

Our response: We carefully checked the spelling on the axis titles in our new manuscript.

Reviewer #2 (Significance (Required)):

This manuscript represents a continuation of the author's characterization of the 3 PAT1s in Arabidopsis development after Zuo et al., 2021; Zuo et al., 2022a; Zuo et al., 2022b. The mutants and the corresponding RNA sequencing experiments are of value to the community working on RNA regulation and degradation or plant development. While the initial findings are interesting, the authors do not explore the stimulus-induced condensation differences between the homologues or try to link the extreme differences in expression profiles mechanistically or functionally. I think the manuscript could greatly benefit from contextualizing their work within the frame of their previous studies and what is known about PBs in terms of plant development. While the RNA seq is a comprehensive data set, a closer examination and a better representation of the results would help readers to access the findings.

__Our response: __We thank the reviewer for the constructive criticism. We hope the reviewer is satisfied by our modified manuscript.

Reviewer expertise: RNA granule biology, Arabidopsis, molecular biology

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

Summary:

In the study "PAT mRNA decapping factors function specifically and redundantly during development in Arabidopsis" authors investigate potential specific functions of Arabidopsis PAT1 orthologs in plant development. Authors observe differences in rosette phenotypes (leaf size, serration and number) of single and multiple mutants of PAT1 gene family, show variation in translocation of the corresponding PAT1 proteins to processing bodies under a set of stress conditions and perform transcriptomics on the established mutants to elucidate the impact of individual PATs on posttranscriptional regulation of plant gene expression. Authors conclude that PAT1 orthologs have both overlapping and specific roles in plant development.

__Our response: __We thank the reviewer for the peer review. Please see our detailed answers to the reviewer’s suggestions in the following.

Major comments:

1. The study contains intersting transcriptomics data that will be of use for the scientific community. However, analysis of the transcriptomics results could be discussed a bit more in depth. Authors could express their opinion about what gene expression changes might be caused by direct degradation via PAT1-dependent decapping mechanism and what changes are more likely to have occurred indirectly via other factors.

__Our response: __We followed the reviewer’s suggestion and thus we analysed and discussed more in depth about the transcriptomic data (Line145, 220 &232)

The intersting phenotypic observations are currently poorly linked to the transcriptomics/qPCR data provided, resulting in a somewhat fragmented story flow.

__Our response: __We appreciate the reviewer thought the pat mutants’ phenotype are interesting, however we disagre with the reviewer on the statement of “poorly linked to the transcriptomics/ qPCR data”. For instance, downregulation of developmental and auxin responsive genes could explain the stunt growth phenotype in the pat triple mutant. Furthermore, the published petiole elongation regulator genes XTR7/XTH15 and PIL2/PIF6 exhibit decreased expression level only in mutants with shorter petioles. Nevertheless, we hope our new data and analysis will satisfy the reviewer.

The transcriptomics was performed on the 6-weeks old plants. It would be helpful to learn more about authors reasoning for choosing this developmental stage for sampling. Why did authors decide against sampling at the earlier stages, before the observed leaves phenotypes were established?

__Our response: __The pat mutants growth phenotypes showed bigger difference among each other at the late stage, therefore we performed RNA-seq on these samples. But we agree with the reviewer (also reviewer 1, major comment #2), transcriptomic shift at earlier stage could also be responsible for the observed phenotype, thus we performed qRT-PCR on the pat mutants at earlier stages for certain genes to examine this (Line 162 &169)

Authors obtained intriguing results on specific translocation of PAT1, PATH1 and PATH2 to processing bodies in the root cells upon various stresses. Perhaps root transcriptomics of single PAT1, PATH1 and PATH2 knockouts under control conditions, treatment that translocate all three proteins to PBs(IAA) and selectively translocate only PAT1 (e.g. cytokinin) could shed more light on the redundancy an specificity of these proteins as the mRNA decapping factors.

__Our response: __We appreciate the reviewer found our findings interesting. The specific translocation of PAT1, PATH1 and PATH2 to PBs in the root cells upon various stimuli indicates functional specificity and redundancy in cellular level which correlates with mutants’ growth phenotype. However, we agree with the reviewer that root transcriptomic data on pat mutants are very interesting, we are more than willing to share these mutants with peers who want to persue this in more detail.

Do authors consider PAT1, PATH1 and PATH2 to be localized to different PBs sub-populations? It could be intersting to check co-localization of PAT1, PATH1 and PATH2 under various stress conditions. Could authors elaborate on their view of PBs composition and fate to which different PAT1s are recruited?

__Our response: __We agree with the reviewer that it’s interesting to check co-localization of PAT1, PATH1 and PATH2. We observed partial localization of CFP-PATH2(in blue) and Venus-PAT1(in yellow) when transiently expressed in Benthmiana. But for permanent lines, we failed at observing separate CFP-PATH2(Blue) signal due to too much signal leakage from Venus-PAT1(Green). Given the fact that PATs function redundantly, we would assume they are partially co-localized in cellular level.

Could authors speculate what features in the PAT1 protein might cause it being recruited to PBs more efficiently (or better to say, under a broader range of stresses) in comparison to PATH1 and 2?

__Our response: __The release of ribosome-free mRNPs induces PB formation (Brengues et al., 2005). We suspect PAT1 could bind broader mRNAs compared to PATH1 and PATH2, therefor PAT1-mRNPs could form PBs more efficiently. Moreover, Sachdev et al found yeast PAT1 enhances the condensation of Dhh1 and RNA and PAT1-DHH1 interaction is essential for PB assembly (Sachdev et al., 2019), we assume PAT1 might have better interaction with DHH1 compared to PATH1 and PATH2 thus promote PB formation more efficiently. Please see our discussion part (Line 252)

Are all three Arabidopsis PAT paralogs co-expressed in the same tissues /developmental stages?

__Our response: __Please see our response to reviewer 2 major comment #4.

Could authors elaborate a bit more why the triple pat1 knockout has a much more severe phenotype in comparison to a single pat1 loss-of-function mutant or any of the double pat1 mutants. Do authors observe complementary changes in the PAT1 genes expression in the mutant lines, e.g. is PATH1 expressed at a higher level in the absence of PAT1 and PATH2?

__Our response: __We now elaborate more about the reason why triple pat1 knockout has the most severe phenotype in the multiple pat mutants (Line 210). We do see higher transcriptional level of PAT1 in path1-4path2-1summ2-8 and also higher transcriptional level of PATH1 in pat1-1path2-1summ2-8 but the same PATH2 transcriptional level in pat1-1path1-4summ2-8 compared to summ2-8 (Fig S1C, Line 104)

Please provide the name of the used statistical test in all figure legends.

__Our response: __We now provide the statistical test in “Material and Methods” part (Line 367).

Minor comments:

1. Authors might want to reconsider the title as it is somewhat too vague in its current form.

__Our response: __We now changed our title into “ PAT mRNA decapping factors are required for proper developmental in Arabidopsis”

Line 9: explanation of PAT1 and PATH1 and 2 abbreviations is best placed at the first mentioning of the name.

__Our response: __We carefully followed the reviewer’s suggestion (Line 10)

Line 10: mRNA degradation is rather a posttranscriptional regulation of gene expression.

__Our response: __We agree and changed our statement in the new ms (Line 9).

Lines 11 and 12: path1 and path2 abbreviation are not explained. Please note that on the Figure 1A the same proteins are labelled as PAT1H1 and PAT1H2

__Our response: __We thank the reviewer for pointing it out, we now have PATH1 and PATH2 abbreviations explained in Line 10 and also correct the labels in Fig 1A.

Lines 22-25: Would you be so kind to rephrase or elaborate on what yoPBu mean. LSM1-7/PAT1 complex are known to bind oligoadenylated transcripts indeed and even stabilize their 3' ends, it is not clear what "engage transcripts containing deadenylated tails" means in this context.

__Our response: __We hope we now rephrase the statement in a clear way (Line 25)

Line 29: for the sake of clarity, it might be beneficial to list the known activators of the decapping DCP2 enzyme, including the VCS. Generally the introduction could benefit from a bit more in depth review of the decapping mechanism.

__Our response: __We hope the more detailed introduction will satisfy the reviewer (Line 27).

Line 51:"other 2 PATs" => "other two PATs". Generally the text is quite well written, but might need a bit of polishing.

__Our response: __The text is corrected now (Line 64).

Authors are absolutely correct in their attempt to provide full information about mutant backgrounds. However, for the sake of comprehension, it would be great to grant the double and triple mutants in the summ2 background shorter and more legible names. For example, the pat1-1path1-4path2-1summ2-8 mutant could be named as pat1/h1/h2/s.

__Our response: __We originally used pat1/h1/h2/s for the triple but a colleague pointed out “h1” or “h2” are not proper gene names and suggested us to rename them. But we agree that the double and triple pat names are comprehensive, to compromise we change the triple pat mutants into pat triple.

Figure 1B:

• it would be intersting to have authors opinion on why PBs are formed in this case under non-stress(?) conditions.

__Our response: __Forming PBs is a dynamic process, and we assume that even under normal conditions, there is still ongoing mRNA decay and translational repression which should be seen as some background level of PBs (Line 85).

Please note that expressing only the N-terminal part of CFP is a weak negative control for BiFC. No restoration of CFP can occur in such case and thus it is a given that no fluorescence can be observed in these samples. For example, co-expression of nCFP-PAT1 with cCFP-GUS, would be a more rigorous negative control, better aligned with the coIP experiments.

__Our response: __We had nCFP-Gus with cCFP-LSM1 as real negative control in old Fig 1B (bottom lane). We also agree with the reviewer that only the N-terminal part of CFP is a weak negative control for BiFC, therefore we removed the weak control and only left the rigorous negative control (new Fig 1B).

Please note that some arrows point at a structure that seems to be not discernible a signal.

__Our response: __It’s due to the poor quality of the picture from the PDF file, arrows in the original high-resolution figure do point at discernible foci.

Figure 1C: It might be helpful to also include a Col-0 WT plant

__Our response: __Col-WT plant is now included in Fig S1A.

It is not clear how qPCR data and complementation lines help to characterize the established PATH1 and PATH2 loss-of-function mutants. There is no immunodetection of the corresponding proteins in the knockouts, qPCR shows no dramatic decrease in the transcript level of PATH1 and H2 and the phenotypes of complemented lines presented in the Fig S1E at a glance look quite similar to the phenotypes of the corresponding knockout mutants. Complementation lines are not used for any other experiments in this study and it is not clear why authors decided to include this material into the article.

__Our response: __To characterize the path1 and path2 mutants, we first did qRT-PCR to check the transcriptional level expression, but like the reviewer mentioned, there was no dramatic decrease indicating the mutations of path1-4 and path2-1 did not change PATH1 and PATH2 transcriptional level expression. We also tried to raise antibodies against PATH1 and PATH2, however the antibodies failed to recognize any PAT proteins. Therefore, we used the complementation lines to characterize the mutations in PATH1 and PATH2. Since path1 and path2 single mutants don’t have obvious growth phenotype and the dwarf pat triple is barely possible to transform, we had to complement the pat1path1 and pat1path2 double mutants. If the reviewer takes a closer look, the growth phenotype of the complementation lines Venus-PATH1/ pat1-1path1-4summ2-8 and Venus-PATH2/ pat1-1path2-1summ2-8 are similar to pat1-1summ2-8 but not the background pat double mutants. The complementation lines were also used to study PATH1 and PATH2 cellular localization.

Figure S1C misses labels indicating what detection of what gene is shown on what chart.

__Our response: __We thank the reviewer for pointing it out, the gene names are indicated now in new FigS1C.

Experiments to visualize PBs under various stress stimuli were conducted on roots for the Figure 2 while coIP was performed on the green tissue. Could authors elaborate on whether PB formation could be expected to be the same in different plant organs? Somewhat related to the same topic, Figure 2 contains micrographs obtained on meristematic, transition and elongation root zones, in which epidermal cells are present at various developmental stages. Since PAT proteins are suggested to impact plant development, it might be prudent to obtain observations for all samples at the same developmental stage. Could authors provide their opinion about how representative the provided micrographs are for all root zones? Furthermore, Venus-PATH2 under ACC treatment shows punctate localization only in a single cell out of the three-ish cells visible on the micrograph, potentially indicating differences in PAT2 recruitment to PBs in trichoblasts and atrichoblasts. This in itself could be an intersting observation helpful for elucidating the specific roles of PAT1 orthologs.

__Our response: __CoIP results from Benthamiana leaves indicate Arabidopsis PATs and LSM1 are in the same complex, and PB visualization in root area suggests PATs respond to different hormone treatments. flg22 treatment has been published to induce PB formation in Arabidopsis root but dissemble PBs in Arabidopsis protoplasts, indicating a tissue specific manner of PB formation. We randomly chose 1 picture/treatment from 9 (3 plants * bio-triplicates) which showed the same. However, we thank the reviewer for pointing out the confocal pictures we chose were not all from elongation zone, we now carefully checked all our confocal pictures and made sure they are from the same developmental stages. We also discuss more of PATH2 localization in response to ACC (Line 251).

Figure 4C would greatly benefit from a more detailed description in the main text and figure legend of what authors show/conclude.

__Our response: __We thank the reviewer for the suggestion hence we describe Fig 4C in more detail in our new manuscript (Line 146).

Figure 5, please avoid using the same color for the bars for the triple pat knockout and the control summ2-8 line

__Our response: __We changed the colour scheme for all the mutants (new Fig 4E).

Figure 5B legend should include the name of the statistical test.

__Our response: __We now include the name of the statistical test in “Material and Methods” (Line 367).

Figure S2: The coIP experiment is a bit difficult to interpret due to the extremely low protein quantities in some of the input samples. Perhaps a repetition with more balanced input quantities would be beneficial. The figure legend does not contain information on how normalized intensity values were obtained.

__Our response: __We used the same amount of total protein for each sample (3mg) for each IP, PATH1 and PATH2 don’t express as high as PAT1. The numbers indicate the comparative ratio between PAT-HA protein signal and LSM1-GFP signal, and PAT1-HA/LSM1-GFP under non-treatment condition is normalized as 1.

Line 130: Fig S2 is referenced but Fig S3 is meant

__Our response: __We thank the reviewer for pointing out our mistake, the correct figure is now referenced.

Reviewer #3 (Significance (Required)):

Strength:

Regulation of gene expression by mRNA decay is an extremely intersting topic and is highly relevant in plant stress and developmental biology. This study provides a more in depth view on the potential specific roles of the three PAT1 orthologs in Arabidopsis plants. Authors established loss-of-function mutants of the corresponding genes and performed transcriptomics analysis that will be a valuable source for future studies. Furthermore, microscopy analysis of PATH1 and PATH2 translocation to PBs indicates their potential specific roles in plant stress response.

Weakness: The current version of this study suffers from vague presentation of the results. Starting from the title and ending with discussion authors provide a "general" view on their results and do not go into detailed interpretations. Thus, no mechanistic insight has been derived or at least suggested from the wealth of the transcriptomics, phenotypic and microscopy data.

The introduction should provide more detailed information on what is known on the PAT1 role in the mRNA decapping pathway and its relevance for plant stress response and development.

Please note, that the above mentioned suggestion of different sampling for transcriptomics analysis is not meant as a request for this particular study, but rather as an illustration of an expectation a reader would built while following the current version of the text. A thorough description of the strategy for transcriptomics and a more in depth analysis might significantly strengthen the study's coherence and impact.

Advance:

At this stage, the study looks more like an incremental advance of the work from the same laboratory performed for the single PAT1 protein. However, as mentioned in the comments above, the study might be made significantly stronger by elaborating the results analysis and highlighting potential discoveries.

Audience:

The topic of this study is of a significant interest to a broad audience performing research in plant stress biology and also developmental plant biology.

__Our response: __We thank the reviewer for acknowledging the significance of our work and the structural criticism. We hope our detailed answers to the reviewer’s suggestions and the additional data we included in the manuscript will satisfy the reviewer.

Reviewer's and co-reviewer's fields of expertise:

Molecular Biology, Plant cell biology, Plants Stress response, Autophagy, Stress granules

__Reviewer #4 (Evidence, reproducibility and clarity (Required)): __

PAT1 (Protein Associated with Topoisomerase II) are RNA-binding proteins involved in the control of mRNA decay in the cytoplasm. Plants possess multiple PAT1 family members, three in Arabidopsis, PAT1, PATH1 and PATH2. According to the literature, the pat1 mutant shows dwarfism and de-repressed immunity. In this paper, Zou et al. describe the function of PATH1 and PATH2. Two pieces of evidence are consistent with their role in the control of mRNA decay. First, Co-IP and bimolecular Fluorescence Complementation assays in tobacco indicate physical interaction and co-localization of PAT1, PATH1 or PATH2 with LSM1 (Fig. 1), which is a protein present in decapping complexes that form the cytoplasmic foci involved in mRNA decay. Second, PAT1, PATH1 and PATH2 are present in these cytoplasmic Processing Bodies (Fig. 2). Zou et al. generated path1 and path2 mutants, double mutants with pat1 and the triple mutant using independent alleles and the summ2 background to avoid autoimmunity interference. The mutants show leaf growth (Fig. 3) and gene expression (Fig. 4) phenotypes that are not exactly similar among the different family members, but there is significant redundancy revealed by these phenotypes.

__Our response: __We thank the reviewer for the peer review. Please see our detailed answers to the reviewer’s suggestions in the following.

1. The conclusions are straight forward and, apparently, well supported by the data. However, the authors should confirm that when they provide the number of replicates (n) in the legends to the figures, this actually refers to the number of biological replicates. The statements should be based on true biological replicates (not technical replicates). The statistical tests should also be explicitly indicated (including that used to identify DEG in the RNAseq experiment).

__Our response: __We carefully went through our figures and made sure the number of replicates (n) were correctly stated in figure legends and the statistical tests were indicated (Line 367)

Reviewer #4 (Significance (Required)):

The results are useful but mainly descriptive. Personally, I am interested in the mechanisms involved in the control of growth and the manuscript does not mechanistically link the action of PAT1, PATH1 and PATH2 to the transcriptome and the latter to the growth patterns.

__Our response: __We thank the reviewer for acknowledging the significance of our work of characterizing PATs and we hope our new data could satisfy the reviewer in regarding to “mechanistical link”.

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 #4

Evidence, reproducibility and clarity

PAT1 (Protein Associated with Topoisomerase II) are RNA-binding proteins involved in the control of mRNA decay in the cytoplasm. Plants possess multiple PAT1 family members, three in Arabidopsis, PAT1, PATH1 and PATH2. According to the literature, the pat1 mutant shows dwarfism and de-repressed immunity. In this paper, Zou et al. describe the function of PATH1 and PATH2. Two pieces of evidence are consistent with their role in the control of mRNA decay. First, Co-IP and bimolecular Fluorescence Complementation assays in tobacco indicate physical interaction and co-localization of PAT1, PATH1 or PATH2 with LSM1 (Fig. 1), which is a protein present in decapping complexes that form the cytoplasmic foci involved in mRNA decay. Second, PAT1, PATH1 and PATH2 are present in these cytoplasmic Processing Bodies (Fig. 2). Zou et al. generated path1 and path2 mutants, double mutants with pat1 and the triple mutant using independent alleles and the summ2 background to avoid autoimmunity interference. The mutants show leaf growth (Fig. 3) and gene expression (Fig. 4) phenotypes that are not exactly similar among the different family members, but there is significant redundancy revealed by these phenotypes.

The conclusions are straight forward and, apparently, well supported by the data. However, the authors should confirm that when they provide the number of replicates (n) in the legends to the figures, this actually refers to the number of biological replicates. The statements should be based on true biological replicates (not technical replicates). The statistical tests should also be explicitly indicated (including that used to identify DEG in the RNAseq experiment).

Significance

The results are useful but mainly descriptive. Personally, I am interested in the mechanisms involved in the control of growth and the manuscript does not mechanistically link the action of PAT1, PATH1 and PATH2 to the transcriptome and the latter to the growth patterns.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

In the study "PAT mRNA decapping factors function specifically and redundantly during development in Arabidopsis" authors investigate potential specific functions of Arabidopsis PAT1 orthologs in plant development. Authors observe differences in rosette phenotypes (leaf size, serration and number) of single and multiple mutants of PAT1 gene family, show variation in translocation of the corresponding PAT1 proteins to processing bodies under a set of stress conditions and perform transcriptomics on the established mutants to elucidate the impact of individual PATs on posttranscriptional regulation of plant gene expression. Authors conclude that PAT1 orthologs have both overlapping and specific roles in plant development.

Major comments:

• The study contains intersting transcriptomics data that will be of use for the scientific community. However, analysis of the transcriptomics results could be discussed a bit more in depth. Authors could express their opinion about what gene expression changes might be caused by direct degradation via PAT1-dependent decapping mechanism and what changes are more likely to have occurred indirectly via other factors.
• The intersting phenotypic observations are currently poorly linked to the transcriptomics/qPCR data provided, resulting in a somewhat fragmented story flow.
• The transcriptomics was performed on the 6-weeks old plants. It would be helpful to learn more about authors reasoning for choosing this developmental stage for sampling. Why did authors decide against sampling at the earlier stages, before the observed leaves phenotypes were established?
• Authors obtained intriguing results on specific translocation of PAT1, PATH1 and PATH2 to processing bodies in the root cells upon various stresses. Perhaps root transcriptomics of single PAT1, PATH1 and PATH2 knockouts under control conditions, treatment that translocate all three proteins to PBs(IAA) and selectively translocate only PAT1 (e.g. cytokinin) could shed more light on the redundancy an specificity of these proteins as the mRNA decapping factors.
• Do authors consider PAT1, PATH1 and PATH2 to be localized to different PBs sub-populations? It could be intersting to check co-localization of PAT1, PATH1 and PATH2 under various stress conditions. Could authors elaborate on their view of PBs composition and fate to which different PAT1s are recruited?
• Could authors speculate what features in the PAT1 protein might cause it being recruited to PBs more efficiently (or better to say, under a broader range of stresses) in comparison to PATH1 and 2?
• Are all three Arabidopsis PAT paralogs co-expressed in the same tissues /developmental stages?
• Could authors elaborate a bit more why the triple pat1 knockout has a much more severe phenotype in comparison to a single pat1 loss-of-function mutant or any of the double pat1 mutants. Do authors observe complementary changes in the PAT1 genes expression in the mutant lines, e.g. is PATH1 expressed at a higher level in the absence of PAT1 and PATH2?
• Please provide the name of the used statistical test in all figure legends.

Minor comments:

• Authors might want to reconsider the title as it is somewhat too vague in its current form.
• Line 9: explanation of PAT1 and PATH1 and 2 abbreviations is best placed at the first mentioning of the name.
• Line 10: mRNA degradation is rather a posttranscriptional regulation of gene expression.
• Lines 11 and 12: path1 and path2 abbreviation are not explained. Please note that on the Figure 1A the same proteins are labelled as PAT1H1 and PAT1H2
• Lines 22-25: Would you be so kind to rephrase or elaborate on what you mean. LSM1-7/PAT1 complex are known to bind oligoadenylated transcripts indeed and even stabilize their 3' ends, it is not clear what "engage transcripts containing deadenylated tails" means in this context.
• Line 29: for the sake of clarity, it might be beneficial to list the known activators of the decapping DCP2 enzyme, including the VCS. Generally the introduction could benefit from a bit more in depth review of the decapping mechanism.
• Line 51:"other 2 PATs" => "other two PATs". Generally the text is quite well written, but might need a bit of polishing.
• Authors are absolutely correct in their attempt to provide full information about mutant backgrounds. However, for the sake of comprehension, it would be great to grant the double and triple mutants in the summ2 background shorter and more legible names. For example, the pat1-1path1-4path2-1summ2-8 mutant could be named as pat1/h1/h2/s.
• Figure 1B:
• it would be intersting to have authors opinion on why PBs are formed in this case under non-stress(?) conditions.
• Please note that expressing only the N-terminal part of CFP is a weak negative control for BiFC. No restoration of CFP can occur in such case and thus it is a given that no fluorescence can be observed in these samples. For example, co-expression of nCFP-PAT1 with cCFP-GUS, would be a more rigorous negative control, better aligned with the coIP experiments.
• Please note that some arrows point at a structure that seems to be not discernible a signal.
• Figure 1C: It might be helpful to also include a Col-0 WT plant
• It is not clear how qPCR data and complementation lines help to characterize the established PATH1 and PATH2 loss-of-function mutants. There is no immunodetection of the corresponding proteins in the knockouts, qPCR shows no dramatic decrease in the transcript level of PATH1 and H2 and the phenotypes of complemented lines presented in the Fig S1E at a glance look quite similar to the phenotypes of the corresponding knockout mutants. Complementation lines are not used for any other experiments in this study and it is not clear why authors decided to include this material into the article.
• Figure S1C misses labels indicating what detection of what gene is shown on what chart.
• Experiments to visualize PBs under various stress stimuli were conducted on roots for the Figure 2 while coIP was performed on the green tissue. Could authors elaborate on whether PB formation could be expected to be the same in different plant organs? Somewhat related to the same topic, Figure 2 contains micrographs obtained on meristematic, transition and elongation root zones, in which epidermal cells are present at various developmental stages. Since PAT proteins are suggested to impact plant development, it might be prudent to obtain observations for all samples at the same developmental stage. Could authors provide their opinion about how representative the provided micrographs are for all root zones? Furthermore, Venus-PATH2 under ACC treatment shows punctate localization only in a single cell out of the three-ish cells visible on the micrograph, potentially indicating differences in PAT2 recruitment to PBs in trichoblasts and atrichoblasts. This in itself could be an intersting observation helpful for elucidating the specific roles of PAT1 orthologs.
• Figure 4C would greatly benefit from a more detailed description in themain text and figure legend of what authors show/conclude.
• Figure 5, please avoid using the same color for the bars for the triple pat knockout and the control summ2-8 line
• Figure 5B legend should include the name of the statistical test.
• Figure S2: The coIP experiment is a bit difficult to interpret due to the extremely low protein quantities in some of the input samples. Perhaps a repetition with more balanced input quantities would be beneficial. The figure legend does not contain information on how normalized intensity values were obtained.
• Line 130: Fig S2 is referenced but Fig S3 is meant

Significance

Strength: Regulation of gene expression by mRNA decay is an extremely intersting topic and is highly relevant in plant stress and developmental biology. This study provides a more in depth view on the potential specific roles of the three PAT1 orthologs in Arabidopsis plants. Authors established loss-of-function mutants of the corresponding genes and performed transcriptomics analysis that will be a valuable source for future studies. Furthermore, microscopy analysis of PATH1 and PATH2 translocation to PBs indicates their potential specific roles in plant stress response.

Weakness: The current version of this study suffers from vague presentation of the results. Starting from the title and ending with discussion authors provide a "general" view on their results and do not go into detailed interpretations. Thus, no mechanistic insight has been derived or at least suggested from the wealth of the transcriptomics, phenotypic and microscopy data.<br /> The introduction should provide more detailed information on what is known on the PAT1 role in the mRNA decapping pathway and its relevance for plant stress response and development. Please note, that the above mentioned suggestion of different sampling for transcriptomics analysis is not meant as a request for this particular study, but rather as an illustration of an expectation a reader would built while following the current version of the text. A thorough description of the strategy for transcriptomics and a more in depth analysis might significantly strengthen the study's coherence and impact.

Advance: At this stage, the study looks more like an incremental advance of the work from the same laboratory performed for the single PAT1 protein. However, as mentioned in the comments above, the study might be made significantly stronger by elaborating the results analysis and highlighting potential discoveries.

Audience: The topic of this study is of a significant interest to a broad audience performing research in plant stress biology and also developmental plant biology.

Reviewer's and co-reviewer's fields of expertise:

Molecular Biology, Plant cell biology, Plants Stress response, Autophagy, Stress granules

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Referee #2

Evidence, reproducibility and clarity

Zuo et al., characterize the role of three cytoplasmic mRNA-decay activator proteins PAT1, PATH1 and PATH2 in the context of plant development and leaf morphology in Arabidopsis thaliana and Nicotiana benthamiana. The authors show that the triple pat mutant displays the most severe dwarfism of all combinatorial mutants. Through treatment with different stimulants the authors found that only IAA treatment induces the three homologues to form condensates (possibly PBs), while PAT1 forms condensates upon every tested stimulus. An extensive RNA seq experiment revealed miss-regulation of several hundred genes in the higher order mutants, several of which were involved in auxin responsive and leaf morphology determinant genes.

Major points:

• Title is not meaningful as is and, in my opinion, does not reflect the main findings in the manuscript.
• The results section could benefit from improved flow between the paragraphs and more reasoning for the next steps taken to help readers understand the aims of the authors.
• L46: "So far little is known about the functions of these three PATs in plant development.", The authors themselves have studied these proteins in the context of seed germination and ABA control, as well as apical hook formation and auxin responses. Should at least be mentioned and the results discussed in this context.
• What are the expression levels and patterns of PATH1 and PATH2 compared to PAT1? Is anything known about spatial or temporal regulation of these proteins?
• Figure 1:
  • I do not agree that the authors have shown that "PATH1 and PATH2 are also mRNA decapping factors", rather that these proteins can co-localize (and possibly interact) with LSM1. Decapping assays for example with the known PAT1 de-capping targets from their previous work and their extensive mutant collection could be used to test this.
  • From the BiFC experiment (Figure 1B) it looks like PATs are mostly soluble in the cytoplasm (like LSM1) and might be stress-induced components of PBs (like LSM1). Do PATs co-localize with other canonical PB markers that are more prone to condensation, like DCPs or VCS? BiFC could be performed after IAA treatment to confirm that the cytoplasmic foci are indeed LSM1-positive PBs.
  • A: please provide uncropped images of all Western blots in supplemental data.
• I applaud the authors for establishing this great higher order mutant collection that will be very useful for researchers in the field. However, I am confused about the description of these mutants. If I understood it correctly, these mutants were already used in a previous study by the authors, namely "Zuo, Z., et al., Molecular Plant-Microbe Interactions, 35(2), 125-130." & Zuo, Z., et al., (2021). FEBS letters, 595(2), 253-263." In this study the authors refer to a BioRxiv "Zuo, Z., et al., (2019)." as the reference for these Arabidopsis lines. Is this current manuscript a continuation of the BioRxiv? Please elaborate whether these lines have been used and described in previous studies.

• L72: Is the strong developmental phenotype of the higher order mutants persistent under long day conditions? Considering the strong developmental phenotypes of the mutants, the flowering transition and morphology could be an interesting trait to study. Why did you choose short day conditions for this study?

• L78: This statement is hard to see in Figure 1C and best described for Figure 3A.

• L82: Please include a reasoning for testing PATs localization after hormone treatment. Do you have any indication that other PB proteins behave similar to either PAT1 or the PATHs after hormone treatment to substantiate that these foci observed are indeed PBs? What is known about PBs after hormone treatment in planta?
• Figure 2:
  • How does the localization of LSM1 change under the same treatments? Does ist behave like PAT1 or the homologues?
  • Which part of the root was imaged for this experiment? Is it possible that the observed foci are ARF-condensates as reported by Jing et al., 2022? Do you observe a gradual change in numbers or morphology along the root?
  • How did the authors decide on the concentrations for the stimulant treatments? Have you tried different doses, and could the responses be dose-dependent?
  • A representative image is not sufficient for quantitative responses, like RNA granule condensation. Please provide a quantification of stimulant-induced foci after the different treatments.
• L91: Does that mean that most co-precipitated signal comes from the soluble fraction and not PB-localized? Would an RNAse treatment step eliminate the co-precipitation (optional)?
• L92/93: Or alternatively that PAT1 localizes to PBs independent of the stress, while PATHs are signal-specific PB components?
• Figure 3:
  • I wonder if these results fit better in conjunction with Figure 1, either as a combined figure or move before Figure 2.
  • It is interesting that path2/pat1, while being dwarfed, is less serrated compared to pat1 or path1/pat1. Can you find any indications in your RNAseq set which genes might be involved?
  • Indicate statistical test used to determine p-value
• L116/L117: Doesn't the result in Figure 3E indicate that PATH1 and PATH2 are not fully redundant, but that PATs have specific and narrow roles in leaf development? L116 goes against your statement in L150 & L160. What is known about the expression patterns of PAT1, PATH1 and PHATH2?
• L123: PC3 only explains 0.55% of the variance, so differences along this axis will be overinflated. In my interpretation the pat1/path2 mutant is clustering apart from the other higher order mutants, which is also reflected in the leaf phenotypes. A 2D PCA would be sufficient to describe most of the variation.
• Figure 4:
  • A: The 3D-PCA inflates the differences between higher order mutants along PC3, even though this axis explains only 0.55% of the variance, maybe a 2D-PCA would more intuitively cluster the samples together?
  • B: Please explain the scale in the figure legend and which genes were included? Only DEGs between triple mutant and summ2-8 or DEGs that were different in at least one higher order mutant?
  • C: several comparisons are missing from the upset-plot. Please show the complete plot, also is there a white box laid over the second bar in the upper graph? It would help the reader, if the results section would explain the plots and the comparisons took. Which differences are the authors interested in?
  • From Figure 4B, the triple mutant has an almost inverted expression of mis-regulated genes. High expression genes are now lowly expressed and vice-versa. Has this been reported for other RNA decay mutants before?
• How do you explain that mutants in RNA decay have a large group of repressed transcripts and a large group of enriched transcripts? Wouldn't you suspect a general higher expression in RNA decay mutants or which kind of feedback loop would you propose is happening here? Also, since both kinds of expression changes are recorded in your RNA seq can you speculate on the specificity? Why are some genes up- and others downregulated? Would you suspect that transcription factors are under PATs control?
• Where is the sequencing data deposited? This dataset can be of great value for researchers in the field, but the raw data needs to be made commonly available.

Minor points:

• Check order and nomenclature for protein / gene names in Abstract and Introduction
• L26 / L83 "aggregate" implies non-functionality, I would use "concentrate", "condensate" or "accumulate".
• L35, L45 & L54 all state the same. Maybe remove at least one mention to reduce redundancy?
• L211: Did you use the same imaging settings for all lines?
• L17: RNA quality "control" word missing?
• L477: Authors should cite the newest version of their BioRxiv: Zuo, Z., Roux, M. E., Chevalier, J. R., Dagdas, Y. F., Yamashino, T., Højgaard, S. D., ... & Petersen, M. (2022). The mRNA decapping machinery targets LBD3/ASL9 to mediate apical hook and lateral root development in Arabidopsis. bioRxiv, 2022-07.
• Figure 3B-F, Figure 4C: check spelling on the axis titles.

Significance

This manuscript represents a continuation of the author's characterization of the 3 PAT1s in Arabidopsis development after Zuo et al., 2021; Zuo et al., 2022a; Zuo et al., 2022b. The mutants and the corresponding RNA sequencing experiments are of value to the community working on RNA regulation and degradation or plant development. While the initial findings are interesting, the authors do not explore the stimulus-induced condensation differences between the homologues or try to link the extreme differences in expression profiles mechanistically or functionally. I think the manuscript could greatly benefit from contextualizing their work within the frame of their previous studies and what is known about PBs in terms of plant development. While the RNA seq is a comprehensive data set, a closer examination and a better representation of the results would help readers to access the findings.

Reviewer expertise: RNA granule biology, Arabidopsis, molecular biology

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Referee #1

Evidence, reproducibility and clarity

The manuscript investigates the role of PAT1 gene family in Arabidopsis thaliana. Though the PAT1 protein has been previously investigated and displayed immune-related and developmental phenotypes, the other two members of the family, PATH1 and PATH2, have not been well studied. The authors set out to understand the role of these proteins in relation to the role of PAT1. They thus generated single, double, and triple mutants of the possible combinations of PAT1 genes and examined their phenotypes. As the study focused on the developmental effects of PAT1, the mutants were generated on the background of the summ2 mutant to avoid phenotypes related to immune response. The authors notice a developmental difference between the pat1 mutant combinations, suggesting that PAT1 acts differently than PATH1 and PATH2 and that the PATH proteins serve a redundant function. They also performed RNA-seq analysis to identify differentially-regulated genes in the mutant combinations. The study is interesting and well-executed, yet I believe some questions should still be addressed:

• The research mainly focuses on the developmental phenotype of pat mutants but also tests the interaction of PATH proteins with RNA decapping enzymes to check their function and localization during different treatments. I found it a bit confusing since Figure 1 also shows the developmental phenotype of the mutants. I think editing the order of the figures would make the overall story more coherent.
• My main concern is the correlation between the developmental phenotype of the mutants and the gene expression. Leaf samples for RNA extraction were taken when the plants were 6 weeks old, and the developmental phenotype is very evident. It is thus not possible to tell whether the differences in gene expression are a cause or effect of the developmental phenotype. I think performing qPCR of selected candidates at earlier developmental times might help solve this issue, as well as the characterization of younger plants for the developmental phenotypes (such as leaf number).
• Overall, the manuscript is missing data regarding replicate numbers in the IP and confocal microscopy experiments.

Minor comments:

• Figure 1C - the authors should add a picture of Col0 plants as well as the mutants.
• Figure 3 - Calculating the leaf-to-petiole ratio in the different mutants would be good.
• Figure 4 - the details in the figure are very unclear, especially in the PCA. It would be good to display the data in 2D for PC1 and PC3 and change the colors a bit.

Significance

Both PATH proteins have been less investigated than PAT1, and in that sense, the work is novel. However, it seems that most of the phenotype is attributed to PAT1 rather than the other family members, limiting the interest to the broad plant science community.

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Reply to the reviewers

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

The study largely focuses on the use of a 293 cell line that lacks a functional Dicer gene originally identified by the Cullen group. Baldaccini use this cell line, referred to as NoDice cells, to reconstitute various Dicer isoforms that have thus far been described in a variety of settings (e.g., stem cells and oocytes). Collectively, these data demonstrate the capacity of certain N-terminal truncations of Dicer to inhibit Sindbis virus and reduce the presence of viral dsRNA, supporting some of the observations made thus far concerning an antiviral role for mammalian Dicer. For other viruses, this impact was significantly more modest (SFV reduction is less than a log) or was not observed at all (VSV and SARS-CoV-2). The authors then go on to characterize the nature of the observed antiviral activity and ultimately implicate PKR and the induction of NF-kB in priming the cell's antiviral defenses. Importantly, the group also found that this antiviral activity neither required the nuclease activity of Dicer nor the kinase activity of PKR - providing evidence against antiviral RNAi in mammals. In all, the data would seem to suggest that Dicer can act as a dsRNA sensor and can mediate the activation of an NF-kB response - akin to what is observed in response to NOD or some TLR engagement. In all, it is the opinion of this reviewer that this work brings additional clarity to a concept that remains controversial in the field and therefore embodies something meaningful for the community.

With that said, there are a few issues that require additional attention. The first of these is textual. The introduction of the paper accurately describes the evidence in support of mammalian RNAi but does not invest the same time in discussing the data to the contrary. For example, Seo et al demonstrated that virus infection results in poly-adp-ribosylation of RISC preventing RNAi activity (PMID: 24075860), Uhl et al showed that IFN-induced ADAR1 resolves dsRNA in the cell and prevents RNAi (PMID: 37017521), and Tsai et al showed that virus-derived small RNAs are not loaded into the RISC in a manner that would enable antiviral activity (PMID 29903832). None of this work is referenced in this manuscript and it generates an unbalanced introduction as it relates to the controversy surrounding the idea of RNAi in mammals.

Reply: We thank the reviewer for their positive comments and suggestions. In the revised version of this manuscript, we will rewrite the introduction to take into account the published data that are not in favor of an antiviral role of RNAi in mammals and we will add the suggested references

The second issue that would further strengthen this paper relates to the fact that the authors spend a considerable amount of time discussing the data of Figure 6 and 7 as conditions that are defined by a Dicer that can not be processive in its nuclease activity (WT) vs. one that can (N1). However, there seems to be little consideration about the fact that the introduction of WT Dicer into these cells also restores miRNA biology whereas N1 appears to remain only partially functional (based on the data of Fig 3E). Given this, it seems the authors should verify that the high baseline of NFkB signaling that is being observed when comparing WT to N1 is not a product of restored miRNA function in WT cells, in contrast to the hypotheses outlined in the manuscript. This could be addressed by silencing Drosha or DGCR8 in the Dicer knockout cells prior to their reconstitution of Dicer. In the opinion of this reviewer, this experimental control would significantly strengthen the conclusions the authors are making here.

Reply: This would indeed be an ideal experiment to rule out the contribution of miRNAs in the observed phenotype. We believe however that this particular experiment would prove difficult to realize given that we reconstitute Dicer expression by lentiviral transduction and keep the cells under selection for a couple of weeks before using them for further experiments. This time frame is therefore not compatible with the use of siRNA to knock-down Drosha or DGCR8. Alternatively, we could knock them out by CRISPR-Cas9, but this would take too long and is not feasible in the frame of this work.

We can however address the concern regarding the role played by miRNAs in the observed phenotype of the Dicer N1 cells. Indeed, we can determine the miRNA profile from our small RNA sequencing data and compare them between the Dicer WT and Dicer N1 cells. We have done this comparison and could not find striking differences in miRNA expression between the two cell lines. We will add this additional piece of evidence in our revised manuscript.

Reviewer #1 (Significance (Required)):

In the manuscript entitled, "Canonical and non-canonical contributions of human Dicer helicase domain in antiviral defense" Baldaccini et al. describe their findings concerning the ability of certain N-terminal deletion variants of Dicer in contributing to mammalian antiviral activity. The concept of a functional antiviral RNAi system in mammals is a contentious one with many publications including data both in support of its existence and opposing this idea. In this manuscript, Baldaccini et al. perform a wide range of well-controlled experiments to specifically address aspects of those reports to both provide clarity in what has been documented thus far and to expand on those concepts further.

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

Summary

Whether RNAi is used as an antiviral mechanism in mammals has been a hotly debated issue. The research team previously published several papers on the roles of Dicer in siRNA/miRNA biogenesis and in antiviral responses. They have recently reported that the helicase domain of human Dicer specifically interacts with several proteins that are involved in the IFN response, including PKR. In this study, Baldaccini et al. investigated the involvement of Dicer in antiviral response using various mutants of human Dicer. They showed that deletion mutants of helicase domain exhibit antiviral activity that requires the presence of PKR. They further demonstrated that one of the mutants, N1-Dicer showed antiviral activity in an RNAi-independent manner but depending on the presence of either native PKR or kinase deficient mutants. Transcriptomic analysis revealed that numerous genes involved the IFN and inflammatory response were upregulated in the cells that express N1-Dicer, which is likely due to an increased activation of the NFκB pathway. Based on these findings, the authors propose that Dicer may act as antiviral molecule using its helicase domain, which representing a novel non-canonical function of Dicer.

Major comments:

1.The results from experiments with SARS-CoV2 are intriguing (Fig.2). The authors speculated that NFkb activation is in favor of the replication of this virus. It would be interesting to see the infection and replication of SARS-CoV2 in PKR deficient cells and cells expressing PKR mutants (as described in Fig.5). The results may prove/disapprove the authors' speculation and yield additional findings.

Reply: We thank the reviewer for this suggestion. We have cells that are double knock-out for Dicer and PKR (NoDice/∆PKR) that were transduced to stably express Dicer WT or Dicer N1 and further transduced to express ACE2. We will infect those cell lines with SARS-CoV-2, which will allow us to see whether the difference in viral accumulation can still be observed in the absence of PKR. However, it might prove more difficult to reconstitute PKR expression (WT or mutants) in these cells since they are already transduced twice with two different constructs (Dicer and ACE2).

Western blot analysis. In the method section, it is stated that proteins were quantified with Bradford method and equal loading was verified by Ponceau S staining. The members of also probed with gamma-tubulin (It was stated that antibodies against alpha-tubulin was used in the method section) as a loading control, however, the bend intensity of tubulin shows great variations among different lanes in several figures while Ponceau S staining is similar (Fig.s, 4, 5, and 8). The differences compromise the accuracy of the results.

Reply: We apologize for the difference in Tubulin signal in some of our western blots. There are several possibilities to explain those inconsistencies between Ponceau staining and Tubulin blotting, including an effect of viral infection on Tubulin expression. To remove ambiguities around this issue, we could quantify the signal across several blot replicates and provide the quantification after normalization. In addition, we would like to stress that regarding quantification of the infection, we think that the plaque assay experiments are more reliable than quantification of western blot signals.

3.RNA-seq analysis revealed that Dicer N1 cells have significantly increased expression levels of signaling molecules in type I IFN response even in uninfected cells. While this provides a potential explanation for the antiviral phenotype of N1-Dicer cells. I wonder why the expression levels of type I IFNs (probably the most potent antiviral molecules) were not analyzed in WT and Dicer N1 cells. Measurement of the levels of IFNα and IFNβ by ELISA in the cells before and after infection could provide the important and direct data to support their conclusion.

Reply: This an interesting suggestion but unfortunately, we do not believe that it would possible to quantify IFNα and IFNβ by ELISA in the cell line that we used in our experiments. Indeed, the level of expression might just be too low to be able to measure something meaningful. We could measure the induction of IFNβ expression at the mRNA level by RT-qPCR though. However, we do not believe that the observed increased expression of genes that belong to the type I IFN response is solely the effect of an increased production of IFN. These genes are also under the control of other transcription factors, including NF-kB for some of them, and it might prove difficult to make a direct link with IFNα or IFNβ production.

4.While the data presented in Fig. 5 provides convincing evidences that the antiviral activity of mediated by PKR against SINV is independent of its kinase activity in N1-Dicer cells. An interesting question is that whether antiviral activity associated with PKR is N1-Dicer dependent, which could be addressed by comparing the viral infection of NoDice∆PKR and NoDicer expressing PKR mutants.

Reply: Yes indeed, we have generated NoDice/∆PKR cells expressing PKR WT or mutant and we will infect them with SINV to confirm whether the presence of Dicer N1 is needed for the observed phenotype.

5.In the concluding paragraph of the discussion, the authors presented an oversimplified discerption of a complex model that involves a crosstalk between IFN-I and RNAi and Dicer-PKR interaction, which is difficult for the reader to compose a clear picture of mechanisms involved. It could be helpful to use a schematic illustration to summarize the action model of PKR incorporated with the canonical and non-canonical Dicer functions.

Reply: We will add a schematic model in the revised version of our manuscript to summarize our main findings.

Minor comments:

1.It stated that NoDice FHA-Dicer WT #4 and NoDice FHA:Dicer N1 110 #6 are referred to as Dicer WT and Dicer N1 cells (p.6). For simplicity, Dicer WT and Dicer N1 cells should be used throughout manuscript, including in all figures. The labels in the figures are difficult to read and are confusing in some cases.

Reply: This will be changed in the revised version to increase the clarity of the figures.

2.It is to note that p-PKR was only detected at in N1-Dicer cells at 24 hpi (Fig.8A). This is an interesting observation that was not discussed. It appears that this could be due to a delayed viral replication since these cells are already in an elevated antiviral state. This possibility could be tested by examining viral replication and dsRNA accumulation at more time points in the experiments described in Fig.1.

Reply: We have performed a kinetic of infection at more time points and we will incorporate these experiments in the revision.

3.The authors may point out the limitations of the studies. For examples, all cells used in the study are engineered HEK cell lines and were tested with limited number of viruses. As such, the observations may reflect Dicer-PKR interaction under artificially overexpressed conditions, but how the model established from the current study applies to primary cells require further investigation.

Reply: This is indeed important, we will add a sentence about this in the discussion.

Reviewer #2 (Significance (Required)):

The findings reported in this study shed some new light on a long-debated issue regarding the potential roles of RNAi as physiologically relevant antiviral mechanism in mammals. Identification of a new antiviral function of Dicer helicase domain via interaction with PKR is a new advancement of the field, and it also adds a new dimension to a complex subject that overlaps of innate immunity , RNA biology, and developmental biology associated with Dicer.

Field of expertise: Innate immunity, cell signaling, cytokine biology

Areas that that I do not have sufficient expertise to evaluate: Small RNA cloning, sequencing and, analysis.

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

This work by Baldaccini et al. explores the interplay between Dicer and the antiviral protein PKR in the context of viral infection. It builds on a previous publication of the team which demonstrates that the Dicer helicase interacts with multiple RNA binding proteins, including PKR (see Montavon et al.). In this work from 2021, they demonstrate that an artificially-truncated form of Dicer (Dicer-N1) lacking part of the helicase is antiviral against RNA viruses in a PKR-dependent fashion. This was an interesting finding because the field largely assumed that Dicer-N1 performs its antiviral function via canonical dicing of dsRNA, as part of an antiviral RNAi pathway. The present manuscript follows up on this initial discovery and deciphers the specifics of Dicer-N1 antiviral phenotype, as well as delineates the interplay between Dicer's helicase and PKR. The authors main claims are as follow:

1. i) Dicer-N1 antiviral effect does not require its catalytic activity, therefore is completely RNAi-independent.
2. ii) Neither does it require canonical PKR activation, but relies instead on NF-kB-driven inflammation. The origin of this inflammation is not studied.
3. ii) Truncated Dicers other than Dicer-N1 are antiviral through RNAi, but are also PKR-dependent. The authors claims are mostly supported by the data, although I suggest below some improvements regarding experimental approaches and data presentation. This work details in an interesting manner the interplay between the machinery of RNAi and the classical pathway of innate immunity (PKR). As explained by the authors, there is solid data in the literature demonstrating the mutual exclusivity of IFN and antiviral RNAi in differentiated cells. This mostly goes through the receptors LGP2, which inhibits dsRNA dicing by Dicer. The authors data suggest that, conversely, Dicer may play a role in preventing the unwanting activation of PKR (a non-canonical activation leading to inflammation). Given that PKR activation does not depend on virus, the authors discuss potential mechanisms of PKR triggering. This is an interesting topic that deserves further investigation (not necessarily within the frame of this work - it can be a follow-up). Another interesting piece of information is that different truncated Dicers behave differently with respect to implementing antiviral RNAi. Whilst Dicer-N1 isn't proficient in doing so, the other forms are. It shows that lab-generated truncations do not fully recapitulate what is observed with existing truncated Dicers (DicerO and aviD).

Experimental design and data interpretation

1. The authors should compare infection between different cell lines across a range of time points (ie, a virus growth curve). In Fig 4E for example, I worry that cells expressing or not PKR will reach the plateau of viral particle accumulation at different time points. One could imagine that cells lacking PKR do not show any differences in particle production at 24h, but do at earlier time points.

Reply: This is an interesting suggestion, we can perform a kinetic experiment by looking at more time points to address this point. This will allow us to determine the time needed for every cell line to reach the plateau of infection.

Western blots should be accompanied with proper quantifications plotted as bar graph with biological replicates (p-PKR, p-eIF2a and capsid).

Reply: We have biological replicates for our western blot experiments, and we will quantify those to better determine the observed changes. However, in the case of p-eIF2a, we do not think it is pertinent to measure it since there are other kinases than PKR that are known to induce eIF2a phosphorylation upon SINV infection. It might therefore not prove very informative to precisely quantify this particular signal.

Microscopy images should be properly quantified across biological replicates (Fig 1&2 for the J2 staining, for example).

Reply: We could do a proper quantification of the J2 signal across replicates, but we do not think it would bring much to our message. Here, we mostly used J2 staining as a qualitative indication that the infection was impacted or not. We have a proper quantification of the effect with our plaque assay experiments, which are way more robust to determine the levels of infection between conditions.

Confounding factors hinder the interpretation of siRNA accumulation (Suppl Fig 2): i) the efficiency of dsRNA dicing from different Dicers will generate different amounts of siRNAs from a given amount of dsRNA and ii) the higher antiviral response translates into decreased infection, so decreased dsRNA substrate. I suggest that the authors normalise the amount of viral siRNAs over the total amount of viral genomes. This should allow to assess if Dicer-N1 is better at dicing dsRNA than WT in these conditions.

Reply: This is a valid concern and we agree that it is important to be able to normalize small RNA reads between conditions before reaching a conclusion. The problem is that there is no easy way to do this since we do not get a direct measurement of viral genomes accumulation from our small RNA sequencing data. To better compare the two conditions, we could normalize the individual viral siRNA to the total number of viral reads. Another problem that we face is that we are looking here at the AGO-loaded small RNAs, which makes it more difficult to assess dicing efficiency since not every generated siRNA might be loaded into an Argonaute protein. In fact, this has been proposed by the Cullen laboratory in a paper published in 2018 (Tsai et al. doi: 10.1261/rna.066332.118). They showed that although viral siRNAs were generated during IAV infection, those were inefficiently loaded and thus did not significantly impacted the infection.

In Fig 8, the authors should verify that phospho-p65 increase depends on PKR by repeating the experiment in PKR KO cells.

Reply: Yes, good point. We will check what happens to phosphorylation of p65 in PKR KO cells. In addition, we can also measure the effect on a known NF-kB target by RT-qPCR (e.g. PTGS2).

Data representation

1. Levels of phospho-PKR and eIF2a need to be normalised on the total amount of PKR and eIF2a, respectively. The authors should quantify the blots and present bar graphs with biological replicates and statistics.

Reply: As mentioned above in our reply to point 2, we can add the quantification for phospho PKR, but we do not think it is pertinent to do it for eIF2a.

Could the authors add the names of representative genes on the volcano plots of Fig 7?

Reply: Yes, this will be done.

Points of discussion

1. In Fig 4C, catalytically-dead mutants of truncated Dicers (other than N1) do not display an antiviral effect. Presumably, such proteins implement canonical antiviral RNAi. Is there a reason why the authors interpret this data as Dicers being "partially" antiviral through RNAi (l. 92). This data instead suggest that is it totally dependent on RNAi.

Reply: Indeed, and we do not say the contrary. It seems that some of this helicase-truncated Dicer proteins can act through RNAi. However, they also depend on PKR, so in the end it might be a combination of the two that allows their antiviral effect.

Gurung et al. demonstrate that PKR is activated in Dicer KO mouse ES cells, which results in phosphorylation of eIF2a at steady-state. This is different from the authors' data, in which PKR activation does not affect eiF2a phosphorylation. Could the authors discuss this discrepancy?

Reply: The problem that we face here is that SINV is known to also activate GCN2 and therefore eIF2a phosphorylation does not strictly rely on PKR in our experimental conditions. In addition, we did not check eIF2a phosphorylation in Dicer KO cells, but we always compare Dicer WT and Dicer N1 expressing cells.

Do the authors expect that truncated Dicers other than N1 trigger an inflammatory response such as the one described for N1? Would it be possible to have this antiviral inflammatory response in conjunction with antiviral RNAi?

Reply: This goes back to Point 1 mentioned previously. We think indeed that there might be a dual action of Dicer and that it will be important to check whether in other cellular systems or animal model such a phenomenon can be observed as well. This is a point that we did address in the discussion of our manuscript (line 522-525).

Reviewer #3 (Significance (Required)):

This is a study that conceptually advances the field of antiviral RNAi in mammals, including its interplay with the machinery of innate immunity. It is of interest for virologists and immunologists. My expertise is centered on the mechanisms of innate immunity in mammalian cells, including antiviral RNAi.

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Referee #3

Evidence, reproducibility and clarity

This work by Baldaccini et al. explores the interplay between Dicer and the antiviral protein PKR in the context of viral infection. It builds on a previous publication of the team which demonstrates that the Dicer helicase interacts with multiple RNA binding proteins, including PKR (see Montavon et al.). In this work from 2021, they demonstrate that an artificially-truncated form of Dicer (Dicer-N1) lacking part of the helicase is antiviral against RNA viruses in a PKR-dependent fashion. This was an interesting finding because the field largely assumed that Dicer-N1 performs its antiviral function via canonical dicing of dsRNA, as part of an antiviral RNAi pathway. The present manuscript follows up on this initial discovery and deciphers the specifics of Dicer-N1 antiviral phenotype, as well as delineates the interplay between Dicer's helicase and PKR. The authors main claims are as follow:

i) Dicer-N1 antiviral effect does not require its catalytic activity, therefore is completely RNAi-independent.

ii) Neither does it require canonical PKR activation, but relies instead on NF-kB-driven inflammation. The origin of this inflammation is not studied.

ii) Truncated Dicers other than Dicer-N1 are antiviral through RNAi, but are also PKR-dependent.

The authors claims are mostly supported by the data, although I suggest below some improvements regarding experimental approaches and data presentation. This work details in an interesting manner the interplay between the machinery of RNAi and the classical pathway of innate immunity (PKR). As explained by the authors, there is solid data in the literature demonstrating the mutual exclusivity of IFN and antiviral RNAi in differentiated cells. This mostly goes through the receptors LGP2, which inhibits dsRNA dicing by Dicer. The authors data suggest that, conversely, Dicer may play a role in preventing the unwanting activation of PKR (a non-canonical activation leading to inflammation). Given that PKR activation does not depend on virus, the authors discuss potential mechanisms of PKR triggering. This is an interesting topic that deserves further investigation (not necessarily within the frame of this work - it can be a follow-up). Another interesting piece of information is that different truncated Dicers behave differently with respect to implementing antiviral RNAi. Whilst Dicer-N1 isn't proficient in doing so, the other forms are. It shows that lab-generated truncations do not fully recapitulate what is observed with existing truncated Dicers (DicerO and aviD).

Experimental design and data interpretation

1. The authors should compare infection between different cell lines across a range of time points (ie, a virus growth curve). In Fig 4E for example, I worry that cells expressing or not PKR will reach the plateau of viral particle accumulation at different time points. One could imagine that cells lacking PKR do not show any differences in particle production at 24h, but do at earlier time points.
2. Western blots should be accompanied with proper quantifications plotted as bar graph with biological replicates (p-PKR, p-eIF2a and capsid).
3. Microscopy images should be properly quantified across biological replicates (Fig 1&2 for the J2 staining, for example).
4. Confounding factors hinder the interpretation of siRNA accumulation (Suppl Fig 2): i) the efficiency of dsRNA dicing from different Dicers will generate different amounts of siRNAs from a given amount of dsRNA and ii) the higher antiviral response translates into decreased infection, so decreased dsRNA substrate. I suggest that the authors normalise the amount of viral siRNAs over the total amount of viral genomes. This should allow to assess if Dicer-N1 is better at dicing dsRNA than WT in these conditions.
5. In Fig 8, the authors should verify that phospho-p65 increase depends on PKR by repeating the experiment in PKR KO cells.

Data representation

1. Levels of phospho-PKR and eIF2a need to be normalised on the total amount of PKR and eIF2a, respectively. The authors should quantify the blots and present bar graphs with biological replicates and statistics.
2. Could the authors add the names of representative genes on the volcano plots of Fig 7?

Points of discussion

1. In Fig 4C, catalytically-dead mutants of truncated Dicers (other than N1) do not display an antiviral effect. Presumably, such proteins implement canonical antiviral RNAi. Is there a reason why the authors interpret this data as Dicers being "partially" antiviral through RNAi (l. 92). This data instead suggest that is it totally dependent on RNAi.
2. Gurung et al. demonstrate that PKR is activated in Dicer KO mouse ES cells, which results in phosphorylation of eIF2a at steady-state. This is different from the authors' data, in which PKR activation does not affect eiF2a phosphorylation. Could the authors discuss this discrepancy?
3. Do the authors expect that truncated Dicers other than N1 trigger an inflammatory response such as the one described for N1? Would it be possible to have this antiviral inflammatory response in conjunction with antiviral RNAi?

Significance

This is a study that conceptually advances the field of antiviral RNAi in mammals, including its interplay with the machinery of innate immunity. It is of interest for virologists and immunologists. My expertise is centered on the mechanisms of innate immunity in mammalian cells, including antiviral RNAi.

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Referee #2

Evidence, reproducibility and clarity

Summary

Whether RNAi is used as an antiviral mechanism in mammals has been a hotly debated issue. The research team previously published several papers on the roles of Dicer in siRNA/miRNA biogenesis and in antiviral responses. They have recently reported that the helicase domain of human Dicer specifically interacts with several proteins that are involved in the IFN response, including PKR. In this study, Baldaccini et al. investigated the involvement of Dicer in antiviral response using various mutants of human Dicer. They showed that deletion mutants of helicase domain exhibit antiviral activity that requires the presence of PKR. They further demonstrated that one of the mutants, N1-Dicer showed antiviral activity in an RNAi-independent manner but depending on the presence of either native PKR or kinase deficient mutants. Transcriptomic analysis revealed that numerous genes involved the IFN and inflammatory response were upregulated in the cells that express N1-Dicer, which is likely due to an increased activation of the NFκB pathway. Based on these findings, the authors propose that Dicer may act as antiviral molecule using its helicase domain, which representing a novel non-canonical function of Dicer.

Major comments:

1.The results from experiments with SARS-CoV2 are intriguing (Fig.2). The authors speculated that NFkb activation is in favor of the replication of this virus. It would be interesting to see the infection and replication of SARS-CoV2 in PKR deficient cells and cells expressing PKR mutants (as described in Fig.5). The results may prove/disapprove the authors' speculation and yield additional findings. 2. Western blot analysis. In the method section, it is stated that proteins were quantified with Bradford method and equal loading was verified by Ponceau S staining. The members of also probed with gamma-tubulin (It was stated that antibodies against alpha-tubulin was used in the method section) as a loading control, however, the bend intensity of tubulin shows great variations among different lanes in several figures while Ponceau S staining is similar (Fig.s, 4, 5, and 8). The differences compromise the accuracy of the results. 3.RNA-seq analysis revealed that Dicer N1 cells have significantly increased expression levels of signaling molecules in type I IFN response even in uninfected cells. While this provides a potential explanation for the antiviral phenotype of N1-Dicer cells. I wonder why the expression levels of type I IFNs (probably the most potent antiviral molecules) were not analyzed in WT and Dicer N1 cells. Measurement of the levels of IFNα and IFNβ by ELISA in the cells before and after infection could provide the important and direct data to support their conclusion. 4.While the data presented in Fig. 5 provides convincing evidences that the antiviral activity of mediated by PKR against SINV is independent of its kinase activity in N1-Dicer cells. An interesting question is that whether antiviral activity associated with PKR is N1-Dicer dependent,, which could be addressed by comparing the viral infection of NoDice∆PKR and NoDicer expressing PKR mutants. 5.In the concluding paragraph of the discussion, the authors presented an oversimplified discerption of a complex model that involves a crosstalk between IFN-I and RNAi and Dicer-PKR interaction, which is difficult for the reader to compose a clear picture of mechanisms involved. It could be helpful to use a schematic illustration to summarize the action model of PKR incorporated with the canonical and non-canonical Dicer functions.

Minor comments:

1.It stated that NoDice FHA-Dicer WT #4 and NoDice FHA:Dicer N1 110 #6 are referred to as Dicer WT and Dicer N1 cells (p.6). For simplicity, Dicer WT and Dicer N1 cells should be used throughout manuscript, including in all figures. The labels in the figures are difficult to read and are confusing in some cases. 2.It is to note that p-PKR was only detected at in N1-Dicer cells at 24 hpi (Fig.8A). This is an interesting observation that was not discussed. It appears that this could be due to a delayed viral replication since these cells are already in an elevated antiviral state. This possibility could be tested by examining viral replication and dsRNA accumulation at more time points in the experiments described in Fig.1. 3.The authors may point out the limitations of the studies. For examples, all cells used in the study are engineered HEK cell lines and were tested with limited number of viruses. As such, the observations may reflect Dicer-PKR interaction under artificially overexpressed conditions, but how the model established from the current study applies to primary cells require further investigation.

Significance

The findings reported in this study shed some new light on a long-debated issue regarding the potential roles of RNAi as physiologically relevant antiviral mechanism in mammals. Identification of a new antiviral function of Dicer helicase domain via interaction with PKR is a new advancement of the field, and it also adds a new dimension to a complex subject that overlaps of innate immunity , RNA biology, and developmental biology associated with Dicer.

Field of expertise: Innate immunity, cell signaling, cytokine biology

Areas that that I do not have sufficient expertise to evaluate: Small RNA cloning, sequencing and, analysis.

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Referee #1

Evidence, reproducibility and clarity

The study largely focuses on the use of a 293 cell line that lacks a functional Dicer gene originally identified by the Cullen group. Baldaccini use this cell line, referred to as NoDice cells, to reconstitute various Dicer isoforms that have thus far been described in a variety of settings (e.g., stem cells and oocytes). Collectively, these data demonstrate the capacity of certain N-terminal truncations of Dicer to inhibit Sindbis virus and reduce the presence of viral dsRNA, supporting some of the observations made thus far concerning an antiviral role for mammalian Dicer. For other viruses, this impact was significantly more modest (SFV reduction is less than a log) or was not observed at all (VSV and SARS-CoV-2). The authors then go on to characterize the nature of the observed antiviral activity and ultimately implicate PKR and the induction of NF-kB in priming the cell's antiviral defenses. Importantly, the group also found that this antiviral activity neither required the nuclease activity of Dicer nor the kinase activity of PKR - providing evidence against antiviral RNAi in mammals. In all, the data would seem to suggest that Dicer can act as a dsRNA sensor and can mediate the activation of an NF-kB response - akin to what is observed in response to NOD or some TLR engagement. In all, it is the opinion of this reviewer that this work brings additional clarity to a concept that remains controversial in the field and therefore embodies something meaningful for the community.

With that said, there are a few issues that require additional attention. The first of these is textual. The introduction of the paper accurately describes the evidence in support of mammalian RNAi but does not invest the same time in discussing the data to the contrary. For example, Seo et al demonstrated that virus infection results in poly-adp-ribosylation of RISC preventing RNAi activity (PMID: 24075860), Uhl et al showed that IFN-induced ADAR1 resolves dsRNA in the cell and prevents RNAi (PMID: 37017521), and Tsai et al showed that virus-derived small RNAs are not loaded into the RISC in a manner that would enable antiviral activity (PMID 29903832). None of this work is referenced in this manuscript and it generates an unbalanced introduction as it relates to the controversy surrounding the idea of RNAi in mammals.

The second issue that would further strengthen this paper relates to the fact that the authors spend a considerable amount of time discussing the data of Figure 6 and 7 as conditions that are defined by a Dicer that can not be processive in its nuclease activity (WT) vs. one that can (N1). However, there seems to be little consideration about the fact that the introduction of WT Dicer into these cells also restores miRNA biology whereas N1 appears to remain only partially functional (based on the data of Fig 3E). Given this, it seems the authors should verify that the high baseline of NFkB signaling that is being observed when comparing WT to N1 is not a product of restored miRNA function in WT cells, in contrast to the hypotheses outlined in the manuscript. This could be addressed by silencing Drosha or DGCR8 in the Dicer knockout cells prior to their reconstitution of Dicer. In the opinion of this reviewer, this experimental control would significantly strengthen the conclusions the authors are making here.

Significance

In the manuscript entitled, "Canonical and non-canonical contributions of human Dicer helicase domain in antiviral defense" Baldaccini et al. describe their findings concerning the ability of certain N-terminal deletion variants of Dicer in contributing to mammalian antiviral activity. The concept of a functional antiviral RNAi system in mammals is a contentious one with many publications including data both in support of its existence and opposing this idea. In this manuscript, Baldaccini et al. perform a wide range of well-controlled experiments to specifically address aspects of those reports to both provide clarity in what has been documented thus far and to expand on those concepts further.

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Reply to the reviewers

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

Authors used organoid technology to study the effects of the serum from lupus patients on intestinal epithelium. By culturing organoids derived from human colon crypts, they specifically determined the response of epithelial cells to inflammatory mediators present in lupus serum. Using bulk and scRNA-seq, authors found that secretory cells function and differentiation were impaired as well as the mitochondrial metabolism. These effects were shown to be mediated by type 1 interferon in combination with other pro-inflammatory cytokines present in lupus serum.

The reduction of mucus secretion after SLE-serum treatment and the downregulation of tight junctions' genes seem to indicate an increased permeability of the epithelial barrier, thus it would be interesting to determine the expression and distribution of tight junction proteins and to test in the organoids whether the paracellular permeability is increased upon SLE-serum treatment. These analyses will give a functional result of this in vitro model.

If the organoids take a few days to culture and the material is available, the measurement of paracellular permeability may take no more than 2 weeks. It is true that they will need a microneedle to inject the FITC-Dextran 4K into the organoids and record the images for 24h.

• We thank the reviewer for suggesting this experiment. Reviewer #2 had the same suggestion. The results obtained elevate our overall results and the quality of our research.
• Tight junction protein expression is cell-type dependent as shown in literature1,2 and in our scRNA-seq analysis (Suppl. Table 7). Additionally, we observed that the expression changes of ZO-1(TJP1; Fig. 7A) are accumulated in colonocytes. That might be the reason we could not detect significant changes in organoid sections with staining for tight junction proteins ZO-1 and Occludin and analyzing all cell types. The data of the permeability assay however was able to show that the function of the tight junctions is altered. If this change is caused by changes in protein abundance as suggested by reported transcriptomic changes remains to be elucidated in future research using single-cell proteomic approaches.

• For the permeability assay we stimulated organoid monolayers for 72h with SLE or control serum. The measured translocation of FITC showed an increased barrier leakiness in SLE compared to control condition. These functional results not only support our findings presented in our study that the epithelial barrier is altered upon SLE serum stimulation, but they also provide the definitive proof of concept highlighting the crucial connection between SLE and intestinal barrier integrity. Furthermore, it shows that changes on transcriptional level and alterations in cell type composition translate into a barrier dysfunction which could have potentially detrimental effects in vivo. The data has been added to Figure 1H, line 722-731; 746-751.

  I would like to know which of the donor's cells were used from figure 2 on and why.

• Organoid line I was used for the 24h stimulation and for the 72h stimulation whereas organoid line II was used for the 72h stimulation only. Due to limitations in serum availability we had to limit the experiments that exceeded the initial transcriptomic analysis to one organoid line. After confirming that the serum was affecting both organoid lines, we continued using organoid line II.

  The bioinformatics analyses using gene expression data and scRNASeq were well done. No comments.

  Reviewer #1 (Significance (Required)):

  For the field of autoimmunity, to study the crosstalk between the systemic response and the gut epithelium response results quite important as the increased permeability of the gut epithelial barrier has been suggested to fuel the systemic inflammation in lupus. However, as the author mention, there is not enough information about the interaction of epithelial cells and the systemic inflammatory mediators in lupus. This system can be useful to determine a personalized treatment for patients by testing the effect of individual serum on organoids. Moreover, the use of organoids can be extended to study the gut epithelium response in other autoimmune diseases mediated by type 1 interferon.

  Increased permeability of the gut epithelial barrier has been related with lupus development. In humans, it is not known whether it is a cause or consequence, but in lupus mouse models it has been demonstrated that there is a reduction of the systemic autoimmune response concomitant with a reduction of gut permeability. The authors have validated an in vitro model that can be used to study how gut epithelium is affected by systemic inflammatory mediators and that will help to develop novel therapeutic approaches or personalize treatments.

Thank you for your insightful comments. We are encouraged to see that the reviewer has accurately grasped the core purpose and implications of our research. The intricate relationship between gut epithelial barrier permeability and lupus development is indeed vital for expanding our scientific knowledge and for future therapeutic breakthroughs. We are happy that the overall message we aimed to convey with our research was well captured and appreciated by the reviewer. We believe our in vitro model will serve as a foundation for further detailed studies and for the development of therapeutic strategies in this field. Your acknowledgment of our work inspires us to persist in our research efforts.

Interest stakeholders: Clinical and basic researchers in autoimmunity, gastroenterology, and rheumatology.

My field of expertise is systemic and organ-specific autoimmunity at cellular and molecular level. My work covers autoimmunity and gut microbiota. I study how B cells regulate the microbiota composition and how that microbiota impacts gut permeability and inflammation in mouse lupus models. On the other hand, the bioinformatics analyses are well-done for both bulk RNASeq and scRNASeq.

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

The group of Dr. Resnik-Docampo provides a very elegant study on two patient lines for SLE. The study is definitely very interesting and opens many scientific avenues that are worthy of being explored further. Major comments: -Barrier integrity or its alterations can be tested in organoids with specific dyes, I feel this would give definitive proof of concept.

• We thank the reviewer for the suggestion. Reviewer #1 had the same suggestion. The results obtained elevate our overall results and the quality of our research.

• For the permeability assay we stimulated organoid monolayers for 72h with SLE or control serum. The measured translocation of FITC showed an increased barrier leakiness in SLE compared to control condition. These functional results not only support our findings presented in our study that the epithelial barrier is altered upon SLE serum stimulation, but they also provide the definitive proof of concept highlighting the crucial connection between SLE and intestinal barrier integrity. Furthermore, it shows that changes on transcriptional level and alterations in cell type composition translate into a barrier dysfunction which could have potentially detrimental effects in vivo. The data has been added to Figure 1H, line 722-731; 746-751.

  -In supplementary figure 1 a caspase 3 staining is presented, please show a positive control for caspase 3 staining on organoids or alternstively use a different method to prove no differential cell death.

• Due to the processing of the organoids it is difficult to have a positive control. However, we can confirm that the used cleaved Caspase 3 antibody is able to detect cell death by the following staining. There are positive cells in the center of the organoid where dead cells accumulate. Additionally in Figure 1C we show with a cytotoxicity assay measuring LDH release that there is no significant difference between both groups. Furthermore, brightfield imaging showed no obvious differences and the DEGs show also no evidence of increased cell death.

  -Serum from SLE patients reduces drastically Edu positivity, it would be interesting to see a clonogenicity assay to see whether this reflects on reduced stem cell clonogenic potential

• We agree. However, this analysis goes beyond the time and material limitations we have in our project.

  -Goblet cells in the colon are very heterogeneous, which subpopulations of goblet cell are reduced? how does this affect mucus composition?

• We see that subpopulation GC4 is significantly reduced upon SLE serum stimulation (Fig. 7C and Suppl. Fig. 7C). Overall, we see a trend of a general reduction of all GC subpopulation and an indication that there might be also a shift in subtype abundance. We would need to increase the study population to be able to draw any conclusions on how exactly the GC subpopulations change. So far not much is known about how the different GC subpopulations affect mucus composition. This field is completely understudied especially in the human intestine. Future projects should focus on mucus composition and how it is changed with changes of the subpopulations (even under physiological conditions).

• We thank the reviewer for the question about the mucus composition. We included the analysis of FCGBP protein abundance (Fig. 4C and Suppl. Fig. 4D; line 245-247) in our study. The increased FCGBP protein abundance upon SLE serum stimulation which is in line with our transcriptomic changes complements our data and supports our hypothesis that the mucus composition is altered. This new data improves the quality of our research.

  Minor comments: - Please provide an hypothesis on how mitochondrial alterations are linked to altered lineage progeny of stem cells. This should be discussed more in depth.

• It is known that cells in the crypt compartment that undergo rapid division depend on glycolysis for ATP production once the cell differentiates it switches to oxidative phosphorylation.3 In vitro it has been shown that differentiation coincides with the switch to oxidative phosphorylation.4 There is a complex interplay between Notch signaling and FoxO transcription factors which is driving differentiation and cell fate decision.5 Especially the differentiation towards the secretory lineage highly depends on the metabolic switch from glycolysis to oxidative phosphorylation. Furthermore, even mucus secretion itself is dependent on oxidative phosphorylation.6 This is in line with our differentiation experiment where less oxidative phosphorylation coincided with the absence of goblet cells. We hypothesize that the changed cellular composition upon SLE serum stimulation is at least partly reflected in the altered mitochondrial function. If the decrease in the secretory lineage alone can explain the seen mitochondrial changes needs to be further elucidated. While a detailed examination at single-cell level analysis of mitochondrial function might be able to answer if they drive the altered cell differentiation, such an in-depth analysis is beyond the scope of this article and would be best addressed in a dedicated study on the topic. Within the scope of our analysis and considering the still limited knowledge of mitochondrial function in specific cell types of the human colon we included some more discussion (line 696-698 and 702-703).

  -Many antimicrobial peptides are changed, this could reflect on microbiome composition as well as mucus composition and properties, which I am sure will be the topic of future studies. This should be discussed more in depth.

• We hypothesize that the alterations in antimicrobial peptide expression along with the seen changes in major mucus components would be translated into changes in mucus composition. Since the mucus serves as the niche for gut microbiota this could lead to changes in microbiome composition. It is of high interest to analyze the mucus composition of the stimulated organoids. Furthermore, assays analyzing the killing capacity of the potentially secreted antimicrobial peptides could help us to understand the relevance of the observed changes. We addressed this in line 714-715 and line 750-752.

  Reviewer #2 (Significance (Required)):

  The study is useful for both broad and specialized audiences. The findings are interesting and of relevance to the field of SLE, gut epithelial biology. The strength of the manuscript is that it opens many scientific avenues, its weakness is that they are not mechanistically dissected to the fullest rendering the study a bit descriptive. Nonetheless, I consider positively the manuscript after a minor revision given the major message of the paper can be proven.

Thank you for your constructive feedback. We are genuinely encouraged by your recognition of the utility and relevance of our study for both broad and specialized audiences in the fields of SLE and gut epithelial biology. Your acknowledgment resonates with our larger objectives: beyond merely exploring the specific connection between SLE and intestinal leakiness, our aim has been to create a methodological approach that illuminates novel avenues to study complex diseases. It is deeply heartening to realize that this overarching message and intent were clearly understood and agreed upon by the reviewer. We recognize and appreciate your insights into the strengths and areas for improvement of our manuscript, and we are committed to addressing the highlighted points to further enhance our contribution to the field.

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

Inga Viktoria Hensel et al. used colon organoid to study the impact of lupus patients' serum on gut epithelial barrier. The exposure of SLE serum on colon organoids increased gene expression related to cell cycle, chromosome organization, mitochondrial function as well as interferon signaling, but downregulated that related to secretion, cytoskeleton, and anchoring junctions of the cells. Higher type I IFN in the SLE serum and unregulated interferon signature genes post stimulation suggest a potential role of type I interferon in this process. The addition of a type 1 interferon receptor (IFNAR1) antagonist, Anifrolumab, blocked the stimulation function of SLE serum but the combination of IFN-2α and control serum failed to recapitulate the results from SLE serum, suggesting that more than one cytokine was involved. SLE serum exposure altered metabolic profiles of organoids with a significant increase of basal respiration and ATP production. Stimulating organoid with SLE serum confirmed an alteration in cell differentiation with a loss of secretory lineage. scRNA-seq analysis revealed that colon organoid had all major cell types from colon in vivo. SLE serum stimulation shifted cell differentiation with decreased number of goblet cells and downregulated mucin, AMP and other components that were required for gut barrier integrity.

Finally, the authors performed a gene expression analysis of colon biopsies derived from SLE patients and healthy controls. While the authors should be commended to attempt a validation of the results obtained with organoids, the small sample size and patient heterogeneity prevented a statistical analysis. Some genes involved in absorption and ion transport as well as secretory lineage showed a similar trend with organoid assay, suggesting that colon organoids may be a good tool for future studies. However, it is noticeable that the biopsies from SLE patients did not show the IFN signature and the decreased in Muc2 expression, which dominated the gene signature of organoids exposed to SLE serum. There is no information about the disease activity of the SLE patients, as well as their IFN activity, which makes difficult to interpret these results.

• We thank the reviewer for the questions and suggestions. They helped us to improve our manuscript and make it more concise for the reader.

Specific concerns: 1. Line 107, Why did The authors use 72 hours post treatment. Are other timepoints available and have similar results?

• We used two different time points, 24h and 72h. The nature of the organoid culture limits the total length of the experiment. Organoids can be cultured for a maximum of 5-7 days. Differentiation from the stem cell to the fully differentiated cell takes 5-7 days. Preliminary results showed that serum stimulation prior to day 2 led to a decrease in organoid survival, most likely because serum stimulation in general induces differentiation. We therefore chose 72h as the stimulation that mimics a chronic exposure as a differentiating cell would face in vivo. With this time span we were able to see manifestations in cell differentiation changes but avoided beginning cell death to prolonged culture. However, we also wanted to understand a more acute exposure to the serum. Therefore, we chose 24h as a second stimulation duration. With this time point we were able to detect initial changes in cell fate decision which was important in the interpretation of the accumulated effects seen after 72h.

Figure 1D, how do the authors explain the heterogeneity among SLE samples (2, 3, 4, 5) on organoid line II? These samples do not seem to correlate with cytokine levels shown in Fig. 2. This issue may be worth exploring further, such as correlation between cytokine levels and gene expression.

• The heterogeneity seen among the SLE samples most likely reflects the complex composition of the serum itself. A similar heterogeneity (PC1 axis) is also seen for the controls. The epithelial cells eventually will react to all contained factors showing an integrated response that makes it difficult to correlate to a single cytokine.

Line 144, the 2 outlier SLE serum samples are not same between organoid lines with NO. 1&5 in Organoid line II and with NO. 1&4 in Organoid line I. The statement is misleading.

• We corrected the statement according to the suggestions (Line 146-148).

Line 169, IFN-a2 and IL-6 are not significantly different.

• The statement was rephrased (Line 166-174).

Line 179-180, Reduced fitness of organoids exposed to SLE serum is an overstatement. It was not directly tested, and there is no difference in apoptosis.

• The term ‘reduced fitness’ referred to the results seen in the mitochondrial stress test. We rephrased the parts to make the statement more concise (Line 182).

Line 242-243: SLE serum stimulation induced MUC2 high expression in Organoid II but lower level in organoid I (Figure 4B & Figure S4C). This is a major discrepancy that needs to be addressed.

• This discrepancy comes from the different differentiation dynamics observed in both organoid lines. Therefore, for the downstream analysis we considered the results from both lines to have a robust analysis. With the results from the 24h timepoint and the scRNA-seq which were performed with either of the lineages respectively, we can be certain that the overall seen effect on the secretory lineage is a valid finding (we addressed this in line 229-232).

Line 251-252: How do authors make sure that "we were facing an effect on the differentiation process rather than cell type loss"?

• We can exclude an increase of cell death since we did not see changes in LDH release (Fig. 1C) and cleaved Caspase 3 abundance (Suppl. Fig. 1A) when we compared both conditions. Additionally, the data from the 24h stimulation time point showed the reduction of transcription factors (Fig. 4J) important for differentiation which manifested in a reduction of secretory cell markers upon longer stimulation (72h) (edited statement in line 256-258).

Line 259, How about apoptosis gene levels here?

• Apoptosis markers BAX and BCL2 are not amongst the differentially expressed genes. (see Suppl. Table 4).

Line 290 : It has been shown that the response of colon explants to IFN-α was variable among donors (https://www.sciencedirect.com/science/article/pii/S2352345X16301084#undfig1). This study should be cited. Was the response to IFNa tested on both organoids?

• The reference was included (Line 669-671). The response to IFNα was only tested in organoid line II given the limited availability of the serum that was used for co-stimulation. Overall, however, we saw an effect in both donor lines and less response was rather connected to the serum, not the organoid donor. In the publication reported interindividual heterogeneity depends on the therewith connected release of IL-18. Future studies could include analysis of cytokine release from the organoids after serum stimulation and a higher number of organoid lines to validate our findings.

Line 305-307: Is single cell sequencing from single organoid line or from combined? Do two organoid lines show different distributions?

• scRNA-seq was performed using organoid line II. Due to limited resources, we unfortunately could not include another organoid line.

  Reviewer #3 (Significance (Required)):

  While there is mounting evidence of an altered intestinal barrier integrity in SLE patients, there is little insights in the mechanisms. Using colon organoids is a novel approach with great potentials to investigate this issue. The strongest signature found by the authors was type IFN, which is indicates that the colon epithelial cells respond in a similar manner to other cell types. The secretory and absorption genes are of potential greater interest to unraveling mechanisms to gut alteration in SLE. This study is of interest for audiences interested in lupus basic and clinic research, as well as investigators working of gut barrier integrity.

Thank you for your constructive feedback. We are encouraged by your acknowledgment of our novel approach using colon organoids to explore the altered intestinal barrier integrity in SLE patients. Your emphasis on the significance of the type IFN signature and the importance of secretory and absorption genes aligns with our perspective.

Incorporating the intestinal barrier functional experiment emphasizes the translational nature of our study. We agree with your view that our findings are relevant for those involved in both basic and clinical lupus research, as well as specialists in intestinal biology. Your encouraging feedback strengthens our conviction in the wider significance of our work. We are motivated to keep bridging the gap between these two essential areas of study.

References

1. Pearce, S. C. et al. Marked differences in tight junction composition and macromolecular permeability among different intestinal cell types. BMC Biol. 16, 1–16 (2018).
2. Kishida, K., Pearce, S. C., Yu, S., Gao, N. & Ferraris, R. P. Nutrient sensing by absorptive and secretory progenies of small intestinal stem cells. Am. J. Physiol. Liver Physiol. 312, G592–G605 (2017).
3. Rath, E., Moschetta, A. & Haller, D. Mitochondrial function — gatekeeper of intestinal epithelial cell homeostasis. Nat. Rev. Gastroenterol. Hepatol. 15, 497–516 (2018).
4. Rodríguez-Colman, M. J. et al. Interplay between metabolic identities in the intestinal crypt supports stem cell function. Nature 543, 424–427 (2017).
5. Ludikhuize, M. C. et al. Mitochondria Define Intestinal Stem Cell Differentiation Downstream of a FOXO/Notch Axis. Cell Metab. 32, 889-900.e7 (2020).
6. Sünderhauf, A. et al. Loss of Mucosal p32/gC1qR/HABP1 Triggers Energy Deficiency and Impairs Goblet Cell Differentiation in Ulcerative Colitis. Cmgh 12, 229–250 (2021).

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Referee #3

Evidence, reproducibility and clarity

Inga Viktoria Hensel et al. used colon organoid to study the impact of lupus patients' serum on gut epithelial barrier. The exposure of SLE serum on colon organoids increased gene expression related to cell cycle, chromosome organization, mitochondrial function as well as interferon signaling, but downregulated that related to secretion, cytoskeleton, and anchoring junctions of the cells. Higher type I IFN in the SLE serum and unregulated interferon signature genes post stimulation suggest a potential role of type I interferon in this process. The addition of a type 1 interferon receptor (IFNAR1) antagonist, Anifrolumab, blocked the stimulation function of SLE serum but the combination of IFN-2α and control serum failed to recapitulate the results from SLE serum, suggesting that more than one cytokine was involved. SLE serum exposure altered metabolic profiles of organoids with a significant increase of basal respiration and ATP production. Stimulating organoid with SLE serum confirmed an alteration in cell differentiation with a loss of secretory lineage. scRNA-seq analysis revealed that colon organoid had all major cell types from colon in vivo. SLE serum stimulation shifted cell differentiation with decreased number of goblet cells and downregulated mucin, AMP and other components that were required for gut barrier integrity.

Finally, the authors performed a gene expression analysis of colon biopsies derived from SLE patients and healthy controls. While the authors should be commended to attempt a validation of the results obtained with organoids, the small sample size and patient heterogeneity prevented a statistical analysis. Some genes involved in absorption and ion transport as well as secretory lineage showed a similar trend with organoid assay, suggesting that colon organoids may be a good tool for future studies. However, it is noticeable that the biopsies from SLE patients did not show the IFN signature and the decreased in Muc2 expression, which dominated the gene signature of organoids exposed to SLE serum. There is no information about the disease activity of the SLE patients, as well as their IFN activity, which makes difficult to interpret these results.

Specific concerns:

1. Line 107, Why did The authors use 72 hours post treatment. Are other timepoints available and have similar results?
2. Figure 1D, how do the authors explain the heterogeneity among SLE samples (2, 3, 4, 5) on organoid line II? These samples do not seem to correlate with cytokine levels shown in Fig. 2. This issue may be worth exploring further, such as correlation between cytokine levels and gene expression.
3. Line 144, the 2 outlier SLE serum samples are not same between organoid lines with NO. 1&5 in Organoid line II and with NO. 1&4 in Organoid line I. The statement is misleading.
4. Line 169, IFN-a2 and IL-6 are not significantly different.
5. Line 179-180, Reduced fitness of organoids exposed to SLE serum is an overstatement. It was not directly tested, and there is no difference in apoptosis.
6. Line 242-243: SLE serum stimulation induced MUC2 high expression in Organoid II but lower level in organoid I (Figure 4B & Figure S4C). This is a major discrepancy that needs to be addressed.
7. Line 251-252: How do authors make sure that "we were facing an effect on the differentiation process rather than cell type loss"?
8. Line 259, How about apoptosis gene levels here?
9. Line 290 : It has been shown that the response of colon explants to IFN-α was variable among donors (https://www.sciencedirect.com/science/article/pii/S2352345X16301084#undfig1). This study should be cited. Was the response to IFNa tested on both organoids?
10. Line 305-307: Is single cell sequencing from single organoid line or from combined? Do two organoid lines show different distributions?

Significance

While there is mounting evidence of an altered intestinal barrier integrity in SLE patients, there is little insights in the mechanisms. Using colon organoids is a novel approach with great potentials to investigate this issue. The strongest signature found by the authors was type IFN, which is indicates that the colon epithelial cells respond in a similar manner to other cell types. The secretory and absorption genes are of potential greater interest to unraveling mechanisms to gut alteration in SLE. This study is of interest for audiences interested in lupus basic and clinic research, as well as investigators working of gut barrier integrity.

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Referee #2

Evidence, reproducibility and clarity

The group of Dr. Resnik-Docampo provides a very elegant study on two patient lines for SLE. The study is definitely very interesting and opens many scientific avenues that are worthy of being explored further.

Major comments:

• Barrier integrity or its alterations can be tested in organoids with specific dyes, I feel this would give definitive proof of concept.
• In supplementary figure 1 a caspase 3 staining is presented, please show a positive control for caspase 3 staining on organoids or alternstively use a different method to prove no differential cell death.
• Serum from SLE patients reduces drastically Edu positivity, it would be interesting to see a clonogenicity assay to see whether this reflects on reduced stem cell clonogenic potential
• Goblet cells in the colon are very heterogeneous, which subpopulations of goblet cell are reduced? how does this affect mucus composition?

Minor comments:

• Please provide an hypothesis on how mitochondrial alterations are linked to altered lineage progeny of stem cells. This should be discussed more in depth.
• Many antimicrobial peptides are changed, this could reflect on microbiome composition as well as mucus composition and properties, which I am sure will be the topic of future studies. This should be discussed more in depth.

Significance

The study is useful for both broad and specialised audiences. The findings are interesting and of relevance to the field of SLE, gut epithelial biology. The strength of the manuscript is that it opens many scientific avenues, its weakness is that they are not mechanistically dissected to the fullest rendering the study a bit descriptive. Nonetheless, I consider positively the manuscript after a minor revision given the major message of the paper can be proven.

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Referee #1

Evidence, reproducibility and clarity

Authors used organoid technology to study the effects of the serum from lupus patients on intestinal epithelium. By culturing organoids derived from human colon crypts, they specifically determined the response of epithelial cells to inflammatory mediators present in lupus serum. Using bulk and scRNA-seq, authors found that secretory cells function and differentiation were impaired as well as the mitochondrial metabolism. These effects were shown to be mediated by type 1 interferon in combination with other pro-inflammatory cytokines present in lupus serum.

The reduction of mucus secretion after SLE-serum treatment and the downregulation of tight junctions' genes seem to indicate an increased permeability of the epithelial barrier, thus it would be interesting to determine the expression and distribution of tight junction proteins and to test in the organoids whether the paracellular permeability is increased upon SLE-serum treatment. These analyses will give a functional result of this in vitro model.

If the organoids take a few days to culture and the material is available, the measurement of paracellular permeability may take no more than 2 weeks. It is true that they will need a microneedle to inject the FITC-Dextran 4K into the organoids and record the images for 24h.

I would like to know which of the donor's cells were used from figure 2 on and why.

The bioinformatics analyses using gene expression data and scRNASeq were well done. No comments.

Significance

For the field of autoimmunity, to study the crosstalk between the systemic response and the gut epithelium response results quite important as the increased permeability of the gut epithelial barrier has been suggested to fuel the systemic inflammation in lupus. However, as the author mention, there is not enough information about the interaction of epithelial cells and the systemic inflammatory mediators in lupus. This system can be useful to determine a personalized treatment for patients by testing the effect of individual serum on organoids. Moreover, the use of organoids can be extended to study the gut epithelium response in other autoimmune diseases mediated by type 1 interferon.

Increased permeability of the gut epithelial barrier has been related with lupus development. In humans, it is not known whether it is a cause or consequence, but in lupus mouse models it has been demonstrated that there is a reduction of the systemic autoimmune response concomitant with a reduction of gut permeability. The authors have validated an in vitro model that can be used to study how gut epithelium is affected by systemic inflammatory mediators and that will help to develop novel therapeutic approaches or personalize treatments.

Interest stakeholders: Clinical and basic researchers in autoimmunity, gastroenterology, and rheumatology.

My field of expertise is systemic and organ-specific autoimmunity at cellular and molecular level. My work covers autoimmunity and gut microbiota. I study how B cells regulate the microbiota composition and how that microbiota impacts gut permeability and inflammation in mouse lupus models. On the other hand, the bioinformatics analyses are well-done for both bulk RNASeq and scRNASeq.

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Reply to the reviewers

We thank the reviewers to appreciating the depth and quality of the results presented in our manuscript. We are happy that he/she has appreciated our contemporary approach to addressing an important problem but also a thorny and debated topic in the field that has lasted for over 30 years since it was first proposed by Mike Berridge. Our work not only addresses mechanisms in cultured human cells but also for the very first time addresses the key problem of Li action in the human brain using human iPSC derived forebrain cortical neurons.

We are delighted with the reviewer’s comment that “This effort highlighted the author's commendable goal to develop a thoughtful story and not just another publication.” We thank the reviewer for appreciating our detailed multi-disciplinary approach to addressing a long standing (> 4 decades) problem of key significance in human psychiatry and neuroscience. We thank him/her for noting that the work deserves to be presented in a journal with a cross-disciplinary focus. A few technical points that have been noted by the reviewer have been addressed below. Most of these can be effectively addressed by modest rewriting of text to make certain points clearer. The one experiment that has been suggested can be done and will be completed within 1 month.

1. Description of the planned revisions

Reviewer #1 (Evidence, reproducibility and clarity):

The authors functionally define in the inositol monophosphate phosphatase IMPA1, as the true target of lithium regulating phosphatidylinositol turnover and calcium signalling. While the observed IMPA1 inhibition by lithium led to the historical 'inositol depletion hypothesis' over the past 30+ years were published evidence both in support and against this concept. These contradictory sets of results have led to decreased interest in phosphoinositides as the signalling pathway affected by the therapeutic action of lithium in bipolar disorder (BD) patients. The remarkable results shown here will revert this trend since the data clearly demonstrate a key role of IMPA1 in setting the rate of phosphatidylinositol turnover, and consequentially the extent of calcium signalling. While the data are consistent with the 'inositol depletion hypothesis' the authors do not prove or disprove the validity of this hypothesis since the actual levels of inositol were not measured in their experiments. However, this is not a criticism, since quantifying cellular inositol is complex, it is just a suggestion for future work. After clarifying the points listed below this work will be suitable for publication.

• The experiments using inositol rich DMEM (reported on page 17 and in Fig 2I,J) require a better explanation and an adequate material and method section. It is not clear if the 'normal/control' condition uses inositol-free DMEM. The standard concentration of inositol in DMEM is 40uM. Thus, are the ~155uM (28 mg/litre) added by the authors at the high end of the 40uM? Given that FBS contains inositol have the authors used dialyzed serum? While adding 155uM of inositol on either inositol-free medium or to medium containing 40uM inositol does not alter the author's message, this technical information are important for the reproducibility of the data presented and to understand how HEK293T manages inositol homeostasis.

The standard concentration of inositol in DMEM high Glucose media (Dulbecco’s Modified Eagle Medium; Life Technologies) is 40 µM (7 mg/ litre) and our HEK293T cells were maintained under standard conditions at (37oC, with 5% CO2) in this media, supplemented with 10% Foetal bovine serum (FBS). This FBS was not dialyzed, so it might contain trace amounts of inositol.

For our inositol rich DMEM, 117 μl of 100 μM of inositol (18 mg/ml) was added to 100 ml of DMEM high Glucose media, supplemented with 10% FBS- this led to the final effective concentration of inositol in the media ~155 µM (28 mg/ litre). This media was referred to as the inositol rich media and used for the inositol supplementation in Fig. 2I-J.

Therefore, the inositol supplementation we refer to is effectively raising the extracellular inositol concentration from ca. 40mm to 155mM which is 3X elevation. This information has been added to the results section.

• It would be helpful to know if store operated calcium entry is altered in impa1-/--M1 cells. This information would nicely complement Fig.3 C-E data.

We have studied store operated calcium entry in IMPA1-/- cells and it is decreased. The quantification of this reduction can be added to the paper.

• In the Introduction at the end of page 4, the evidence not supporting the inositol depletion hypothesis is correctly discussed. This section lacks the discussion of another work questioning this theory (PMID: 30171184). The conclusion of this work is also in agreement with the authors finding that lithium affects the rare/turnover (lines 490/506) of PIP2 synthesis.

Saiardi A, Mudge AW. Lithium and fluoxetine regulate the rate of phosphoinositide synthesis in neurons: a new view of their mechanisms of action in bipolar disorder. Transl Psychiatry. 2018 Aug 31;8(1):175. doi: 10.1038/s41398-018-0235-2. PMID: 30171184.

This paper suggests that lithium mediated inhibition of IMPase leads to an accumulation of IP1 and this elevated IP1 leads to a competitive inhibition of the rate of synthesis of PI, and hence turnover of PIP2. Combined with lithium’s inhibition of inositol uptake, this inhibition of PI synthesis can lead to the mood stabilizing effect of lithium, rather than the inositol depletion. This point will be added to our manuscript and the reference cited.

• In the material and methods, Liquid Chromatography Mass spectrometry is abbreviated to LCMS while in the main text (line 493) LC-MS is used. The dashed version should be used throughout the manuscript.

Liquid Chromatography Mass spectrometry will be abbreviated to LC-MS throughout the text in the revised version.

• I suggest to define (line 500) phosphatidylinositol 4-phosphate as (PI(4)P simplified as PIP). This will be consistent with the phosphatidylinositol 4,5-bisphosphate abbreviation as (PIP2) as reported in the introduction (line 97)

PIP refers to all the functional isoforms of Phosphatidylinositol phosphate- PI 3P, PI 4P and PI 5P. By the LC-MS/MS analysis, we had measured the total PIP masses but we cannot distinguish between the individual functional isomers of PIP. However, pre-existing literature suggests that PI 4P is the most abundant isoform of PIP present in cell- its level is approximately 50 folds higher than that of PI 5P (Rameh et al., 1997). Hence we can suggest that the change in the total mass of PIP (as seen by the LC-MS/MS) is mainly reflective of the PI 4P.

• Line 646: Instead of using [this study] the authors should refer to the Figure panels supporting the discussed argument.

The identity of the channels mediating Ca2+ transients in this system was shown by us in Sharma et al., 2020. In the revision, we will cite this paper.

Referees cross-commenting

Reviewer #2 main message is identical to my. The work is a "contemporary re-evaluation of the inositol depletion hypothesis" but it does settle the debate. Say that reviewer #2 also recognises the importance of the work in defining IMPA1 as the only lithium target affecting the PI cycle removing GSK3 from the picture. Additionally, we agree that the thorough transcriptional analysis of the effect of lithium on human cortical neurons will be very informative for any researcher interested in psychiatric disorders.

Reviewer #2 requests are rational and not demanding. Most queries require extra information or the reformatting of the data presented.

Reviewer #1 (Significance):

The submitted manuscript addresses an important topic. The authors developed HEK293 stable expressing muscarinic receptor to study the effect of lithium (without or after receptor activation) on PI(4,5)P2 turnover using two approaches, by microscopy and biochemically by LC-MS. These analyses were followed by a thorough characterization of the effect of lithium on calcium signalling. The generation of HEK293 impa1-/- line has allowed the authors to demonstrate that the observed effect of lithium on PI(4,5)P2 turnover and calcium signalling were IMPA1 dependent. The authors pushed the work to a higher level by studying the effect of lithium on iPSC-derived human cortical neurons demonstrating that lithium reduces neurons excitability and calcium signalling. Although previously published attempts failed to generate IMPA1 deficient human cortical neurons the authors managed to produce iPSC impa1-/- but, as reported and consistent with previous literature, this cell line failed to differentiate into neurons. This effort highlighted the author's commendable goal to develop a thoughtful story and not just another publication. The work is complemented by a very informative transcriptional analysis characterising the effect of lithium on human cortical neurons. Noteworthy is also the author's efforts to functionally and transcriptionally define the effect of another lithium target, GSK-3. These experiments emphasize that GSK-3 does not phenocopy the effect of lithium. This is another utterly important message of the paper.

In conclusion, the authors presented an easily readable, comprehensive, and experimentally convincing story. Furthermore, the developed experimental tools (HEK293-m1AchR) and the extensive data set (transcriptomic analysis) will be instrumental to further studies aimed at elucidating mechanistically how phosphoinositide signalling affects BD pathophysiology.

Reviewer #2 (Evidence, reproducibility and clarity):

This manuscript seeks to test if inhibition of the phosphoinositide (PI) cycle is the relevant pathway targeted by lithium in bipolar affective disorder (BPAD). Firstly, a cultured model system (HEK293T) is used to test the effects of lithium on the PI cycle. Using PI(4,5)P2 probes along with mass spectrometry, Li is shown to inhibit PI(4,5)P2 re-synthesis after PLC activation, though not to perturb pre-stimulus levels. Release of calcium from intracellular stores along with refilling from extracellular calcium is also inhibited - though there are no effects on stored calcium capacity. Crucially, with the exception of the calcium refilling step, these effects if Li can be abolished by genetic ablation of IMPA1, the proposed molecular target of Li. Having established the affected pathway, the manuscript then studies the effects of Li treatment on iPSC-differentiated cultured cortical neurons. Spontaneous and muscarinic evoked calcium transients are shown to be abolished by Li. None of these effects in HEK293T or neurons can be recapitulated by an inhibitor of GSK3beta, another proposed target for Li. Finally, a transcriptomic analysis of Li treated neurons is presented, showing down regulation of relevant genes, especially genes involved in neuronal calcium signaling and glutamatergic signaling.

The inositol depletion hypothesis has been debated for nearly four decades. As it stands, this manuscript does not settle this debate once and for all, but it does add some novel and important insights: that 1) IMPA1 is certainly the target of lithium, at least in terms of the PI cycle and 2) Lithium treatment can lead to longer-term transcriptional changes in neuronal calcium and glutamatergic signaling that can dampen excitability. The paper is on the whole clearly written, and the data are easy to follow. That said, there are a number of areas where the manuscript is lacking key details, or where the results do not fully support the conclusions. Specific suggestions for amendment are as follows:

(1) The PH-PLCdetla1 PH domain has been used to follow PI(4,5)P2 turnover in HEK293T cells. Although long established, the manuscript does not discuss the fact that this domain also binds to IP3, which given high enough concentrations, can compete the PH domain off the membrane. As such, what is being measured is the convolution of PI(4,5)P2 decreases and IP3 increases (see for example doi: 10.1083/jcb.200301070 ). Ideally, a non-IP3 binding probe would have been used, such as the Tubby c-terminal domain (doi: 10.1186/1471-2121-10-67; doi: 10.1113/jphysiol.2008.153791). As it stands, the failure of the PH domain to return to the membrane after Li treatment reported in figures 1G, 3F and 3L could either be due to a failure of PI(4,5)P2 re-synthesis, or a failure to breakdown IP3 - either of which are plausible explanations given inhibition of IMPA1. This concern is somewhat mitigated by the inclusion of mass determinations of the lipids in figure 1H-J, which support the PI(4,5)P2 re-synthesis defect. However, the potential problems with interpretation of the data with the PH domain should be discussed.

PH-PLCδ-GFP probe is used in the field as a biosensor for PI 4,5-P2 (Chakrabarti et al., 2015; Várnai and Balla, 1998) and has been used to monitor the PIP2 turn-over rate. However, as the reviewer has pointed out, this probe also has an affinity towards IP3 (Xu et al., 2003) and therefore the failure of the probe to return to the plasma membrane could also, in principle, reflect the accumulation of IP3.

We are well aware of this discussion in the field and to make sure that our measurements using the PH-PLCδ-GFP probe are indeed a true reflection of PIP2 re-synthesis , we have also used a biochemical method to establish the levels of PIP2. Our measurements of the total mass of PIP2 by LC-MS/MS corroborate our findings using the probe, on the delay in PIP2 resynthesis. Nonetheless, we will explicitly mention this point in the discussion.

Drawback of the Tubby c-terminal domain-

Most of the biosensors for PI 4,5-P2 have distinctive advantage and disadvantages- PH-PLCδ-GFP probe is a more sensitive reporter but its IP3 binding may compromise its accuracy to measure PI 4,5-P2 changes. However, the Tubby c-terminal domain has exhibited lower sensitivity to report on changes of PI 4,5-P2 during PLC activation, although being more specific in its affinity towards PI 4,5-P2 (Szentpetery et al., 2009). Furthermore, recent studies have revealed that Tubby c-terminal domain can also bind to PI 3,4-P2 as well as PI 3,4,5-P3 (Hammond and Balla, 2015). Lastly a very recent study has noted that in contrast to PH-PLCδ-GFP probe, the tubby domain binds selectively to certain domains of the plasma membrane at membrane contact sites making it not a detector of PIP2 levels across the plasma membrane (Thallmir et,al., 2023, PMCID: PMC10445746 DOI: 10.1242/jcs.260848 ).

(2) The strongest evidence for the effects of IMPA1 inhibition coming from inositol depletion are given by the experiment reported in figure 2I and J, where inositol supplementation rescues calcium mobilization. This should also be performed for the PIP2 re-synthesis experiments.

We thank the reviewer for this suggestion.

We will perform this experiment and add the results to the revised manuscript. Duration estimated for this experiment- 30 days.

(3) It is implicit in the manuscript that DMEM does not contain inositol. This is not true; Life technologies' formulation for DMEM contains 40 micromol/l myo-inositol, which is sufficient to support activity of both proton/myo-inositol and sodium/myo-inositol symporters (HMIT and SMIT). On the face of it, therefore, inositol depletion seems unlikely. The reviewer wonders what concentration of added inositol mediated the rescue? This key fact is missing from the manuscript. At the very least, the details should be included and the reason for rescue of already inositol replete cells discussed. Ideally, the key experiments would be repeated with inositol-free medium and supplementation.

Repeated cycles of GPCR linked PLC signalling depend on a stable and on a continuous supply of PIP2 at the cell membrane, which in turn depends on the cytoplasmic pool of inositol in the cell. Inositol pool can be maintained by three avenues- via the recycling of the inositol by the stepwise dephosphorylation of IP3, de novo synthesis of inositol from glucose 6-phosphate and the transport of inositol from the extracellular environment across the plasma membrane. Li inhibits IMPase, an enzyme that dephosphorylates inositol monophosphate to generate free inositol.

Due to Li’s inhibition of IMPase, the inositol pool cannot be regenerated by the first two avenues since both of them need IMPase. However, restriction of the inositol pool by Li’s inhibition of IMPase can be bypassed by the transport of inositol from the extracellular media via SMIT (Sodium-dependent myo-inositol co-transporter) and/or HMIT (Proton-dependent myo-inositol co-transporter). At steady state, the low amount of inositol in the DMEM media (the inositol concentration in normal DMEM media being approximately 7 mg/litre or 40 µM) might be sufficient for maintaining the inositol pool and thereby PIP2 levels at the steady state. But this amount of inositol in the DMEM media appeared to be limiting to sustain the inositol pool and thereby PIP2 levels under conditions of hyperactivated PIP2 cycle. This is likely the reason why Li mediated inositol depletion (by inhibition of IMPA1) leads to a decreased rate of PIP2 synthesis at the plasma membrane as well as decreased PLC mediated Ca2+ release, in the background of activated PLC.

However, when the cells were grown in an inositol rich DMEM media (inositol concentration is ca. 28 mg/litre or approximately 155 µM; which is similar to the inositol concentration in the cerebrospinal fluid (Swahn, 1985; Shetty et al., 1996)); transport of extracellular inositol by SMIT/HMIT could sustain a continuous level of PIP2 levels even in a PLC activated background. This explains the rescue of the decreased PLC mediated Ca2+ release phenotype in the control-M1 cells grown in inositol supplemented DMEM despite the Li treatment.

This section can be added to the Results section (page 17) in the revised version.

(4) The introduction refers to lithium as a "non-competitive" inhibitor of IMPA1. This is erroneous, as lithium is in fact an uncompetitive inhibitor. This is a key distinction: since the uncompetitive inhibitor blocks the enzyme:substrate complex, it is most effective where substrate accumulates the most - in this context, sites of intense PLC activity. This was central to Berridge's inositol depletion hypothesis. Also, the Allison et al citation is incorrect here. The correct citation is PMID: 2833231.

Li inhibits IMPA1 in an uncompetitive manner.

This will be corrected in the revised version of the manuscript, with the appropriate references.

Ref cited by reviewer- Gee NS, Ragan CI, Watling KJ, Aspley S, Jackson RG, Reid GG, Gani D, Shute JK. The purification and properties of myo-inositol monophosphatase from bovine brain. Biochem J. 1988 Feb 1;249(3):883-9. doi: 10.1042/bj2490883. PMID: 2833231; PMCID: PMC1148789.

Ref- Hallcher LM, Sherman WR. The effects of lithium ion and other agents on the activity of myo-inositol-1-phosphatase from bovine brain. J Biol Chem. 1980 Nov 25;255(22):10896-901. PMID: 6253491.

(5) other key experimental details are missing from the figures/figure legends/results and or methods. Namely, what concentration of carbachol was used? What was the optimum concentration of thapsigargin? For figure 2 B-C, was carbachol used to evoke calcium mobilization?

For the agonist mediated Ca2+ release, 20 µM of carbachol was used. This is mentioned in the Materials and Methods section (line 238); however, we will mention this in the figure legends and results for clarity, in the revised version.

For the store depletion in the SOCE experiments, 10 µM of thapsigargin was used. This is mentioned in the Materials and Methods section (line 249); however, we will mention this in the figure legends and results for clarity.

In Fig. 2B, C, Carbachol was used to evoke calcium mobilization in the cells. This is mentioned in the Results section (line 510)- we will mention this in the figure legends for clarity.

(6) The effects of IMPA1 knockout and rescue in figure 3F are rather unconvincing. All treatment groups' means fall within 1 SD; are the changes statistically significant? Plotting 95% C.I. or standard error may be more informative for these experiments.

This can be addressed in the revised version.

Minor comments:

() There are some inconsistencies in the figure panels. Arrows labelled "CCh" are used to denote CCh addition in e.g. Fig. 3D, whereas simple arrows are used elsewhere e.g. Fig. 3F or no arrow at all e.g. Fig. 3B.

All the points where CCh has been added to stimulate PLC will be denoted with an arrow labelled Cch for clarity and consistency. This will be addressed in the revised version.

() Details of what the error denotes is missing in Figs. 2B-C, 3B-C, F - as is N for 3A.

Whiskers in box plots show the minimum and maximum values with a line at the median. This will be addressed in the revised version.

() Fig. 2D: It should be made explicit that arrows indicate TTX addition in the figure. More importantly, it should be clarified whether this is also the case for Fig. 5D? Transients do not appear to be depleted by this addition.

This has been mentioned in the figure legends for the figure (line 1077)- we will address this in the revised version.

Few of the neuronal transients are not abolished by TTX- this variability can be addressed by other representative traces.

() In figure 6C, it is stated that "there was no down regulation in transcripts for SCN1A (Nav1.1) or SCN9A (Nav7.1)" but this is not strictly true from the data; the Li-treated cells definitely trend lower. The effect is clearly not statistically significant, so although it is not possible to state that they reduced, this is not the same thing as being able to assert that they are not reduced. Perhaps it could be more helpful to plot the size of the reduction between these transcripts?

This will be addressed as- “there was no significant downregulation in transcripts for SCN1A (Nav1.1) or SCN9A (Nav7.1)".

The difference in the transcript level for SCN1A (Nav1.1) or SCN9A (Nav7.1) can be plotted for further clarification.

Reviewer #2 (Significance):

The manuscript is ultimately a contemporary re-evaluation of the inositol depletion hypothesis for Li treatment of BPAD, first proposed by Berridge in 1989. The manuscript certainly does not end the debate - other pathways and mechanisms for lithium's actions on a complex human behavioral phenotype will surely persist. However, it does add some important new insights: firstly, that IMPA1 is certainly the target mediating the effects of Li on the PI cycle; and secondly, that long-term, Li may exert effects at the transcriptional level to down regulate calcium and glutamatergic signaling in the brain. However, there is no mechanism presented to link these two findings. The work is therefore of interest to researchers with an interest on studying psychiatric disorders, basic mechanisms of neuronal excitability as well as molecular mechanisms of cell signaling. It therefore deserves to be published in a journal with a cross disciplinary focus.

2. 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.

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

Nil

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Referee #2

Evidence, reproducibility and clarity

This manuscript seeks to test if inhibition of the phosphoinositide (PI) cycle is the relevant pathway targeted by lithium in bipolar affective disorder (BPAD). Firstly, a cultured model system (HEK293T) is used to test the effects of lithium on the PI cycle. Using PI(4,5)P2 probes along with mass spectrometry, Li is shown to inhibit PI(4,5)P2 re-synthesis after PLC activation, though not to perturb pre-stimulus levels. Release of calcium from intracellular stores along with refilling from extracellular calcium is also inhibited - though there are no effects on stored calcium capacity. Crucially, with the exception of the calcium refilling step, these effects if Li can be abolished by genetic ablation of IMPA1, the proposed molecular target of Li. Having established the affected pathway, the manuscript then studies the effects of Li treatment on iPSC-differentiated cultured cortical neurons. Spontaneous and muscarinic evoked calcium transients are shown to be abolished by Li. None of these effects in HEK293T or neurons can be recapitulated by an inhibitor of GSK3beta, another proposed target for Li. Finally, a transcriptomic analysis of Li treated neurons is presented, showing down regulation of relevant genes, especially genes involved in neuronal calcium signaling and glutamatergic signaling.

The inositol depletion hypothesis has been debated for nearly four decades. As it stands, this manuscript does not settle this debate once and for all, but it does add some novel and important insights: that 1) IMPA1 is certainly the target of lithium, at least in terms of the PI cycle and 2) Lithium treatment can lead to longer-term transcriptional changes in neuronal calcium and glutamatergic signaling that can dampen excitability. The paper is on the whole clearly written, and the data are easy to follow. That said, there are a number of areas where the manuscript is lacking key details, or where the results do not fully support the conclusions. Specific suggestions for amendment are as follows:

1. The PH-PLCdetla1 PH domain has been used to follow PI(4,5)P2 turnover in HEK293T cells. Although long established, the manuscript does not discuss the fact that this domain also binds to IP3, which given high enough concentrations, can compete the PH domain off the membrane. As such, what is being measured is the convolution of PI(4,5)P2 decreases and IP3 increases (see for example doi: 10.1083/jcb.200301070 ). Ideally, a non-IP3 binding probe would have been used, such as the Tubby c-terminal domain (doi: 10.1186/1471-2121-10-67; doi: 10.1113/jphysiol.2008.153791). As it stands, the failure of the PH domain to return to the membrane after Li treatment reported in figures 1G, 3F and 3L could either be due to a failure of PI(4,5)P2 re-synthesis, or a failure to breakdown IP3 - either of which are plausible explanations given inhibition of IMPA1. This concern is somewhat mitigated by the inclusion of mass determinations of the lipids in figure 1H-J, which support the PI(4,5)P2 re-synthesis defect. However, the potential problems with interpretation of the data with the PH domain should be discussed.
2. The strongest evidence for the effects of IMPA1 inhibition coming from inositol depletion are given by the experiment reported in figure 2I and J, where inositol supplementation rescues calcium mobilization. This should also be performed for the PIP2 re-synthesis experiments.
3. It is implicit in the manuscript that DMEM does not contain inositol. This is not true; Life technologies' formulation for DMEM contains 40 micromol/l myo-inositol, which is sufficient to support activity of both proton/myo-inositol and sodium/myo-inositol symporters (HMIT and SMIT). On the face of it, therefore, inositol depletion seems unlikely. The reviewer wonders what concentration of added inositol mediated the rescue? This key fact is missing from the manuscript. At the very least, the details should be included and the reason for rescue of already inositol replete cells discussed. Ideally, the key experiments would be repeated with inositol-free medium and supplementation.
4. The introduction refers to lithium as a "non-competitive" inhibitor of IMPA1. This is erroneous, as lithium is in fact an uncompetitive inhibitor. This is a key distinction: since the uncompetitive inhibitor blocks the enzyme:substrate complex, it is most effective where substrate accumulates the most - in this context, sites of intense PLC activity. This was central to Berridge's inositol depletion hypothesis. Also, the Allison et al citation is incorrect here. The correct citation is PMID: 2833231.
5. other key experimental details are missing from the figures/figure legends/results and or methods. Namely, what concentration of carbachol was used? What was the optimum concentration of thapsigargin? For figure 2 B-C, was carbachol used to evoke calcium mobilization?
6. The effects of IMPA1 knockout and rescue in figure 3F are rather unconvincing. All treatment groups' means fall within 1 SD; are the changes statistically significant? Plotting 95% C.I. or standard error may be more informative for these experiments.

Minor comments:

• There are some inconsistencies in the figure panels. Arrows labelled "CCh" are used to denote CCh addition in e.g. Fig. 3D, whereas simple arrows are used elsewhere e.g. Fig. 3F or no arrow at all e.g. Fig. 3B.
• Details of what the error denotes is missing in Figs. 2B-C, 3B-C, F - as is N for 3A.
• Fig. 2D: It should be made explicit that arrows indicate TTX addition in the figure. More importantly, it should be clarified whether this is also the case for Fig. 5D? Transients do not appear to be depleted by this addition.
• In figure 6C, it is stated that "there was no down regulation in transcripts for SCN1A (Nav1.1) or SCN9A (Nav7.1)" but this is not strictly true from the data; the Li-treated cells definitely trend lower. The effect is clearly not statistically significant, so although it is not possible to state that they reduced, this is not the same thing as being able to assert that they are not reduced. Perhaps it could be more helpful to plot the size of the reduction between these transcripts?

Significance

The manuscript is ultimately a contemporary re-evaluation of the inositol depletion hypothesis for Li treatment of BPAD, first proposed by Berridge in 1989. The manuscript certainly does not end the debate - other pathways and mechanisms for lithium's actions on a complex human behavioral phenotype will surely persist. However, it does add some important new insights: firstly, that IMPA1 is certainly the target mediating the effects of Li on the PI cycle; and secondly, that long-term, Li may exert effects at the transcriptional level to down regulate calcium and glutamatergic signaling in the brain. However, there is no mechanism presented to link these two findings. The work is therefore of interest to researchers with an interest on studying psychiatric disorders, basic mechanisms of neuronal excitability as well as molecular mechanisms of cell signaling. It therefore deserves to be published in a journal with a cross disciplinary focus.

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Referee #1

Evidence, reproducibility and clarity

The authors functionally define in the inositol monophosphate phosphatase IMPA1, as the true target of lithium regulating phosphatidylinositol turnover and calcium signalling. While the observed IMPA1 inhibition by lithium led to the historical 'inositol depletion hypothesis' over the past 30+ years were published evidence both in support and against this concept. These contradictory sets of results have led to decreased interest in phosphoinositides as the signalling pathway affected by the therapeutic action of lithium in bipolar disorder (BD) patients. The remarkable results shown here will revert this trend since the data clearly demonstrate a key role of IMPA1 in setting the rate of phosphatidylinositol turnover, and consequentially the extent of calcium signalling. While the data are consistent with the 'inositol depletion hypothesis' the authors do not prove or disprove the validity of this hypothesis since the actual levels of inositol were not measured in their experiments. However, this is not a criticism, since quantifying cellular inositol is complex, it is just a suggestion for future work. After clarifying the points listed below this work will be suitable for publication.

The experiments using inositol rich DMEM (reported on page 17 and in Fig 2I,J) require a better explanation and an adequate material and method section. It is not clear if the 'normal/control' condition uses inositol-free DMEM. The standard concentration of inositol in DMEM is 40uM. Thus, are the ~155uM (28 mg/litre) added by the authors at the high end of the 40uM? Given that FBS contains inositol have the authors used dialyzed serum? While adding 155uM of inositol on either inositol-free medium or to medium containing 40uM inositol does not alter the author's message, this technical information are important for the reproducibility of the data presented and to understand how HEK293T manages inositol homeostasis.<br /> It would be helpful to know if store operated calcium entry is altered in impa1-/--M1 cells. This information would nicely complement Fig.3 C-E data.<br /> In the Introduction at the end of page 4, the evidence not supporting the inositol depletion hypothesis is correctly discussed. This section lacks the discussion of another work questioning this theory (PMID: 30171184). The conclusion of this work is also in agreement with the authors finding that lithium affects the rare/turnover (lines 490/506) of PIP2 synthesis.<br /> In the material and methods, Liquid Chromatography Mass spectrometry is abbreviated to LCMS while in the main text (line 493) LC-MS is used. The dashed version should be used throughout the manuscript.<br /> I suggest to define (line 500) phosphatidylinositol 4-phosphate as (PI(4)P simplified as PIP). This will be consistent with the phosphatidylinositol 4,5-bisphosphate abbreviation as (PIP2) as reported in the introduction (line 97)<br /> Line 646: Instead of using [this study] the authors should refer to the Figure panels supporting the discussed argument.

Referees cross-commenting

Reviewer #2 main message is identical to my. The work is a "contemporary re-evaluation of the inositol depletion hypothesis" but it does settle the debate. Say that reviewer #2 also recognises the importance of the work in defining IMPA1 as the only lithium target affecting the PI cycle removing GSK3 from the picture. Additionally, we agree that the thorough transcriptional analysis of the effect of lithium on human cortical neurons will be very informative for any researcher interested in psychiatric disorders.

Reviewer #2 requests are rational and not demanding. Most queries require extra information or the reformatting of the data presented.

Significance

The submitted manuscript addresses an important topic. The authors developed HEK293 stable expressing muscarinic receptor to study the effect of lithium (without or after receptor activation) on PI(4,5)P2 turnover using two approaches, by microscopy and biochemically by LC-MS. These analyses were followed by a thorough characterization of the effect of lithium on calcium signalling. The generation of HEK293 impa1-/- line has allowed the authors to demonstrate that the observed effect of lithium on PI(4,5)P2 turnover and calcium signalling were IMPA1 dependent. The authors pushed the work to a higher level by studying the effect of lithium on iPSC-derived human cortical neurons demonstrating that lithium reduces neurons excitability and calcium signalling. Although previously published attempts failed to generate IMPA1 deficient human cortical neurons the authors managed to produce iPSC impa1-/- but, as reported and consistent with previous literature, this cell line failed to differentiate into neurons. This effort highlighted the author's commendable goal to develop a thoughtful story and not just another publication. The work is complemented by a very informative transcriptional analysis characterising the effect of lithium on human cortical neurons. Noteworthy is also the author's efforts to functionally and transcriptionally define the effect of another lithium target, GSK-3. These experiments emphasize that GSK-3 does not phenocopy the effect of lithium. This is another utterly important message of the paper.

In conclusion, the authors presented an easily readable, comprehensive, and experimentally convincing story. Furthermore, the developed experimental tools (HEK293-m1AchR) and the extensive data set (transcriptomic analysis) will be instrumental to further studies aimed at elucidating mechanistically how phosphoinositide signalling affects BD pathophysiology.

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Referee #3

Evidence, reproducibility and clarity

In this work, the authors generate a multi-omic dataset (RNA, proteomic and metabolomic) from fibroblast cell-lines of human and bat origins, in study of the specific differences in bat that allows them to have a good cancer resistance and longevity. They specifically focus on metabolic differences between humans and bats. They perform differential analysis followed by GO enrichment analysis to highlight differences related to the electron transport chain both at the level of RNA and protein abundance. They then use FBA sampling and specific constraints to propose an hypothesis of reverse direction of the second complex of the ETC, as well as better resistance to ROS, which they support with several subsequent experiments.

Overall, the paper is very well written, the findings are presented clearly and efficiently. For the most part, the assumption and limits of the study are clearly stated by the author (notably with respect to the limits of using only cell lines). In my opinion, the goal of the paper, which is presented as a stepping stone into further characterisation of the metabolic differences between human and bat for potential oncological research benefits, is clearly stated and appropriate.

There are however several points that I think are important to address inorder to improve the quality of the scientific work and its interest for the rest of the scientific community.

Major

The authors state:<br /> "We then set the lower bound of the PaLung Complex I reaction flux to a value equal to 70% of its theoretical maximum. Similarly, we set the upper bound of the WI-38 Complex I reaction at a value equal to 30% of its theoretical maximum value. This ensured that the PaLung model would have higher flux through the Complex I reaction, in comparison to the WI-38 model."

How do the results hold with different thresholds ? Are these findings robust with e.g. in ranges between 10 to 50% (90-50%) (instead of only 30% and 70%). Furthermore, the histogram figures doesnt seem to reflect a 70% of maximum lower bound for complex I (threshold at a value of 30 seems like extremity of tail).

Number of differentially expressed genes is extremely high because such cutoffs are not really meaningful given the comparison between two organisms. No need to refer to the 6247 above cutoff as differentially regulated genes (see: https://elevanth.org/blog/2023/07/17/none-of-the-above/ and https://daniel-saunders-phil.github.io/imagination_machine/posts/if-none-of-the-above-then-what/ for pointers toward current best practice in biological statistics). Enough to simply note that 6247 are above the cutoffs, which suggest a drastic (and expected) difference in expression profiles between the two organisms.

Please highlight the RNA and proteomic analysis assumption and present results within those boundaries (e.g. how are the transcript matched between human and bat, the use of human gene ontologies, etc...). Are the human GO set definitions relevant in bat (it is a common practice with mice and rats, are bats close ?)?

Are oxphos and hypoxia responses the most extreme pathway scores in the GSEA ? Instead of barcode plots that are generally not a very useful use of figure space, use fig 1C to show the top e.g.20 (positive and negative) pathway scores so that we can see how much those two actually stand out. Same for the proteomic analysis. Also, need to show an unbiased side by side comparison of the pathway enrichments for RNA and proteomic, the reported results in main text and figures are too cherry picked to be of interest as they stand.

Finally, and very importantly, please upload ALL the code used for the analysis, with instructions to run it and all the required inputs and source files. The computational analysis is only as credible as it is easy to reproduce.

Minor

Introduce GeTMM, what are its key specificities ?

Fig 1C code bar plot useless, simply report ES and NES and pathway absolute rank in text.

Report Foldchange/p-value/rank of complex-I members and other genes of interest for the narrative of the paper.

Referees cross-commenting

I also think the comments from the other reviewers are appropriate.

Significance

In my opinion, the goal of the paper, which is presented as a stepping stone into further characterisation of the metabolic differences between human and bat for potential oncological research benefits, is clearly stated and appropriate.

Broadly interesting for oncological research.

My espertise is multi-omic data analysis and integration with prior knowledge in the context of complexe diseases.

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Referee #2

Evidence, reproducibility and clarity

Jagannathan et al. performed a multi-omics comparative analysis between fibroblast cells from bats of the species P. alecto and humans. Using a combination of transcriptomics, proteomics and metabolomics, the authors showed differences in central metabolism between the cells of the two species. Specifically, the authors noted higher expression of Complex I components of the electron transport chain, as well as low activity of the Complex II. The computational modeling suggested that the latter is indicative of a state resembling the state of ischemia. Furthermore, the expression of antioxidant components was interpreted as higher in the bat compared to human cells, which is in accordance with previous reports.

Overall, it is a comprehensive multi-omics approach performed with a very interesting biological object, such as a bat. However, some aspects, especially the part of bioinformatic analysis, needs to be enhanced. The existence of differences in mitochondrial metabolism is also not surprising, given the evolutionary distance and very different ecology and lifestyle between the two species, but a more mechanistic follow-up would be of greater interest. Nevertheless, it is the first study using integrated omics approach of that sort done on bats.

Major:

1. The authors compared a fibroblast cell line derived from adult bats with a human embryonic cell line. Please discuss whether mitochondrial metabolism in embryonic cells might be different and how it could have affected the obtained results. Please describe in more detail how the cells were established, what population doubling they were used at (both bat and human cells). Were the cells cultured in atmospheric oxygen or low-oxygen conditions. The exposure of cells to atmospheric oxygen might affect the many mitochondrial parameters measured in this study and could influence the main finding about ischemic-like state. Additionally, please mention in the limitations of the study that only biological n=1 was compared (since cells only from 1 individual per species was used in experimental groups), despite n=3 technical replicates.
2. Reference genomes for bats are not as well annotated as for human. Downregulation of a pathway may result from some genes being excluded from the analysis because of poor annotation of the P. Alecto genome compared to human. The authors state: "Genes with counts per million (CPM) < 1 in more than 3 out of 6 samples were discarded from downstream analysis". So, if the gene was not annotated, was it assigned a zero value and discarded? Was it discarded if it was zero in one species (e.g. bat) or set to 0? If such genes were excluded, while in reality not being mapped, they could have skewed the pathway analysis.
3. All conclusions are based on high-throughput data, however it is accepted that some validation should be provided. Please provide qPCR or WB (if good antibodies are available) validation for several most significantly differentially expressed genes supporting the pathways identified in Figure 2 (preferably supporting the conclusions about Complexes I/II).
4. The major findings of this paper were based on the omic data, followed by some experimental validations. However, the quality of these omic data or the results are not solid enough to motivate the authors to validate these findings. For example, both of the GO terms enriched by the DEGs in Fig.1 are not the top terms as claimed by the authors (not even significant after multiple test correction). Also, even though the 2 GO terms in Fig.2 are quite significant, the expression pattern seems not very consistent among the replicates, which make the enrichments not so solid. This highlights an inconsistency among different omic datasets, which may generate some conflicting results. For example, the low level of metabolites from TCA cycle (Fig.4c) seems not consistent with the high level of TCA-related protein, as described in Fig.2c & d. For the purpose of improving the manuscript quality, the authors may have to evaluate the consistency among the multiple omic datasets or to optimize their bioinformatic pipeline to enhance the results.
5. The dominant up-regulation of complex I in ETC is interesting and is the main finding of this paper. However, no experimental evidence was provided to prove the greater activity of Complex I, for example, metabolites changes. In addition, the genes encoding proteins belong to ETC complex I, II, III and IV vary a lot, with much more genes encoding complex I. Therefore, the author should consider the background gene number when they compare the up-regulated gene number differences in each complex. For example, a fisher-exact test could be done to see if complex I has significantly more genes been up-regulated than a random expectation.
6. If the main findings of this paper can be further confirmed by additional experiments or data, it will be a very nice paper. This could be a potential mechanism that bats used to switch metabolism modes between two metabolic extremes: flight and hibernation, which require high and low energy. However, the usage of only the lung fibroblasts of human and bat may limit the ability of generalizing this 'ischemic-like state' of ETC in most of the bats tissue/organs. While I agree what the authors mentioned in the discussion section, that to extend to primary cells of other species can help generalize this finding, studying the metabolism state of different cell type of bats (e.g., muscle cells responsible for flight; myocytes and neurons for hibernation) probably can provide more insights into the evolution of various interesting phenotypes of bats.

Minor:

• the author may have to add the p value or FDR for each GSEA plot, even though some of the FDR are not significant. Also, it will be better to show the normalized enrichment score (NES) instead of the ES.
• the gene set name in several supplementary tables contains many '%' characters and those needs to be removed.
• in Line 302, "...combined with the earlier findings of downregulated OxPhos expression and low OCR, we conclude...". If my understanding is right, the authors only mentioned the up-regulation of Oxphos expression, instead of down-regulation. This sentence may need to be clarified.
• How did mitochondrial DNA content per cell compared between the two species? Could the results be affected by the number and size of the mitochondria per cell in each species? An indirect measurement of mitochondrial DNA yield in the fractionation experiment would be the total DNA amount that was obtained in mitochondrial fractions per cell lysed.

Significance

The work is significant considering the limitations stated above. This may be considered a pilot study of brand significance.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, the authors conducted a multi-omics analysis comparing cells from the long-lived bat, Pteropus alecto, and human cells. Their findings revealed that bat cells express higher levels of mitochondrial complex I components and exhibit a lower rate of oxygen consumption. Moreover, computational modeling suggested that the activity of complex II in bat cells might be low or even reversed, similar to the conditions observed during ischemia. The decrease in central metabolites and the increased ratio of succinate to fumarate in bat cells might indicate an ischemia-like metabolic state. Despite having high mitochondrial ROS levels, bat cells exhibit higher levels of total glutathione and a higher ratio of NADPH to NADP. Additionally, bat cells showed resistance to glucose deprivation and induction of ferroptosis.

Major comments

1. Regarding Figure 1A, the authors mention 'n = 3' for a single cell line. Does this refer to three different passages or three independent experiments? Please provide a more detailed description to clarify.
2. In relation to Figures 1C and 1D, the authors state in the figure legend that the 'GSEA analysis identifies Respiratory electron transport and Cellular response to hypoxia as the top metabolic pathways that are differentially regulated between PaLung and WI-38 cells.' (Lines 140-144). However, the criteria for selecting these terms as the top metabolic pathways is not clear. In the lists in Supplementary Tables 2 and 3, the authors' proposed term, 'Respiratory electron transport,' is ranked 126th, and 'Cellular response to hypoxia' is ranked 79th. Conversely, terms related to the TCA cycle are ranked 66th and 82nd, and another term that seems to be related to hypoxia, 'OXYGEN-DEPENDENT PROLINE HYDROXYLATION OF HYPOXIA-INDUCIBLE FACTOR ALPHA,' is ranked 62nd. Could the authors please provide a clarification for their choice of 'Respiratory electron transport' and 'Cellular response to hypoxia' as the top metabolic pathways?
3. In the Materials and Methods section (lines 419-421), the authors mention, 'GSEA was run against the complete Gene ontology biological process (GO BP) gene set list (containing 18356 gene sets).' However, they narrow down the gene dataset for analysis (lines 136-138, 'we filtered our gene dataset to contain only genes listed under the Gene ontology category Cellular Metabolic Process (GO ID:0044237), resulting in a truncated list of 4794 genes.'). I'm concerned that this selective approach might introduce bias into the resultant pathways. Is this selective approach commonly employed in this type of analysis? And isn't there a need for adjustments to avoid potential bias?
4. The authors noted that the number of differentially expressed genes (DEGs) is quite high (6,247 out of 14,986) as per lines 134-135, stating that "The number of differentially expressed genes (6,247) was extremely high, suggesting that multiple pathways are differentially regulated between the two species." However, this large number of DEGs could indicate either an improper correction procedure or a need for a more stringent threshold. The authors should address this issue to avoid potential misinterpretation of the results.
5. In Figure 2B, the samples labeled as W1 and P1 appear to be outliers. This raises questions about the integrity of the sampling or analysis process. Please describe about this.
6. Regarding the GSEA analysis of Fig. 2, they are using the full set of GSEA. However, this reviewer is wondering if this is appropriate when analyzing mitochondrial fractions, as I believe using the entire GSEA set could introduce a bias. Is this a common approach? Shouldn't the authors be focusing on mitochondrial-related sets within the GSEA, and then determining the upregulated and downregulated pathways from there?
7. The authors describe in lines 195-197, "GSEA-flagged upregulation in OxPhos was driven mostly by the upregulation of Complex I subunits, for both the proteomic and transcriptomic data (Figure 2G, Supplementary Figure S1D)." However, within this analysis, the number of genes composing each subgroup of the mitochondrial Complexes are 44 for Complex I, 4 for Complex II, 10 for Complex III, and 19 for Complex IV (https://www.genenames.org/data/genegroup/#!/group/639). The authors mention that the genes of Complex I were dominant in the ETC, but, might this just be reflecting the original difference in the number of genes? As this reviewer believes this could have a significant impact on the authors' current claims, this reviewer suggest the authors to carefully reconsider this point, comparing the actual results with the proportion expected from the difference in gene numbers. (Even in Fig. S1D, it appears to correlate with the number of genes: C1 39.3%, C3 10.7%, C4 10.7%, C2 3.5%)
8. As pointed out in Major Point 7, if the authors' claim of enrichment in Complex I is indeed due to the large number of genes included in the Complex I subgroup (https://www.genenames.org/data/genegroup/#!/group/639), can the assumption of High Complex I flux truly be considered valid? In that case, this constraints model would become inappropriate, and the validity of the inferred low or reverse activity of Complex II would be diminished. Therefore, a careful re-examination is desirable.
9. (option, takes about 1-2 months). This reviewer believes that the authors' most important claim, concerning the high activity of Complex I and the low activity of Complex II, lacks strong evidence as no biochemical data of the activities of each mitochondrial complex are presented to substantiate this. Unless additional biochemical experimental data is provided, the assertions should be toned down. While the abstract mentions "complex II activity may be low or reversed," it is stated with certainty in line 108 of the introduction, "associated with the low or reverse activity of Complex II." Based on the present data, this reviewer believes that the claim remains speculative. Therefore, I suggest moderating the overall argument or adding the biochemical data. While the results from metabolomics are supportive, they do not serve as direct evidence.
10. Regarding Figure 5, the title of the figure states "lower antioxidant response", but it doesn't seem that the data in the figure actually shows a lower antioxidant response.
11. In lines 109-110 of the Introduction, the authors state, "we confirmed our prediction of ischemic-like basal metabolism in PaLung cells by characterizing the response of bat cells to cellular stresses such as oxidative stress, nutrient deprivation, and a type of cell death related to ischemia, viz. ferroptosis." However, can the assertion that the cells are in an ischemic-like state be confirmed simply because they are resistant to several types of cellular stress?

Minor points:

1. The authors mention the use of cufflinks/Tophat for mapping/quantification. However, support for these software programs has ended and the creators of these programs themselves recommend using the successor programs. I recommend re-analysis using a more current pipeline (such as HISAT2/StringTie, STAR/RSEM, etc.). Furthermore, the transcriptomics section of the methods should also include the program used for cleaning and trimming.
2. As for the Oxygen Consumption Rate (OCR) data presented in Figure 2F, it makes sense that it's low at the basal level. However, it's perplexing that it is also low even under uncoupled conditions, especially considering the high energy demand associated with flight in this species. Could the authors provide their interpretation on this apparent contradiction?
3. In line 156, the authors mention that 'Profiling detected a total of 1,469 proteins.' Please provide more details in the explanation. Specifically, does this total of 1,469 proteins represent a combined count from both humans and bats, or is this the number of proteins for which orthologs could be identified in both species, just like the authors did with the transcript results.
4. In Supplementary Table 4, only 127 mitochondrial proteins are listed out of the 405 proteins mentioned in "Of these 405 proteins, we identified 127 to be core mitochondrial proteins (lines 161-163)". As there is no explanation for this within Supplementary Table 4, it would be better to include one.
5. In line 472, the phrase "GO BB gene set list" is used. Could this potentially be a typographical error, and should it instead be "GO BP gene set list"?
6. In the volcano plot of Fig. S3B, it appears that the side with lower P/W values generally corresponds with lower p-values. I wonder if there might have been any oversight or mistake in the data analysis process that could explain this observation?
7. In lines 249-252, it is stated, "The low or negative flux values for Complex II in our PaLung simulations indicate that the electrons obtained from Complex I may accumulate at Complex II or potentially even get consumed by Complex II operating in reverse (bypassing the rest of the ETC) in PaLung cells." However, isn't the basic process of electron transfer done through Complex I-III-IV, independent of Complex II?
8. Regarding Figure 4F, the authors state, 'PaLung cells displayed higher viability than WI-38 cells after glucose deprivation (Figure 4F).' However, in addition to the cell images, it would be beneficial to perform experimental quantification of cell death to provide more rigorous data. Additionally, the cells appear to be over-confluent, which might influence the results. Also, scale bars should be included in all photos, including Fig. 6.
9. Regarding Figure 5B, it is stated that 'the expression levels of differentially expressed antioxidant genes' are shown, but it includes those that are not significant. It would be helpful if the authors could clarify how this gene set was selected.
10. Regarding Figure 6C, the values for total glutathione seem to significantly differ from those in Figure 5C. An explanation for this discrepancy would be appreciated to ensure the consistency and reliability of the data.

Referees cross-commenting

I think the comments from the other reviewers are appropriate.

Significance

Collectively, these intriguing results from the interspecies comparison provide novel insights into the differences in metabolism and cellular characteristics between bat and human cells. However, the study has some limitations, notably certain weaknesses in the data and potential overstating of certain interpretations. Addressing these issues would enhance the overall quality and robustness of the manuscript. Furthermore, if feasible, conducting a biochemical analysis of each mitochondrial complex activity would solidify the authors' main conclusions.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This paper provides an elegant investigation into the dysmorphology of skeletal structures upon loss of the extracellular Fraser Complex through use of a zebrafish fras1 mutant. The adult phenotypes of this mutant had not been previously explored in detail. The authors use transgenics, histological staining and immunostaining to visualize the morphological defects, then examine Fraser Complex localization and effects on Shh signaling upon loss of Fras1. They analyse both steady state and regeneration contexts. Most importantly, they demonstrate the blistering that has been shown to occur in larval fins, also occurs during regeneration of the adult fins, and that there is a disorganization of the pre-osteoblasts due to basement membrane corruption. This work provides novel investigation into how Fraser Complex leads to skeletal defects.

Major comments:

Overall the data presented by the authors is logical and very well presented. They make reasonable claims that are supported by sound experimentation. Statistics are used appropriately and the authors combine different approaches to make their points. For example they draw on previous single cell RNA-seq Data sets to define the cell type expressing Fraser complex components but then also use immunostaining and ins situ hybridisation to localise expression domains. I thought the analysis using the ptch1:kaede line to be particularly elegant and informative.

My first major question relates to Figure 7. The authors cage their analysis under the impetus of understanding how the distal anomalies and skeletal defects in Fraser Syndrome arise in development. They present convincing images of distal blistering during regeneration. Were similar blisters seen at any stage during adult fin development prior to the full fin formation? The authors might have noted this during their imaging of the ptch1 reporter Figure 6 Supplement 1. Or they might need to look earlier. Figure 7 is informative analysis. It's a shame to limit it to regeneration and not look during adult fin formation which would have direct inferences for human development.

Secondly, was osteoblast morphology affected as well as their patterning in the fras1 mutants? Perhaps the authors could look at zns-5 antibodies or sp7:egfp line in transverse cryosections to assess if there was a change in osteoblast morphology. Figure 5B' certainly suggests they might be more cuboidal and have lost their flattened shape. This change in osteoblast morphology has been noted in other ECM mutants affecting the lepidotrichia.

Minor comments:

I have only a few minor comments.<br /> Line 55 Introduction. For clarity change this sentence to "variable expressivity and incomplete penetrance reminiscent of the variability seen in distal limb defects in humans with Fraser Syndrome."

Referring to Figure 2, is each fin ray thicker in fras1 mutants than in WT? It appears so but might be just an optical illusion. Would be easy to measure and state in the text.

Line 242, 243 and Figure 5. The text refers to Fig 5C' and Fig 5D', but I could only find Fig 5C' and Fig 6C'. Do you mean E, F??

Related you claim that in fras1 mutants, frem2 protein remains intracellular. How do you know that protein signal is intracellular yet in the WT it is extracellular? Please reword this or show more conclusively. This is also repeated on line 360 in the discussion.

Fig 6B, D are not referred to in the main text.

I couldn't find details of the Runx2 antibody in the materials and methods

Significance

This paper provides novel insights into how loss of Fraser Complex might alter morphology of post-embryonic structures, and gives novel, visual indication of the effect basement membrane disruption has on osteoblast patterning. This will give novel guidance to explaining the basis of skeletal presentations of Fraser Syndrome for basic researchers interested in the importance of osteoblast environment on patterning and clinicians examining similar rare skeletal congenital syndromes.

It elegantly demonstrates that cellular topology, organisation and morphology is just as important as signalling in defining organ growth and shape. The authors also suggest this model of an indirect disruption of osteoblast patterning might explain why there is such variability in distal skeletal phenotype severity in Fraser patients. This is a valid and reasonable hypothesis.

My background directly relates to mutant analysis of zebrafish fins

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, Robbins et al. develop the adult zebrafish caudal fin as a model for limb deformities in Fraser syndrome. They show that the zebrafish fras1 mutant can survive to adulthood and investigate how loss of fras1 influences the caudal fin during its regeneration. The fin ray branching defects and chondral bone defects examined in this study show a degree of variability akin to many defects found in Fraser syndrome, including limb defects. The paper is an easy read, has beautiful imaging, and shows compelling quantification. As such, the authors set up the zebrafish fras1 mutant caudal fin as a novel and interesting platform to investigate the onset and variability of limb defects in Fraser syndrome.

Major comments:

Figure 7 makes some critical claims based solely on H&E staining; better markers are needed. I also strongly recommend that the authors repeat this Figure 7 experiment with immunolabel or other techniques that mark the epithelial and mesenchymal layers distinctly. In particular, since the author's discussion focuses on osteoblast positioning, it seems important to mark the osteoblasts alongside the epithelium.

The authors posit that background mutations explain Fraser syndrome variation, but it's worth also considering non-genomic origins of variation, including potential micro-environmental differences and/or stochasticism. The caudal fin seems like an ideal system to test the idea - one could injure the fin and test how well initial defects predict defects after regeneration. It looks like the authors started to do so in panel 3R, but don't comment on the finding. Also, it looks like the initial severity doesn't completely predict regenerated severity - for instance, the least severe fin pre-injury becomes the most severe fin post-injury. I recommend explaining panel 3R in results text and returning to it in the discussion, to contextualize how this finding might influence understanding of fras1-dependent variability. OPTIONAL: Variability could also be compared between different fins in the same animal; does the severity of caudal fin defect correlate with severity in the pelvic or dorsal fin? If so or if not, what might this suggest about the origins of phenotypic variation in this model?

The study is focused on core Fraser complex, particularly fras1 and the Frem genes which are mutually-stabilizing components of anchoring cords that link nascent epithelia to underlying mesenchyme. The authors could broaden the paper's impact and scope by considering other proteins bound by the core Fraser complex, such as AMACO, Integrins, Npnt, fibrillin, etc. Likewise, examination of Collagen expression, such as collagen VII, may help explain why there is a dissipation over time for the requirement for fras1 to prevent blistering. It may be outside the scope of this study to delve deep into these 'nearby genes' but it seems reasonable to examine them bioinformatically in the scRNA-seq (perhaps adding a supplemental figure if the results are unsatisfying), or at least to discuss them and thereby contextualize the overall findings.

Minor comments:

Figure 8 feels like a visual abstract, summarizing findings and contextualizing existing models to the caudal fin, instead of putting forward a truly new model. It focuses on the concept that Fras1 is needed for epithelial-mesenchymal attachments and that Fraser-components stabilize one another; both of these ideas are over a decade old. Although the concepts are cited appropriately within the discussion narrative, it would be nice if Figure 8 did a bit more. The model could be revised in a way that offers new insights into how the specific defects seen in this study arise, by hinting at answers to some of the many questions raised by the study. What is the source of variation? Why do the fin rays fail to branch in the mutant? (could there be more to that decision than simple osteoblast mispositioning?) Why does defect severity change during regeneration vs. development? Why does an extra hypural cartilage form in the mutant? Is there any similarity between the failure to branch fin rays and the presence of fusions in chondral skeleton? These fusions could also be compared and contrasted with non-limb skeletal fusions? It's certainly optional to tackle all of these issues, but discussing any of them could increase the manuscript's impact and establish interesting fodder for future papers. These changes are important, but I place this remark in 'minor comments', because an improved final figure would not be critical to publication in some journals.

This sentence on line 273-274 is confusing and should be revised: "However, the Fraser Complex at least supports the Shh/Smo downstream cell behaviors that split pre-osteoblasts given frequent ray branching defects in fras1-/- mutants." What do the authors mean by "at least supports"? The phrasing may imply 'Provides physical support essential to,' but that reading does not explain why the fin rays branch in Shh expressing cells regardless of the presence of Fras1. (this comment is actually 'minor')

The Figure 7 title states that the Fraser complex is needed for normal "epithelial-mesenchymal tissue layering." I am not certain what the authors mean by this. The phrase written in the figure title implies that mesenchymal cells start appearing inside of epithelial regions, but that interpretation doesn't match the figure nor results text. An alternative read - one consistent with the final figure - is that the authors are simply trying to show that the blisters form at the interface of the fin and underlying mesenchyme. If this is the primary thrust of the argument, then it could be stated plainly - and shown more clearly in the results section. (this comment is also truly 'minor')

Significance

This manuscript establishes the zebrafish adult caudal fin as a new model to investigate epithelial-mesenchymal interaction defects and skeletal variation caused by loss of the central Fraser complex gene. It is an important contribution to existing models because of the similarity between patterning mechanisms in the caudal fin and tetrapod limbs, which are variably disrupted in Fraser's syndrome. This variability is itself of interest, because the profound variability of Fraser phenotype offers an experimental model for high-variance diseases, which remain poorly understood. The caudal fin is an exciting system to study variation, in particular because it can be cut and regrown rapidly with phenotypic severity compared between regenerates in a clonal system; that regenerative tractability is particularly potent when paired with the zebrafish transgenic toolbox, as the authors show in Figure 6. The present manuscript feels almost complete and yet it opens up many questions, suggesting that it can serve as a good foundation for future studies.

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Referee #1

Evidence, reproducibility and clarity

Robbins and colleagues present a new zebrafish model for studying the rare disorder Fraser Syndrome in a well written manuscript. The authors present an interesting phenotype caused by a mutation in fras1: mutants have small, misshapen fins with rays that frequently fail to form branches. The authors show that the Fras1 protein localizes to the distal portions of regenerating fin rays and that in its absence, another component of the Fraser Complex (Frem2) is decreased and mislocalized. The authors show that Fras1 is not required for Shh/Smo signal transduction but that branching is nonetheless disrupted.

Major comments:

Since the basement membrane ends up being such a big part of the story, it would add support to the model to specifically present a laminin stain in both WT and the mutant. This could potentially support to the idea that the FPC is integrating the BM with the osteoblasts and it would be helpful to see where the BM is relative to the 'blisters.'

The fras1-/- mutants show a near-absence of Frem2 protein; the authors conclude that Fras1 supports Frem2 secretion and assembly into Fraser Complex-containing BM. However have the authors considered the possibility that Fras1 directly or indirectly regulates Frem2 transcription? (The model in Fig 8 seems to show a relative increase in Frem2, which should be altered)<br /> Do the other components of the FPC (Frem1a/b, Frem3) show similarly disrupted levels and localization? As presented, since the Frem1a/b, Frem3 are not actually examined in a fras1-/- context, it is not justified to show their intracellular localization in the model in Fig 8b.

The relative activities of osteoblasts and osteoclasts may regulate the relative location of branches (Cardeira-da-Silva et al 2022). In the fras1 system mutant, it would be beneficial to examine osteoclasts to rule out the idea that Fras1 is simply required for osteoclast activity. This could additional lend support to the idea that disrupted integration between the BE and Obs underlies that failure of fras1-/- mutants to form branches. This could be done within a few months by crossing the mutant into an osteoclast reporter, or more rapidly by using an osteoclast specific antibody or ISH.

The authors look only at the meristic presence/absence of fin ray branches, and do not take fin length into account. Longer rays are more likely to form branches and the fras1-/- have shorter fins. Some of the branches may be absent in the mutant background simply because the rays are not long enough to have formed them. How far are the branches from the body in each background? Where do the branches form along the total length of the rays?<br /> In the regeneration experiments, do the mutants regenerate at the same relative rate as WTs? Could the decrease in the number of branched rays simply be due to the fact that the mutants may not have not regenerated to their original length by 28 dpa? Has the distance from the body to branch changed? These are all addressable with the data the authors have already collected.

Minor comments:

The protruding lower jaw phenotype mentioned in the results should either be shown, or if it is redundant with previous publications please add the citation here.

Please show Amputation planes in Fig 4E-G. It is notable that Fras1 seems to be present in the proximal region (proximal to the amputation plane?). This seems like it deserves mention in the manuscript.

In line 195, please clarify what you mean by ray proportions. The proportion of longest/shortest, presumably?

Please change the title of Fig 3: Fras1 mutants robustly restore skeletal patterning. Also, the ray length ratio in Fig 3Q has been tested with an unpaired t test. It should be a paired test as in R.

This is an unbelievably a minor point, but for consistency with the other panels I think that in Fig 5 E and F should be C' and D'.

The titles of Fig 6 and Fig 7 should indicate indicate Fras1 not the Fraser Complex. Eg. Fras1 is not essential for sonic hedgehog/smoothed signal transduction during fin regeneration

There are also a few grammar errors that should be fixed.

Significance

Robbins and colleagues present a new zebrafish model for studying the rare disorder Fraser Syndrome.

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Reply to the reviewers

First and foremost, we would like to extend our thanks to the two referees and managing editor of Review Commons for their constructive feedback and careful consideration of this manuscript. We have taken into consideration all of the suggestions from the reviewers and address all points below and in the following sections.

Minor comments from Reviewer #1:

“It is not clear why the authors used cell number as a measure of viability compared to the MTS assay used in figure 2.”

Response:

In Fig. 2, both MTS assay and CellTiter-Blue assay are used to assess cell viability at 24h and 72h, respectively, whereas counterstaining with DAPI is used to quantify cell number in viral infection assays. Quantification of viral infection using immunofluorescence requires fixation and permeabilization of the cells which is not compatible with assessment of metabolic activity through either the MTS assay or CellTiter-Blue assay post-imaging. One can perform these assays (e.g., MTS and CellTiter-Blue) prior to imaging, however there were concerns regarding viral assay image quantification after running these assays due to the metabolic demand of dye processing which may influence susceptibility to viral infection/propagation, and fluorescence of the metabolic sensor interfering with subsequent IF staining.

DAPI staining is not meant to show viability per se, however, one can gate for fragmented cell nuclei (indicative of lysed cell) to remove dead cells or nuclear debris from the measurement. However, pre-apoptotic or dying cells cannot be accounted for in this measurement.

In our case, due to the rapid doubling time of the immortalized cell lines used (e.g., Vero E6 ~24h, Calu-3 ~35-48h, L929 ~24h), we are able to see large differences in cell number as infected or lysed cells fail to replicate over the 48h experiment. Thus, DAPI staining can be used as a proxy to determine the overall health of the culture but is not directly a measure of cell viability.

Minor comments from Reviewer #1:

“Why did the authors adopt a different pre-treatment infection protocol for SARS-CoV-2 compared to MHV and OC43?”

Response:

The pre-treatment protocol was developed by collaborators in the BSL3 facility as standard practice for rapid treatment/screening of multiple compounds in a BSL3 lab where hands-on time was limited due to immense research focus on infectious disease (e.g., SARS-CoV-2) at the time. We screened many different nanoparticle formulations with this protocol before assessing nanoparticle effect on MHV and OC43 where we also used standardized protocols.

In reference to comments from Reviewer #2:

“The substance of the work is very interesting, but experience shows that the idea that by testing one isolate you can generalize about all other viruses is not accurate. Viruses mutate. SARS-CoV-2 has shown an exceptional capacity for mutation, and the mechanism by which viruses enter cells by endocytosis or membrane fusion plays a role in their exposure to products concentrated in the lysosome. Viruses that enter by membrane fusion (including certain isolates of SARS-CoV-2) should not a priori be as sensitive because they are not subject to phagolysosome fusion.”

“In this sense, it is important to evaluate efficacy on several viral strains and not on a single strain, as has long been the case for acute viral infections. As with HIV, viruses can present natural or acquired resistances linked to evolution under selection pressure or not.<br /> In practice, we cannot rely on testing two viruses, one that has disappeared (Wuhan) and the first virus of the Omicron generation (B1), to assess the therapeutic capacity of a new strategy.”

Response:

We would like to highlight that MFQ-NP efficacy was evaluated in several different coronavirus models (MHV, HCoV-OC43 and SARS-CoV-2) in addition to two distinct viral strains (SARS-CoV-2 WT-WA1 and Omicron BA.1) in this study. Not only this, but we have selected viruses from distinct Betacoronavirus lineages which infect different species (homo sapiens and mus musculus). At the time, we had chosen Omicron BA.1 as our model strain as it was the dominant strain in circulation and was temporally separated and genetically distinct from the original WT-WA1 strain.

We can appreciate that viruses mutate, and SARS-CoV-2 has exemplified this through its life cycle. Due to this rapid mutation rate, it is challenging to assess the current dominant variant (e.g., XBB.1.16 as of writing this) and complete manuscript preparation in addition to full peer-review prior to the emergence of a new, potentially more relevant, dominant variant. Additionally, it remains challenging to accurately predict the emergence and genotypic/phenotypic changes of new strains before they arise, necessitating investigation on ancestral strains or, at the least, the current dominant strain.

Lastly, we do not wish to speculate/generalize that MFQ-NPs or a similar approach works for “all other viruses”. As exemplified by efficacy studies in three Betacoronavirus lineages, and one of which using two distinct strains, we do argue that this approach is an effective means to inhibit Betacoronavirus infection. We speculate in the discussion that MFQ-NPs may be used as either a prophylactic or treatment for an array of other respiratory coronaviruses, however we neither show data or speculate efficacy against viruses outside of the coronavirus family.

In reference to comments from Reviewer #1:

“The claim that MFQ may impact cell entry is not supported by the data in the paper. At minimum, the impact of treatment on expression of viral entry receptors for all 3 viruses should be performed, viral attachment assays (see PMID 35176124) and viral pseudoparticle assays. Further the conclusion that MFQ inhibits replication as well as entry is not fully supported by the data presented. This could be improved using a single cycle infection experiment using a synchronised infection protocol. The gold standard to determine impacts on replication would be the use of a viral replicon however I appreciate the technical difficulties in performing these experiments.”

Response:

We agree that the mechanism by which MFQ-NPs inhibit coronavirus infection has not been fully interrogated through this work. We do have preliminary evidence addressed in Fig. 4 which suggests that mechanistically MFQ-NPs may work through targeting pH-dependent protease activity and lysosomal function downstream of viral uptake. However, we have not yet investigated the effect that MFQ-NPs may have on viral entry receptors or viral attachment.

To that end, we are proposing to perform RT-qPCR to measure changes in expression level of key membrane bound proteins responsible for viral uptake. For these assays, we plan to treat Calu-3 cells with MFQ-NPs, unloaded PGC-NPs, equivalent concentration of molecular MFQ, or DMSO as control to gauge expression level of ACE2 (Hs01085333_m1), TMPRSS2 (Hs01122322_m1), sialate O-acetyltransferase gene (CasD1, Hs01082700_m1), and sialic acid acetylesterase gene (SIAE, Hs00405149_m1) relative to expression of glyceraldehyde-3-phosphate dehydrogenase (GAPDH, Hs02786624_g1) using TaqMan probes (ThermoFisher, USA). Additionally, we will also measure the expression level of Cathepsin L (Hs00964650_m1). Cathepsin L is not a transmembrane protein, however strong evidence suggests that this lysosomal protease is essential for S protein processing and viral membrane – endolysosomal membrane fusion in the SARS-CoV-2 endocytic infection route.

These proteins are chosen as ACE2 and TMPRSS2 are known mediators of SARS-CoV-2 uptake and fusion, and HCoV-OC43 relies on uptake via sialoglycan-based receptors with 9-O-acetylated sialic acid (9-O-Ac-Sia) as a key component. Although CasD1 and SIAE themselves are not transmembrane receptors for HCoV-OC43, they regulate the addition or removal of O-acetyl ester groups from sialic acids, respectively.

Similarly, we plan to treat L929 cells with MFQ-NPs, unloaded PGC-NPs, equivalent concentration of molecular MFQ, or DMSO as control to gauge expression level of CEACAM1 (Mm04204476_m1) relative to expression of GAPDH (Mm99999915_g1). MHV spike protein binds to murine carcinoembryonic antigen-related cell adhesion molecule 1a (mCEACAM1a) facilitating infection. NP treatment duration will be consistent with viral infection assays (e.g., 48 h) prior to RNA isolation and qPCR.

Results from PCR measurements may warrant further investigation into protein level expression measured by Western Blotting. However, we plan to begin with PCR as blotting for multiple membrane bound proteins is considerably challenging and higher cost than qPCR.

In addition to expression of viral entry receptors, we will also perform a viral attachment assay and internalization assay to further interrogate MFQ’s mechanism of action. To determine whether mefloquine inhibits SARS-CoV-2 binding/attachment, we will perform viral binding assays in Calu-3/ Vero E6-TMPRSS2-T2A-ACE2 cells that express ACE2 at high levels, and HEK293T cells that express ACE2 at lower levels. Assays will be performed using SARS-CoV-2 Spike pseudo-typed lentivirus which expresses a fluorescent reporter upon mammalian cell infection. SARS-CoV-2 Spike pseudo-virus is advantageous as it mimics SARS-CoV-2 entry mechanisms; however, it can be handled at BSL2, and it can be used to accurately quantify viral uptake since this virus is not replication competent.

SARS-CoV-2 can be internalized primarily via receptor-mediated endocytosis in cells which do not express TMPRSS2 (e.g., Vero E6) or via direct plasma membrane fusion in cells which do express TMPRSS2 (e.g., Calu-3 and Vero E6-TMPRSS2-T2A-ACE2). To test whether mefloquine inhibits the endocytosis of SARS-CoV-2, Vero E6 cells will be pre-treated with effective concentrations of MFQ-NPs, equivalent concentration of molecular MFQ, or unloaded PGC-NPs/DMSO as controls. Next, cells will be inoculated with SARS-CoV-2 Spike pseudo-virus at MOI 0.5 at 37 oC for 1 h. Cells will then be washed with PBS to remove unbound virus, media containing treatments will be reintroduced, and the pseudoviral reporter fluorescence will be measured 18-24 h after inoculation.

To test whether mefloquine inhibits TMPRSS2-mediated fusion during SARS-CoV-2 infection we will use TMPRS2 expressing Vero E6-TMPRSS2-T2A-ACE2 and Calu-3 cells. Cells will be pre-treated with Leupeptin/Pepstatin (inhibitors of endolysosomal proteases), camostat mesylate (serine protease inhibitor), MFQ-NPs, molecular MFQ, unloaded PCG-NPs, or DMSO as control for 1 h, and then inoculated with SARS-CoV-2 Spike pseudo-virus (MOI = 0.5). Cells will then be washed with PBS to remove unbound virus, media containing treatments will be reintroduced, and the pseudoviral reporter fluorescence will be measured 18-24 h after inoculation.

Minor comments from Reviewer #1

_<br /> “Further discussion in the introduction as to the potential mechanism of action of MFQ should be included. I would also suggest the authors read the work by Elizabeth Campbell and Bruno Canard concerning the potential difficulties in designing direct acting antivirals for coronaviruses.”

“The figure legends lack detail concerning the number of replicates and statistical comparisons. For viral infections MOIs used are also absent.”_

Response:

We have included a brief summary describing what the field knows of the mechanism of action of MFQ. Namely that MFQ does not directly inhibit the virus/cell membrane attachment process, rather MFQ somehow inhibits viral entry after attachment. We speculate a few mechanisms by which this may occur, which include: (1) inhibiting viral membrane fusion with the cell membrane or endolysosomal membrane, (2) inhibiting proteases responsible for processing SARS-CoV-2 S protein and exposing the fusion peptide, (3) modulating expression levels of ACE2, TMPRSS2, and/or cathepsin, or (4) promoting exocytosis of SARS-CoV-2 particles after uptake.

While it is not the primary goal of the manuscript to determine this mechanism of action, we have evidence currently that MFQ inhibits endolysosomal proteolysis (e.g., mechanism 2 above). Through viral attachment assays and evaluation of receptor expression levels we will also probe mechanism 3 in the revision process.

We have updated the figure legends and methods section to include further details concerning replicates and statistical comparisons. For viral infections we had previously listed the MOIs used in the Materials & Methods section but have also included them in the figure legends.

In reference to comments from Reviewer #2:

“On the one hand, both the introduction and the abstract contain too many elements that give a biased view of the extremely controversial literature. For example, the activity of Hydroxychloroquine and its toxicity have been explored most extensively on the "C19Early" website, which reports on trials carried out in a multitude of countries, including more than 300 trials with Hydroxychloroquine, and it is unreasonable in a scientific paper, designed to last, to report on the major beliefs at a given moment in order to develop a work that has nothing to do with this debate. The same applies to the efficacy of the vaccine. It is difficult to say that the vaccine was poorly distributed, with 20 billion doses, making it the most widely distributed vaccine in the history of mankind in such a short space of time, with results that were not as spectacular as the studies predicted, since the epidemic continued at a comparable level. I suggest that the authors concentrate on their work rather than getting involved in the controversies that are developing around treatments and vaccination.”

Response:

When possible, we have tried to highlight the mixed/controversial results, both positive and negative, of pre-existing therapeutics targeting SARS-CoV-2 and COVID-19 and cited them accordingly. Conjectural phrases such as “selective pressure may lead to 3CLpro mutations conferring nirmatrelvir resistance to new viral mutants” or “there is a growing concern that Molnupiravir, especially when administered at sub therapeutic doses, may result in the creation of more virulent SARS-CoV-2 mutants” are supported by observations in the literature and have been proposed by other experts in the field. Otherwise, we have revised the text to remove any unsupported speculative phrases.

We believe it is worth noting the existing therapeutic strategies in the field to provide context and rationale for our differentiated approach. We have extensively explored the C19Early site as well, and although it does a fantastic job of compiling relevant literature, this site also appears to have a biased view. Throughout preparation of this manuscript, we have considered FDA recommendations and clinical practice in prophylactic protection/treatment of COVID-19 paramount in guiding our introduction and discussion.

We have removed phrasing regarding the limited distribution of vaccines.

In reference to comments from Reviewer #1:

_“The authors claim that MFQ loaded nanoparticles have reduced cytotoxicity compared to 'free MFQ' dissolved in DMSO, however with the NP data and free MFQ data not plotted with the same units this conclusion is hard to reach (Fig.2). While I appreciate the molar units are presented in the text - the reduction in cytotoxicity with MFQ-NP appears to be relatively minor in the both the Calu3 and Vero cell models (doubling in IC50 in both instances). This may indicate quite a narrow therapeutic window for antiviral efficacy without unwanted cytotoxicity. Can the authors replot the data on scales using either molar or ug/ml and use the same dose range for all treatments to enable statistical determination as to whether MFQ-NP significantly reduce cytotoxicity.

To test the antiviral efficacy of the MFQ-NP the authors adopt 2 infection systems, either treating cells pre or post infection. The authors either use fluorescently tagged reporter viruses (OC-43/MHV) or immunofluorescence to visualise and quantify viral infection in cell-line models. Given a key aim of this paper is to determine whether MFQ-NP rather than free MFQ is a superior treatment option, it is challenging to assess this with the data presented in figures 5-6. The units of treatment between NP, MFQ-NP and free MFQ again differ, and the molar dose range of MFQ-NP and free NP is not the same. This makes it very hard to conclude whether MFQ-NPs are more effective then free MFQ. Formal dose response curves with the same dose of empty-NPs, MFQ-NPs and free MFQ are needed here, preferably with match cell viability data using the same assay as figure 2.”_

Response:

We will include additional plots with axis scaling for MFQ-NPs as concentration of MFQ in µM rather than concentration of NPs in µg/mL for further comparison to the free MFQ group. We chose concentration of NPs to match with the equivalent unloaded NP controls. Unfortunately, it would not be possible to create a formal dose response curve with the same dose of empty-NPs and free MFQ as those entities only co-exist in the MFQ-NPs treatment group.

We agree with the observation that the therapeutic window is likely narrow in vitro. This is observed in the viral inhibition and cytotoxicity experiments, where the most efficacious dosing of NPs (e.g., 50 – 100 µg/mL) in inhibiting viral infection is similar to the IC50 value (e.g., 54 µg/mL in Calu-3) at 24 h. Similarly, we see a biphasic dose response in our protease activity assay, suggesting that low doses actually increase endolysosomal protease activity which may promote viral infection.

We speculate this dose limiting toxicity and narrow therapeutic window will likely be improved more drastically in vivo (ongoing continuation of this study), however in vitro we still see at least a minor improvement in MFQ tolerability.

In reference to comments from Reviewer #1:

“Finally while animal experiments are likely beyond the scope of this study, use of air-liquid interface cultures of lung epithelial cells would be a significant improvement to the work and provide further support to their conclusions in a physiologically relevant system.”

Response:

While we appreciate the suggestion of ALI models and animal models to further assess MFQ-NPs in a more physiologically relevant system, we agree that these studies would be beyond the scope of this study. This investigation is planned as a continuation of the current study.

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Referee #2

Evidence, reproducibility and clarity

This work is interesting but poses two problems.

On the one hand, both the introduction and the abstract contain too many elements that give a biased view of the extremely controversial literature. For example, the activity of Hydroxychloroquine and its toxicity have been explored most extensively on the "C19Early" website, which reports on trials carried out in a multitude of countries, including more than 300 trials with Hydroxychloroquine, and it is unreasonable in a scientific paper, designed to last, to report on the major beliefs at a given moment in order to develop a work that has nothing to do with this debate. The same applies to the efficacy of the vaccine. It is difficult to say that the vaccine was poorly distributed, with 20 billion doses, making it the most widely distributed vaccine in the history of mankind in such a short space of time, with results that were not as spectacular as the studies predicted, since the epidemic continued at a comparable level. I suggest that the authors concentrate on their work rather than getting involved in the controversies that are developing around treatments and vaccination.<br /> The substance of the work is very interesting, but experience shows that the idea that by testing one isolate you can generalize about all other viruses is not accurate. Viruses mutate. SARS-CoV-2 has shown an exceptional capacity for mutation, and the mechanism by which viruses enter cells by endocytosis or membrane fusion plays a role in their exposure to products concentrated in the lysosome. Viruses that enter by membrane fusion (including certain isolates of SARS-CoV-2) should not a priori be as sensitive because they are not subject to phagolysosome fusion.

In this sense, it is important to evaluate efficacy on several viral strains and not on a single strain, as has long been the case for acute viral infections. As with HIV, viruses can present natural or acquired resistances linked to evolution under selection pressure or not.<br /> In practice, we cannot rely on testing two viruses, one that has disappeared (Wuhan) and the first virus of the Omicron generation (B1), to assess the therapeutic capacity of a new strategy.

Significance

This work is interesting but poses two problems.

On the one hand, both the introduction and the abstract contain too many elements that give a biased view of the extremely controversial literature. For example, the activity of Hydroxychloroquine and its toxicity have been explored most extensively on the "C19Early" website, which reports on trials carried out in a multitude of countries, including more than 300 trials with Hydroxychloroquine, and it is unreasonable in a scientific paper, designed to last, to report on the major beliefs at a given moment in order to develop a work that has nothing to do with this debate. The same applies to the efficacy of the vaccine. It is difficult to say that the vaccine was poorly distributed, with 20 billion doses, making it the most widely distributed vaccine in the history of mankind in such a short space of time, with results that were not as spectacular as the studies predicted, since the epidemic continued at a comparable level. I suggest that the authors concentrate on their work rather than getting involved in the controversies that are developing around treatments and vaccination.<br /> The substance of the work is very interesting, but experience shows that the idea that by testing one isolate you can generalize about all other viruses is not accurate. Viruses mutate. SARS-CoV-2 has shown an exceptional capacity for mutation, and the mechanism by which viruses enter cells by endocytosis or membrane fusion plays a role in their exposure to products concentrated in the lysosome. Viruses that enter by membrane fusion (including certain isolates of SARS-CoV-2) should not a priori be as sensitive because they are not subject to phagolysosome fusion.

In this sense, it is important to evaluate efficacy on several viral strains and not on a single strain, as has long been the case for acute viral infections. As with HIV, viruses can present natural or acquired resistances linked to evolution under selection pressure or not.<br /> In practice, we cannot rely on testing two viruses, one that has disappeared (Wuhan) and the first virus of the Omicron generation (B1), to assess the therapeutic capacity of a new strategy.

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Referee #1

Evidence, reproducibility and clarity

Summary

Petcherski et al describe a nanoparticle delivery system to deliver mefloquine, a inhibitor of viral endocytosis, into cell line models of coronavirus replication. They describe the generation of these nanoparticles and test their antiviral efficacy against 3 different beta coronaviruses OC43, MHV and SARS-CoV-2, including the omicron variant.

Major Comments

The authors claim that MFQ loaded nanoparticles have reduced cytotoxicity compared to 'free MFQ' dissolved in DMSO, however with the NP data and free MFQ data not plotted with the same units this conclusion is hard to reach (Fig.2). While I appreciate the molar units are presented in the text - the reduction in cytotoxicity with MFQ-NP appears to be relatively minor in the both the Calu3 and Vero cell models (doubling in IC50 in both instances). This may indicate quite a narrow therapeutic window for antiviral efficacy without unwanted cytotoxicity. Can the authors replot the data on scales using either molar or ug/ml and use the same dose range for all treatments to enable statistical determination as to whether MFQ-NP significantly reduce cytotoxicity.

To test the antiviral efficacy of the MFQ-NP the authors adopt 2 infection systems, either treating cells pre or post infection. The authors either use fluorescently tagged reporter viruses (OC-43/MHV) or immunofluorescence to visualise and quantify viral infection in cell-line models. Given a key aim of this paper is to determine whether MFQ-NP rather than free MFQ is a superior treatment option, it is challenging to assess this with the data presented in figures 5-6. The units of treatment between NP, MFQ-NP and free MFQ again differ, and the molar dose range of MFQ-NP and free NP is not the same. This makes it very hard to conclude whether MFQ-NPs are more effective then free MFQ. Formal dose response curves with the same dose of empty-NPs, MFQ-NPs and free MFQ are needed here, preferably with match cell viability data using the same assay as figure 2.

The claim that MFQ may impact cell entry is not supported by the data in the paper. At minimum, the impact of treatment on expression of viral entry receptors for all 3 viruses should be performed, viral attachment assays (see PMID 35176124) and viral pseudoparticle assays. Further the conclusion that MFQ inhibits replication as well as entry is not fully supported by the data presented. This could be improved using a single cycle infection experiment using a synchronised infection protocol. The gold standard to determine impacts on replication would be the use of a viral replicon however I appreciate the technical difficulties in performing these experiments.

Finally while animal experiments are likely beyond the scope of this study, use of air-liquid interface cultures of lung epithelial cells would be a significant improvement to the work and provide further support to their conclusions in a physiologically relevant system.

Minor Comments

It is not clear why the authors used cell number as a measure of viability compared to the MTS assay used in figure 2.

Why did the authors adopt a different pre-treatment infection protocol for SARS-CoV-2 compared to MHV and OC43?

Further discussion in the introduction as to the potential mechanism of action of MFQ should be included. I would also suggest the authors read the work by Elizabeth Campbell an Bruno Canard concerning the potential difficulties in designing direct acting antivirals for coronaviruses.

The figure legends lack detail concerning the number of replicates and statistical comparisons. For viral infections MOIs used are also absent.

Significance

This work has good potential but is let down by the execution of the experimental design. The use of NP for antiviral drugs is a very interesting area and could greatly contribute to drug design for this viral family.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

In this study, the authors made a two-component homing modification gene drive in Anopheles coluzii with a different strategy than usual. The final drive itself targets and disrupts the saglin gene that is nonessential for mosquitoes, but important for the malaria parasite. The drive uses several gRNAs, and some of these target the Lp gene where an anti-malaria antibody is added, fused to the native gene (this native gene is also essential, removing nonfunctional resistance alleles at this locus). In general, the system is promising, though imperfect. Some of the gRNAs self-eliminate due to recombination of repetitive elements, and the fusion of the antimalaria gene had a modest fitness cost. Additionally, the zpg promoter was unable to operate at high efficiency, requiring use of the vasa promoter, which suffers from maternal deposition and somatic expression (the latter of which increased fitness costs at the Lp target). The manuscript has already undergone some useful revisions since its earliest iteration, so additional recommended revisions are fairly modest.

Line 43-45: The target doesn't need to be female sterility. It can be almost any haplosufficient but essential target (female sterility works best, so it has gotten the most study, but others have been studied too).

--- We agree. However, this paragraph focused on previous achievements in malaria mosquitoes, for which suppression gene drives spreading lethality rather than female sterility have not been reported to our knowledge. Even the targeting of doublesex, which is a sex determination rather than female fertility gene, results in female sterility (Kyrou et al. 2018). However, we inserted the possibility of female killing by X-shredder GD (Simoni et al., 2020).

Line 69: A quick motivation for studying Anopheles coluzii should be added here (since gambiae is discussed immediately before this).

---Thank you for drawing our attention to this point. We modified the sentence to:

_Here, we present the engineering of the Lipophorin (Lp) essential gene in Anopheles coluzzii, a prominent member of the A. gambiae species complex and a major malaria vector in sub-Saharan Africa.

_

Introduction section: It might be helpful to break up the introduction into additional paragraphs, rather than just two.

--- We followed this suggestion and broke up the introduction into 5 paragraphs to make it more breathable.

Introduction last part: The last part of the introduction reads more like an abstract or conclusions section. Perhaps a little less detail would fit better here, so the focus can be on introducing the new drive components and targets

--- We have followed this suggestion and substantially shortened this last part of the introduction.

Line 207-213: This material could go in the methods section. There are some other examples in the results that could be similarly shortened and rearranged to give a more concise section.

--- We moved the long description from lines 207-213 to the Methods as suggested, and summarized it simply as:

Only mosquitoes displaying GFP parasites visible through the cuticle were used to infect mice.

We emphasize this point because in subsequent experiments using Saglin knockout mosquitoes, this enrichment for infected mosquitoes will probably attenuate the Plasmodium-blocking phenotype caused by Saglin KO, since mosquitoes lacking Saglin tend to be less infected (Klug et al., 2023). Elsewhere in the Results, we still provide detailed descriptions of procedures because we believe they aid understanding and assessing the quality of the experiments.

Line 283-287: I couldn't find the data for this.

--- Indeed we only summarized the data about the progeny of the [zpg-Cas9; GFP-RFP] line crossed to WT, as we didn’t judge these results worth detailing. Here is our record from one such cross:

GFP-RFP females x WT males  486 (50.7%) GFP+ and 472 (49.3%) GFP- larvae

GFP-RFP males x WT females  1836 (48.9%) GFP+ and 1925 (51.1%) GFP- larvae

This shows no significant gene drive. However in these progenies, a few GFP+ and non-RFP larvae, and a few RFP+ non-GFP larvae were noted by visual examination under the fluorescence microscope, without counting them precisely. Their existence testified to some weak homing activity mediated by zpg-Cas9 in the Lp locus.

We modified the sentence as follows to support our conclusion, and we propose to leave these detailed numbers here in our response, which will be published along with the paper.

In spite of the presence of the zpg-Cas9 and gRNA-encoding cassettes in the GFP-RFP allele, it was inherited in about 50% of male or female progenies, demonstrating little homing activity of the GFP-RFP locus after crosses to WT, except for the appearance of rare GFP-only or RFP-only progeny larvae, …

Line 291: Replace "lied" with "was".

----done.

Line 356: Homing in the zygote would be considered very unusual and is thus worthy of more attention. While possible (HDR has been shown for resistance alleles in the zygote/early embryo), this would be quite distinct from the mechanism of every other reliable gene drive that has been reported. Is the flow cytometry result definitely accurate? By this, I mean: could the result be explained by just outliers in the group heterozygous for EGFP, or perhaps some larvae that hatched a little earlier and grew faster? Perhaps larvae get stuck together here on occasion or some other artifact? Was this result confirmed by sequencing individual larvae?

---- We agree with your skepticism, especially given that the same is not seen in Suppl Fig 2A with a similar genotype setup, i.e., the vasa gene drive at the Lp locus, or in the G1 of populations 6 or 8 at the Saglin locus (Suppl. File 2). Unfortunately, it would take too much time at this point to re-create this line (which has been discarded) to re-examine this issue. Therefore, we acknowledge that another explanation than homing in the zygote may account for this result. Based on our empirical experience COPAS outputs are reliable: such outliers from the heterozygous population are usually not seen, and we always sort neonate larvae a few hours from hatching. Those 6% homozygous-looking larvae may come from a contamination with male pupae when female pupae were manually sorted for the cross to WT males, a human error that we cannot exclude. In this case, the true GFP inheritance would be closer to 79% than to 85%. For these reasons, we must back up from our initial statement as follows:

The progeny of these triple-transgenic females crossed to WT males showed markedly better homing rates (>79% GFP inheritance)

And edit the figure legend of Figure 4B to account for the alternative possibility of a contamination with males:

6% of individuals appeared to be homozygous, revealing either unexpected homing in early embryos due to maternal Cas9 deposition, or accidental contamination of the cross with a few transgenic males.

Results in general: Why is there no data for crosses with male drive heterozygotes? Even if some targets are X-linked, performance at others is important (or did I miss something and they are all X-linked). I see some description near line 400, but this sort of data is figure-worthy (or at least a table).

--- For the only example of functioning split gene drive at the Lipophorin locus on chromosome III, we do show homing results from heterozygous GD males in Suppl. Fig. 2A (91.2% homing in males inferred from ((40.7+53.1+1.8)-50)x2). We added this calculation of the homing rates in the figure legend. For full drive constructs in the Saglin locus on chromosome X (our final functional design), in addition to the data described in the text near line 400, male data showing “teleguided” homing at the Lipophorin locus on chromosome II is shown in Suppl. File 2 (see G2 of population 7, showing close to 100% homing at the GFP locus); the same data (less easy to assess) being converted into the G2 point of the graphs in Figure5.

Lines 362-367: What data (figure/table) does this paragraph refer to?

--- We apologize for the fact that this sentence was misleading. In this population, the genotype frequencies were not tracked at each generation but measured once after 7 generations. We rephrased (now lines 401-403) and now provide the measured values directly in the text:

We maintained one mosquito population of Lp::Sc2A10 combined with SagGDzpg (initial allele frequencies: 25% and 33%, respectively) and measured genotype frequencies after 7 generations. This showed an increase in the frequency of both alleles (G7: GFP allelic frequency = 59.2%, phenotypic expression of DsRed in >90% of larvae, n=4282 larvae),

Lines 405-406: There may be a typo or miscalculation for the DsRed inheritance and homing rate here. Should DsRed inheritance be 90.7%?

--- Thank you for spotting this. You are right, DsRed inheritance would be 90.7% if the homing rate were 81.4% as we mistakenly wrote. Actually DsRed inheritance was really 80.7% so our mistake was in calculating the homing rate: 61.4% is the correct value ((80.7-50)x2), now corrected in the manuscript.

Figure 5: The horizontal axis font size for population 8 is a little smaller than the others.

--- True. Corrected.

Line 454: In addition to drive conversion only occurring in females and the somatic fitness costs, embryo resistance from the vasa promoter would prevent the daughters of drive females from doing drive conversion. This means that drive conversion would mostly just happen with alleles that alternate between males and females.

--- We agree with this idea, although the impact of this phenomenon will depend on the extent of resistance allele formation in early embryos. We observed (Fig. 6) that failed homing mutagenesis in Saglin is not that intense, the sequenced non-drive alleles that were exposed 1-4 times to mutagenic activity in females either being mostly wild-type, or carrying mutations that often still left one or two gRNA target sites intact and vulnerable to another round of Cas9 activity. Therefore, alleles passed on from female to female may still undergo drive conversion to a large extent, that future experiments may be able to quantify.

Line 481: Deletions between gRNAs certainly happen, but I wouldn't necessarily expect this to be the "expectation". In our 2018 PNAS paper, it happened in 1/3 of cases. There were less I think in our Sciences Advances 2020 and G3 2022 paper. All of these were from embryo resistance from maternal Cas9 (likely also the case with your drive due to the vasa promoter). When looking at "germline" resistance alleles, we have recently noticed more large deletions.

--- We agree that the early embryo with maternally deposited Cas9 is probably the most prominent source of mutations at gRNA target sites. Perhaps naïvely we imagined that it would be easier for cells to repair two closely spaced DNA breaks by eliminating the intervening sequence, rather than stitching each break individually. Given that we sequenced many alleles carrying a single mutation, the lack of larger deletions may be explained by lower rates of Cas9 activity in Saglin, with mostly a single break at a time, due to limiting Cas9 amounts and their partial saturation with Lp gRNAs, and/or lesser accessibility of the Saglin locus compared to Lipophorin… We deleted the phrase “Contrarily to our expectation”.

Figure 6C: It may be nice to show the wild-type and functional resistance sequence side-by-side.

--- done

Lines 642-644: This isn't necessarily the case. At saglin, the nonfunctional resistance alleles may still be able to outcompete the drive allele in the long run. This wasn't tested, but it's likely that the drive allele has at least some small fitness costs.

--- We agree. We inserted this comment in a parenthesis in the text (now lines 644-645):

Unlike the first approach, this design may allow Cas9 and gRNA-coding genes to persist indefinitely within the invaded mosquito population (unless nonfunctional resistance alleles outcompete the drive allele in the long run).

A few comments on references to some of my studies:

Champer, Liu, et al. 2018a and 2018b citations are the same paper.

--- Duplicate in our reference library. Corrected.

For Champer, Kim, et al. 2021 in Molecular Ecology, there was a recent follow-up study in eLife that shows the problem is even worse in a mosquito-specific model (possibly of interest as an alternate or supporting citation): https://elifesciences.org/articles/79121

--- Citation added (line 68).

One of my other previous studies was not cited, but is quite relevant to the manuscript: https://www.science.org/doi/10.1126/sciadv.aaz0525<br /> This paper demonstrates multiplexed gRNAs and also models them, showing their advantages and disadvantages in terms of drive performance. Additionally, it models and discusses the strategy of targeting vector genes that are essential for disease spread but not the vectors themselves (the "gene disruption drive"), showing that this can be a favorable strategy if gene knockout has the desired effect (nonfunctional resistance alleles contribute to drive success).

--- your 2020 study will indeed now be useful to inform the design of multiplex gRNAs for various gene drives designs, in terms of number of gRNAs, distribution of their target sites, necessity to generate loss-of-function rather than functional resistance allele in the target gene (such as our Lp and Saglin pro-parasitic genes)… The notion of Cas9 saturation with increasing gRNA numbers is also important. When we initiated this project in 2018, we only had intuitive notions that multiplex gRNAs could improve the durability of GD and increase the chances of resistance alleles to be loss-of-function. We thus arbitrarily maximized the number of gRNAs for each of the two targets: 3 for each target in one design, 3 and 4 in another, which, according to your modelling, is luckily close to the optimal numbers for each locus. We now cite your paper as a GD design tool in the discussion about pathways to optimizing our system:

To further optimize GD design, modeling studies can now aid in determining the optimal number of gRNAs in a multiplex, depending on the specific GD design and purpose (Champer et al., 2020)__.

In addition to this and to the stabilization of multiplex gRNA arrays, other paths to improvement (…)

This one is less relevant, but is still a "standard" homing modification rescue type drive that could be mentioned (and owes its success to multiplexing): https://www.pnas.org/doi/abs/10.1073/pnas.2004373117<br /> The recoded rescue method was also used in mosquitoes (albeit without gRNA multiplexing) by others, so this may be a better one to mention: https://www.nature.com/articles/s41467-020-19426-0

--- We added the two references on what is now Line 663:

Lp::Sc2A10 depends on SagGD for its long-term persistence and spread in a population, and SagGD depends on Lp::Sc2A10 as a rescue allele of the essential Lp target for its survival. This design can be seen as a two-locus variation of rescue-type GDs (Adolfi et al., 2020; Champer et al., 2020)

Sincerely,<br /> Jackson Champer

Referees cross-commenting<br /> Other comments look good. One thing that I forgot to mention: for the 7-gRNA construct with tRNAs, the authors mentioned that it was harder to track, but it sounds like they obtained some data for it that showed similar performance. Even if this one is not featured, perhaps they can still report the data in the supplement?

--- This GD required examination of the mosquitoes at late developmental stages, such as the pupa, to score red fluorescence under control of the OpIE2 promoter, that is unfortunately late-active when expressed from the Lp locus. We precisely scored only the first 128 pupae arising from the progeny of the first obtained G1 [SagGD/+ ; Lp-2A10/+] females crossed to WT males. Among these:

• 115 were GFP+, DsRed+ (89.8%)

• 12 were GFP+, DsRed- (9.3%)

• 1 was GFP-, DsRed- (<1%)

This allowed us to roughly estimate the homing rates at 98.2% at the Lipophorin locus and 79.7% at the Saglin locus, which is similar to the other construct without tRNA spacers.

These approximate rates were confirmed by visual examination of progenies in two subsequent generations of [SagGD/+; Lp-2A10/+] males and females backcrossed to WT.

Reviewer #1 (Significance):

Overall, this study represents a useful advance. Aside from being the first report for gene drive in A. coluzii, it also is the first that investigates the gene disruption strategy and is the first report of gRNA multiplexing in Anopheles. The study can thus be considered high impact. There are also other aspects of the study that are of high interest to gene drive researchers in particular (several drives were tested with some variations).

--- We are grateful for your positive, constructive and in-depth analysis of our study!

Reviewer #2 (Evidence, reproducibility and clarity):

The authors initially created a transgenic mosquito colony expressing the Sc2A10 antibody fused to the lipid transporter Lipophorin, and tested the transmission-blocking activity of this transgene. Building off of previous findings that the Sc2A10 antibody inhibits sporozoite infectivity when expressed in mosquito salivary glands, the authors showed that found it was also efficient at inhibiting sporozoite infectivity when secreted into the hemolymph expressed under the lipophorin endogenous promoter in An. coluzzii. They then designed and tested two different gene drives utilizing the Sc2A10-Lipophorin fusion protein. In the first, the authors used a recoded allele of Lp-Sc2A10 while simultaneously utilizing gRNAs that targeted endogenous Lp in an effort to select for mosquitoes that expressed transgenic Lp-Sc2A10 due to the essential nature of Lp. However, this drive was unsuccessful because recoded Lp is necessarily heterozygous while the GD is entering the population, and Lp proved to be largely haploinsufficient. Further, the zpg promoter expressing cas9 was not effective in promoting homing of the gRNAs. In the second gene drive that was tested, authors made use of the endogenous Saglin locus, which expresses a natural agonist for Plasmodium, and is thus desirable to target for disruption in a gene drive that aims to reduce vector competence for Plasmodium. This gene drive also uses recoded Lp-Sc2A10 to replace the wild-type Lp allele, thus selecting for Sc2A10 expression, however this drive is not dependent on fitness of individuals with only one functional copy of Lp.<br /> The authors discovered that the efficacy of the zpg promoter to drive homing of cas9 is locus-dependent, limiting the success of their gene drive designs. They do show, however, that the Saglin gene drive succeeds at reaching high frequencies in mosquito populations using instead the vasa promoter to express cas9, and that these transgenic mosquitoes are able to reduce infectivity of sporozoites in a bite-back mouse model. However, they observe gene drive refractory mutations in the Lp gene, despite its highly conserved nature, showcasing the difficulty of avoiding drive resistance even in small populations of mosquitoes, and also observed deletions of gRNAs targeting both Lp and Saglin, further highlighting possible shortcomings in gene drive approaches. Together, these findings are useful to the field in walking the readers through an interesting and promising approach for a novel gene drive, and illustrating the challenges in engineering an efficacious and long-lasting drive.

Major comments:

As the authors are able to observe Plasmodium within mosquitoes, it would be useful to have these data in the manuscript pertaining to the prevalence and intensity of infection in mosquitoes prior to bite-back assays. If there are data or images that the authors could include, it would be helpful to show if there is a possibility that infection intensity is a variable that contributes to whether or not mice develop an infection. It would also be interesting to note whether there is a different in infection (oocysts or sporozoites) between transgenic mosquitoes and wild type mosquitoes.

--- This is a valuable suggestion. Please note that, in order to evaluate the transmission-blocking properties of the Lp-2A10 allele (acting at the sporozoite level), we discarded non-infected mosquitoes prior to bite-back experiments, so that infection prevalence was 100% in the mosquitoes retained for the bite-back. We have not systematically compared parasite loads between transgenic and control mosquitoes. In some experiments comparing Lp-2A10 mosquitoes and their control, we dissected a subset of the mosquito midguts after bite-back to visually ascertain that they showed roughly equivalent oocyst numbers between transgenic and controls. However, we have not precisely recorded these data. It is possible that slightly decreased lipid availability in Lp::2A10 mosquitoes (their lipophorin allele producing slightly less Lp than the WT) negatively affects the parasite, as suggested by previous studies highlighting the role of host lipophorin-derived lipids for parasite development in the mosquito (Costa et al, Nat Commun 2018; Werling et al. Cell 2019; Kelsey et al. PLoS Path 2023).

In the case of Lp-2A10 mosquitoes additionally containing a GD in Saglin, it is expected that they should carry lower parasite numbers than their controls, an effect of the Saglin knockout mutation alone (Klug et al., PLoS Path 2023). Re-inforcing the transmission blocking effect of the 2A10 antibody by reducing parasite loads via the Saglin KO was indeed our intention. Hence, having selected the most infected mosquitoes for our bite-back experiments likely attenuated this desired effect, but we still observed a 90% transmission decrease when the two modifications were combined, compared to a 70% decrease with Lp-2A10 alone. We do not plan to perform additional infections experiments for the current manuscript on Plasmodium berghei expressing Pf-CSP, but we do intend to record parasite counts in a follow-up study with an optimized SagGD transgene and Plasmodium falciparum infections. This will be of high relevance for potential future applications in malaria control.

The authors also go into significant detail in the discussion exploring ideas of how to optimize or improve this specific gene drive design. The authors should also stress further the applicability of their discoveries in other gene drive designs, and emphasize the lessons they learned in the difficulties encountered in this study and how these findings could guide others in their decision making process when choosing targets or elements to include in a potential gene drive approach.

--- We feel that we already emphasized these lessons in the manuscript, in the discussion and when justifying the chosen strategies in the Results section. Lessons for future designs include:

• inserting an antimalarial factor into an essential endogenous gene, preserving its function, can provide many benefits (high expression level, secretion signal that can be hijacked, endogenous introns can be hijacked to host a marker, inactivation by mutagenesis or epigenetic silencing being more difficult…);

• a distant-locus gene drive (as here in Saglin) could potentially drive several antimalarial cargoes at the same time, inserted in different loci;

• non-essential mosquito genes agonistic to Plasmodium are attractive host loci for a GD, an already old idea illustrated here by the case of Saglin;

• multiplex gRNAs are a viable approach to reduce the formation of GD-resistant alleles in essential genes and/or to increase the frequency of loss-of-function alleles, which will either disappear if the gene is essential or decrease vector competence if the gene is pro-parasitic. Hence gRNAs targeting intron sequences should be avoided in order to preserve this benefit, as illustrated by one of our Lp gRNAs targeting the first intron and that contributed to generate the only Lp viable resistance allele identified in this study;

• To increase long-term stability of the GD construct, repeats should be minimized in gRNA multiplexes through the use of a single promoter and various spacers (tRNAs, ribozymes?) – it remains to be seen if the 76-nucleotide gRNA constant sequence itself, necessarily repeated, will stimulate unit losses in a gRNA multiplex;

• The best promoter to restrict Cas9 expression to the germ line may be zpg in some but not all loci; the vasa promoter causing maternal Cas9 deposition may still be envisaged if resistance allele formation can be prevented by other means (targeting hyper-conserved essential sequence, multiplexing the gRNAs against an essential gene…).

Minor comments:

Line 44 - female sterility but also female killing approaches to crash pop. like X shredder, if authors would like to expand

--- Female killing citation of Simoni et al, 2020 added (line 45).

Lines 48-60 - Authors should add some references from the literature surrounding ethics and ecology studies related to gene drive release

--- we added: (e.g., National Academies of Science, Engineering, and Medicine, 2016; Courtier-Orgogozo et al., 2017; de Graeff et al., 2021) on lines 49-51.

Line 114 - Given the only moderate impacts of Saglin's role in Plasmodium invasion, I am not sure this saglin deletion is a convincing benefit for GD as it is probably not impactful enough alone - can the authors soften this statement?

--- while it’s correct that Saglin KO mosquitoes show a significant decrease only in P. berghei oocyst counts and not in prevalence when mosquitoes are heavily infected, they do show a significant decrease in both counts and prevalence upon infection with P. berghei and, most importantly_, P. falciparum_ when parasite loads are lower —a situation that is more physiological (e.g. prevalence of 65% and 13% in WT and Sag(-)KI mosquitoes, respectively, upon infection with P. falciparum - Klug et al., PLoS Path 2023). Therefore, for human-relevant P. falciparum infections, an impactful decrease in vector competence can be legitimately expected.

Line 126 -Can the authors provide rationale for expressing Sc2A10 with Lp instead of expressing it from salivary glands?

--- There are three reasons for this. First, we knew from the cited Isaacs et al. papers that the 2A10 antibody was efficient against transmission when expressed in the fat body, and from unpublished work (Maria Pissarev, Elena Levashina and Eric Marois) that anti-CSP ScFvs expressed in the fat body of transgenic mosquitoes blocked sporozoite transmission as efficiently as when expressed from salivary glands. This is certainly favored by the easy sporozoite accessibility to the antibody when both are in mosquito hemolymph. Of note, the transmission blocking results suggest that the binding of ScFv to CSP withstands the crossing of the salivary gland epithelium by sporozoites. Second, we were looking for a host gene expressed as high as possible to produce high levels of Sc2A10 antibody. Third, the host gene must be essential so that resistance alleles would not be viable.

We agree that it would also be possible to use a salivary gene instead of Lp as a host for this antimalarial factor. In this case, a same-locus gene drive may have functioned, but the advantages of the host locus being an essential gene would be lost, at least partially, as genetic ablation of the salivary gland, albeit slowing blood uptake, does not prevent mosquito viability and reproduction (Yamamoto et al., PLoS Path 2016).

Line 140 - Can authors give any comment on why these regions of Lp were chosen to be recoded / targeted with gRNAs?

--- inserting Sc2A10 just after the cleaved Lp secretion signal, and N-terminally to the rest of the Lp protein, was the goal, so that 2A10 would be secreted together with Lp and separated from both signal peptide and Lp by naturally occurring proteolysis. This constrained the choice of the target site to be at the junction between signal peptide and the remainder of Lp protein. An alternative design could have been to insert it between the two subunits ApoLpI and ApoLpII, with duplication of the protease cleavage site, or on the C-terminal extremity of the protein, but there would have been no intron in the immediate vicinity to knock-in a selection marker at the same time.

Line 171 - "stoichiometric"

--- Corrected.

Line 186 - Can the authors comment or speculate on why the expression levels of the fusion protein are expected to be lower than endogenous Lp?

--- We did not expect this. It is hard to predict whether and explain how insertion of exogenous sequences in a gene can alter its expression. Possible explanations include: the existence of harder-to-translate mRNA sequences in the Sc2A10 moiety; the addition of seven exogenous amino acids on the N-terminal side of ApoLpII (mentioned in M&M) possibly modifying the stability of the Lp protein; the modification of the intron sequence perturbing efficient intron excision and/or pre-mRNA expression due to the disruption of regulatory elements or to the new presence of the GFP gene in the antisense orientation (albeit expressed in the nervous system and not in the fat body); the presence of the exogenous Tub56D transcription terminator used to arrest GFP transcription possibly possessing bidirectional termination activity and lowering the mRNA level of the Lp allele…

Line 211 - Why were 6 mosquitoes used for these assays, and 10 mosquitoes used in later assays (Line 223)?

--- Mice were always exposed to groups of 10 mosquitoes, but not all 10 mosquitoes were necessarily biting the mice. We retained mice bitten by at least 6 mosquitoes for further analysis (M&M, lines 871-873 of the revised file).

Line 212 - I would also suggest using letters (Suppl. Table 2A,B,C etc) to refer the specific experiments and sections in the Table.

--- Implemented.

Line 225- 228 - The authors should mention in the text that homozygotes and heterozygotes do not differ in infection assays.

--- Added: Therefore, heterozygous mosquitoes showed a transmission blocking activity comparable to that seen in homozygotes.

Line 249 - Can the author comment on the impacts of population influx / exchange on the idea that the GD cassette need only be transiently in the population?

--- If Lp::Sc2A10 is fixed in the population and the GD gone, indeed an influx of WT alleles through mosquito immigration will begin to replace the antimalarial factor and drive it to extinction due to its fitness cost. As mentioned in the final paragraph of the discussion, this could be seen as an advantage to restore the original natural state—hopefully after malaria eradication! However, we regard a situation where Lp::2A10 never reaches fixation as more likely, with its spread being re-ignitable by updated GDs (line 741 of the revised file).

Line 273 - Can the authors comment on why this may have occurred more frequently than the expected integration of the GD cassette?

--- When a chromosome break is repaired, each side of the cut must recombine with the repair template. A possible explanation for our observation is that one side of the break recombined with the injected repair plasmid, while the other recombined with the intact sister chromosome (physiologically probably the preferred option). Since this situation still leaves truncated chromosomes, another repair event can join the plasmid-bearing chromosome end to the sister chromosome. The observation that complex rearrangement occurred frequently suggests that such events can be very common, but will usually go undetected due to the absence of genetic markers. Here, GFP on the intact sister chromosome served as a genetic marker to betray its unexpected involvement in the repair process.

Line 314 - Not all fitness costs are apparent through standard laboratory rearing as was performed in Klug et al. Authors could consider "no known fitness cost" instead.

--- We agree. This is what we meant by “no fitness cost in laboratory mosquitoes”. We changed this to “no fitness cost at least in laboratory conditions (Klug et al., 2023)” to make clear that this was tested.

Line 407 - don't start new paragraph (same with 409)

--- we removed these two lines, as we realized they contained an error, and made a correction on line 420 of the revised manuscript.

Line 408 - I'm not sure it's clear why all these populations were kept for a different number of generations - can the authors clarify?

--- Populations 1 and 2 were the oldest founder populations, therefore maintained for the longest time. As described in the text, all other populations were derived from populations 1 and 2 later in time by outcrossing a subset of individuals to WT mosquitoes. For these derived populations, we reset the clock of generation counting to 0 as we monitored the homing phenomenon “from scratch” in transgenic males crossed to WT, and in transgenic females crossed to WT. Resetting the clock resulted in an apparent lower number of generations for these derived populations. In addition, some of them were discarded early, usually after reaching a stable state, as it was difficult to maintain so many populations in parallel over a long period of time.

Line 558 - "10/12 mice" not immediately clear - the authors could be more specific about how data was combined here

--- Thank you for pointing out this ambiguity. We replaced by: the absence of infection in a total of 10 out of 12 mice showed… (line 561)

Line 586 - Since there do appear to be some fitness costs associated with the Sc2A10 version of Lp, might it be expected that fitness costs imposed by the transgene itself could lead to selection pressures leading to its loss? Or do the authors think that these fitness costs are prevented from causing selection against Sc2A10 due to the design of the transgene such that its translation is a prerequisite for Lp's translation? Is the fact that its removal occurs more rapidly than Lp's any indication that selection against the persistence of Sc2A10 may occur?

--- Yes, we believe that Lp::Sc2A10 will progressively disappear, replaced by the WT allele, as shown in Figure 1C, in the absence of a GD stimulating its maintenance and spread. In the Lp::Sc2A10 transgene, translation of Sc2A10 is indeed a prerequisite for Lp translation, imposing a degree of genetic stability of this transgene in terms of sequence integrity, but this does not mean that the locus cannot be outcompeted by the WT under natural selection, so that long-term persistence of Lp::Sc2A10 depends on the presence of the GD, as outlined in lines 669-672. As the GD itself can disappear due to the accumulation of resistance alleles, we expect a progressive lift of its pressure to maintain Lp::Sc2A10 and both loci to be progressively lost, a form of reversibility that may be regarded as desirable (lines 773-776 in v2, 741-743 in v3). Alternatively, both transmission blocking alleles could be maintained by releasing an updated version of the dual GD.

Line 659 - add some further detail to this - how do you envision this to occur?

--- We have deleted this paragraph, as it hypothesized that SagGD could frequently be transmitted to the next generation in the absence of Lp::2A10, which is not the case (it would be lethal, and Lp::2A10 homing is anyway extremely efficient). After a putative field release of [SagGD / Y; Lp::2A10/ Lp::2A10] males, both transgenes should rapidly be introgressed in the field’s genetic background.

Line 635 - Long paragraph, should be broken up or removal of text. Some of these ideas could possibly be made more concise to improve readability. There are many different hypotheticals that are expanded upon in the discussion.

--- We admit that this paragraph in the discussion was long and dense. We have split it into 4 smaller paragraphs to better separate the concepts that we want to discuss, and have deleted the part mentioned in the above point.

Line 677 - This scenario seems potentially unrealistic considering the only subtle impacts of Saglin deletion on vector competence, and the potential for population exchange in mosquito populations to dilute out these alleles if the drive begins to fail. Can the author comment or potentially decrease emphasis on such scenarios?

--- while Saglin KO mosquitoes show a moderate decrease of infection prevalence in the context of high infections, the Saglin KO decreases parasite loads in all cases, and most importantly, also prevalence upon physiological infections with P. falciparum (Klug et al., PLoS Path 2023 and see our response to your comment to line 114 above). This yields a higher proportion of non-infected mosquitoes. Therefore, the impact of Saglin mutations should be stronger for the epidemiology of human infections with P. falciparum than in laboratory models of infections where parasite loads are very high.

We agree that mosquito migration in natural populations would progressively dilute out the beneficial alleles once the GD effect ceases. The epidemiological impact is difficult to predict and will strongly depend on the durability of the GD and on the intensity of genetic influx from adjacent mosquito populations.

Line 708 - Can the authors speculate on why zpg is sensitive to local chromatin and elaborate on possible solutions or consequences for other drive ideas? This seems broadly important.

--- We do not precisely know why the zpg promoter is more sensitive to local influences than the vasa promoter, but this phenomenon seems common for other promoters as well (e.g., the sds3 promoter as opposed to the shu promoter in Aedes aegypti (Anderson et al., Nat Comm 2023)). It is possible that the vasa promoter is better insulated from local repressive influences, perhaps by insulating elements akin to gypsy insulators in Drosophila. Knowledge of genetic insulators active for mosquito genes is lacking as far as we know. Characterization of efficient mosquito insulators, for example if one could be identified within vasa, and their combination with zpg or sds3 promoter elements, could potentially improve the locus-independent activity of such promoters. Alternatively, a natural and ideal promoter may still be found showing both an optimal window of expression of Cas9 in the germline, and little susceptibility to local repression.

Line 737 - The suggestion of releasing laboratory-selected resistance alleles in the absence of further context may be provocative and unnecessary here.

--- We didn’t intend to sound provocative, but are interested in the idea of simple resistance alleles with limited sequence alteration that could be selected in the lab, and released to block a gene drive that turned undesirable, so we wanted to share it with the reader. Mutations in the Lp and Saglin loci, preserving their functions, can be limited to one or few nucleotide changes in the gRNA target sites, as illustrated by the mutants we sequenced. Lab population of GD mosquitoes can, therefore, be a source of GD refractory mutants that could be leveraged in recall strategies.

Line 850 - unnecessary comma

--- Corrected.

Line 854 - change to "after infection, moquitoes were "

--- Changed.

Figure 1 - Not clear what is intended to be communicated by shapes portraying proteins / subunits - consider more detailed illustration of mosquito fat body cells synthesizing and secreting proteins rather than words in text box with arrow to clearly demonstrate the point of this figure.

--- We propose a new version of figure 1 to better illustrate the fat body origin of Lp and 2A10. We have also re-worked the graphic design to improve several figures.

Figure 3 - I recommend rearranging this figure so that B comes before C, visually. The proportions for the design of in B should also match those used for A.

--- We have followed these recommendations in the new Figure 3, and also used more logical color codes for the gRNAs and their target genes.

Figure 5 - It is unclear to me why some Populations were maintained for such different lengths of time.

--- Same point as above for line #408: Populations 1 and 2 are the oldest founder populations, therefore maintained for the longest time. As described in the text, all other populations were derived from populations 1 and 2 later in time by outcrossing to WT mosquitoes, resulting in a lower number of generations for these derived populations. In addition, some of them were discarded earlier, usually after reaching a stable state, as it was not possible to maintain so many populations in parallel for a long period of time.

Figure 7 - Ladder should be labeled on the gel. It may also be helpful for the author to indicate clearly exactly which mosquitoes were shown by sequencing to have these different deletions, as it is occasionally unclear based on band sizing.

--- we have added the ladder sizes as well as a numbering of individual mosquitoes on Figure 7. We sequenced 4 gel-purified small -type B- amplicons of Population 1 individually (#1, 2, 4, 6), and a pool of 4 type B amplicons from Population 7 (pooled #2, 4, 5, 6) as well as two samples of several pooled gel-purified large -type A- amplicons from Population 2 (pool of samples #2, 3, 4, 5, 6, 8, 9, 11, 12) and from Population 7 ( pool of #1, 3, 7, 11, 12). This information now also appears in the material and methods section (PCR genotyping of the SagGDvasa gRNA array).

Line 996 - given that there is a size band on the right line of this gel also, can authors crop the gel image to eliminate unnecessary lanes a and b from this figure without losing information needed to interpret this blot?

--- we agree that this would make the message easier to understand, but cropping lanes a and b would place WT control and Lp::Sc2A10 homozygotes on two separate images, even if a size marker is present on each. We prefer keeping the raw image to facilitate direct comparison of the band sizes, making clear that this was a single protein gel.

Line 1070 - 12 out of how many sequenced mosquitoes?

--- 12 mosquitoes from each of these four populations served as PCR templates to generate figure 7. A subset of amplicons were sequenced individually or pooled, as described above and now in Methods. All sequencing reactions of type A and type B amplicons showed consistent results.

Line 1078 - Can remove some detail like % of agarose, and replication of results with different polymerase as these are already in methods.

--- Done.

Line 1098 - "Unbless"

--- Corrected

Reviewer #2 (Significance):

This study illustrates a wide range of issues pertinent for gene drive implementation for malaria control, and as such is of value to the field of entomologists, genetic engineers, parasitologists and public health professionals. The gene drive designs explored for this study are interesting largely from a basic biology perspective pertinent mostly to specialists in the field of genetic engineering and vector biology, but highlight challenges associated with this technology that could also be of interest to a broader audience. A transmission blocking gene drive has not yet been achieved in malaria mosquitoes, and is thus a novel space for exploration. As a medical entomologist that works predominantly outside of the genetic engineering space, I have appreciated the detail the authors have provided with regard to their rationale and findings, even when these findings were inconsistent with the authors' primary objectives or expectations.

--- Thank you for your positive assessment and for this in-depth evaluation of our data.

Reviewer #3 (Evidence, reproducibility and clarity):

The study by Green et al. generated a gene drive targeting both Saglin and Lipophorin in the Anopheles mosquito, with a view to blocking Plasmodium parasite transmission. This is a highly complex but elegant study, which could significantly contribute to the design of novel strategies to spread antimalarial transgenes in mosquitoes.<br /> Overall, this is a complex study which, for a non-specialist reader gets quite technical and heavy in most parts. Despite this, there are key points showing that suppression gene drive may not be the way forward in this instance. However, I would advise explaining certain elements in more detail for the benefit of the general readers. I only have minor points for the authors to address:<br /> 1) Please point out for the general reader that Anopheles coluzzii belongs to the gambiae complex, since you explain that gambiae are the major malaria spreaders in sub-Saharan Africa.

--- done in the introduction (lines 71-73) also in response to Rev. 1

2) The authors pretty much give all results in the last part of the introduction, could the intro be shortened by removing these parts, or just highlighting in a single paragraph the main take home message?

--- We have condensed this part to highlight the take home messages in the last paragraph, also in response to Rev. 1.

3) Why is Vg mentioned? It is only mentioned once and doesn't have any other mention through the manuscript.

--- this introduces the two proteins that are by far the most abundant, and present at similar levels, in the hemolymph of blood-fed females, Vg being also prominent on the Coomassie stained gel of fig.1. We mention Vg also because it represents another excellent candidate locus to host anti-plasmodium factors, as discussed later on lines 600-610 of the Discussion section.

4) Please make it clearer for non-specialists why Cecropin wasn't used.

---On lines 630-636 we explain that we decided to leave out Cecropin to avoid potential additional fitness costs due to expression at all life stages in the fat body, as opposed to solely in the midgut after blood meal (Isaacs et al. PNAS 2012); and to avoid complexifying the anti-Plasmodium Lipophorin locus in a way that could further reduce the functionality of the Lp gene. We also had prior knowledge from unplublished work that Sc2A10 alone was sufficient to block sporozoite infectivity.

5) Why were homozygous and not heterozygous transgenics transfected if there is such as fitness cost to homozygous mosquitoes?

--- the fitness cost of homozygous mosquitoes is actually mild, unnoticeable if homozygotes are bred in the absence of competing heterozygotes and wild-types (lines 151-156). Microinjection experiments to obtain the different versions of SagGD were, therefore, performed on either the heterozygous or homozygous line. As for infection assays, the anticipated effect of gene drive is to promote homozygosity at the Lp::Sc2A10 locus. For this reason, it made sense to test the vector competence of homozygotes, in addition to the fact that the Plasmodium-blocking phenotype was expected to be stronger (and thus, easier to document) with two copies of the transgene. Only after obtaining a large dataset from infection assays with homozygotes did we test heterozygotes and found that they actually had a similar phenotype.

6) Line 211 - what was the average number of infected mosquitoes used per infection for each mosquito strain?

--- As described in the text (lines 204-206 of v2; 208-212 of the revision) and in the Methods (lines 868-873), non-infected mosquitoes were discarded prior to performing the experiment using 10 infected mosquitoes per mouse, and we discarded mice bitten by fewer than 6 mosquitoes. So at least 6 infected mosquitoes bit each mouse (often 8-9).

7) Line 219 - please be clearer regarding this being infection detected in the blood.

--- We replaced « infection » with « detectable parasitemia in the blood »

8) Line 320 - please clarify why the zpg promoter was used.

--- The advantages of zpg are mentioned in lines 257-258 and 320-322 (revised file).

9) Line 375 - what was the rationale for using so many gRNAs?

--- 3 or 4 gRNAs against Lipophorin and 3 gRNAs against Saglin, amounting to a total of 6 or 7 gRNAs against the two loci. The rationale is explained on lines 249-253 : the goal was to maximize the chance of causing loss-of-function mutations in the essential Lp gene and to favor elimination of GD resistant alleles by natural selection, in case of failed homing. For Saglin which is a non-essential gene, we wanted to ensure loss-of-function of failed homing alleles to achieve a reduction in vector competence, even if GD-resistant alleles accumulate. We sought to make this rationale clearer by adding a sentence on lines 328-332:

Multiplexing the gRNAs was intended to promote the formation of loss-of-function alleles in case of failed homing at the Lp and Saglin loci: non-functional alleles of the essential Lp gene would be eliminated by natural selection while non-functional Saglin alleles would reduce vector competence.

Line 555 - please state how long post bite back parasite appears in infected mice.

--- We changed this sentence to : …two of these six mice developed parasitemia six days after infection<br /> (line 556).

Reviewer #3 (Significance):

This is potentially a highly significant study that could provide a vital mechanism for generating efficient gene drives. Although highly technical and complex in most parts, with a little clarification in certain areas this manuscript could be of great value to a general readership.

--- Thank you for your appreciation and thoughtful evaluation of our manuscript.

Reviewer #4 (Evidence, reproducibility and clarity):

The authors hijacked the Anopheles coluzzii Lipophorin gene to express the antibody 2A10, which binds sporozoites of the malaria parasite Plasmodium falciparum. The resulting transgenic mosquitoes showed a reduced ability to transmit Plasmodium.

The authors also designed and tested several CRISPR-based gene drives. One targets Saglin gene and simultaneously cleaves the wild-type Lipophorin gene, aiming to replace the wildtype version with the Sc2A10 alele while bringing together the Saglin gene drive.

Drive-resistant alleles were present in population-caged experiments, the Saglin-based gene drive reached high levels in caged mosquito populations though, and simultaneously promoted the spread of the antimalarial Lp::Sc2A10 allele.

This work contributes to the design of novel strategies to spread antimalarial transgenes in mosquitoes. It also displays issues related to using multiplexing gene-drive designs due to DNA rearrangements that could prevent the efficient spread of the gene drive in the long term.

This is tremendous work considering how many transgenic lines and genetic crosses are performed using mosquitoes. The conclusions are supported by the data presented, and some modifications regarding the experimental design description through text/figure improvements would facilitate the reading and flow of the paper.

Here some questions/comments:

• Line 124-125: Reference?

--- added

• Line 133-134: Reference?

--- added

• Table 1: It seems the authors have some issues recovering a good amount Sc2A10 from hemolymph samples. Is this a problem of the antibody per se? Is it the Lp endogenous promoter weak? Could this be improved by placing the antibody in a different genomic region? Alternatives could be discussed.

--- The 2A10 antibody must be initially produced in the same, very high, amounts as the Lp endogenous protein with which it is co-translated. Therefore, its low relative abundance must result from faster turnover or stickiness to tissue, as hypothesised on lines 176-177. We believe that virtually any other endogenous promoter would be weaker than Lp and produce lower Sc2A10 levels.

• Fig.1B: It would be nice to have a representation of the genome after integration. You could add a B' panel or just another schematic under the current one.

--- In agreement with this suggestion and that of rev. 3, we added a new panel in 1B.

• Supplementary Fig.1b: Could the authors explain the origin of the (first) zpg promoter used? Is it from An. Coluzzii? It seems they use a different one in the gene drive designs later (see comments below too).

--- We initially cloned a PCR-amplified zpg promoter region of the same size as the version published by Kyrou et al., from genomic DNA from our colony of A. coluzzii. The resulting promoter fragment harbored several single nucleotide polymorphisms (SNPs) compared to published sequences, as typically observed when cloning genomic fragments due to high genetic diversity in Anopheles species. Such SNPs are not usually expected to affect promoter activity, but are difficult to distinguish from PCR mutations which, in turn, could decrease or abolish promoter activity if mutating an essential transcription factor binding site. For this reason, our next constructs were based on the validated zpg sequences from Kyrou et al. The first cloning strategy was described in the results section but was missing in the material and method section. This is now corrected (lines 773-779).

• Fig.3: Please, correct to A, B, C order. Current one is A, C, B.

--- Done.

Could the authors include a schematic of the final mosquito genome after integration? I can see they are targeting two different locations (Saglin and Lp). It is unclear though from the figure where the Sc2A10-GFP is coming from. I understand this represents the mosquito genome as you injected heterozygous animals already containing the Sc2A10-GFP. Maybe label the Sc2A10-GFP as mosquito genome or similar? A schematic showing mosquito embryos already carrying this and then the plasmid being injected could help.

--- Figure 3 does not represent the injection of new transgenic constructs. Instead, it shows the conversion process of chromosomes X and II in a germ cell carrying both transgenes in the heterozygous state, to illustrate how the dual gene drive can spread in a population after WT mosquitoes mated with transgenics carrying both the SagGD and Lp-2A10 alleles. We have re-worked the graphic design of this figure and modified its title to make this more clear.

• Line 330-331: Do you know the transgenesis efficiency? Did the authors make single or pools for crossing and posterior screening? It would be interesting to know about transgenesis rates to inform the community.

--- we no longer perform single crosses for transgenesis, as batch crosses ensure higher recovery of transgenics due to the collective reproductive behavior (swarming) in Anopheles. Therefore, we cannot precisely calculate the transgenesis efficiency. However, >60 positive G1s from a pool of 36 G0 males crossed to WT females is indicative of a rather high integration efficiency. We consistently observe high efficiency of transgene integration when using the CRISPR/Cas9 system, that we estimate to be about 5-fold more efficient than docking site transgenesis, and much more efficient than piggyBac mediated transgenesis.

• Line 357/Fig.4B: Could the authors explain in the text GFP+ vs. GFP++?

--- GFP++ was meant to indicate higher intensity of GFP fluorescence than GFP+, due to two copies of the transgene versus one, but see our response to reviewer 1’s comment to line 356 about the questionability of homing in the zygote.

• Line 357: Where is the vasa promoter that made the "rescue" coming from? Is it amplified from Coluzzii? Please, include this explanation for clarification. Why the authors think the zpg from Kyrou et al 2018 works for the cassette integration but not for homing? They discuss positional effects, any references showing that?

--- We amplified the vasa promoter from A. coluzzii using primers CggtctcaATCCcgatgtagaacgcgagcaaa and CggtctcaCATAttgtttcctttctttattcaccgg (annealing sequence underlined) to have a fragment equivalent to that (vas2) characterized in Papathanos et al, 2009. We have now added this information in the Methods under Plasmid construction. This is the only source of vasa promoter used in this work.

About zpg promoter activity : we have past experience suggesting that promoters, such as the hsp70 promoter from Drosophila, can be sufficient to express enzymatic activities in embryos injected with helper plasmids, even though the same promoters appear to become inactive once integrated in the genome. This may be due to injected “naked” plasmids being readily accessible to the transcription machinery, unlike organized chromatin. A recent reference showing genomic positional influences on promoter efficiency is Anderson et al., 2023, which we have added on line 710 of the Discussion.

• Line 362: No reference to figure nor table.

--- These data (numbers from a COPAS analysis) are provided directly in the text in this sentence (which has been clarified in response to Reviewer 1). See lines 364-369 of the revision.

• Line 417: The text brings the reader back to Fig.3C. Could the authors move this panel for easier flow of the paper?

--- We agree that positioning of this panel in Figure 3 is a bit awkward, but this western blot pertains to the characterization of the insertion shown in Fig. 3. Placing it after COPAS analyses would be equally awkward.

• Line 472-474: How many WT alleles were recovered? It is not stated unless I missed anything, which is possible.

--- We refrained from providing a quantification of this, and focussed on qualitative results, as we didn't trust the quantitative representativity of our high-throughput amplicon sequencing results in terms of allele frequency in the sampled mosquito population. A large fraction of sequenced reads corresponded to PCR artefacts such as primer dimers and unspecific short amplicons, potentially affecting the relative frequencies of gene-specific amplicons. However, among the sequenced gene-specific amplicons, WT alleles were the majority (lines 474-475).

• Fig.5. Could the authors discuss why the observed DsRed-gene drive drop in population 1 at ~18 generation? The population gets to the point where only 50% of the population carries the Cas9-DsRed cassette. Considering that the Saglin gene drive only converts through females (inserted into the X chr.), and some indels could be generated by generation 20, how do you explain the great recovery until fully spreading into the population?

--- We agree that this is somewhat puzzling. We don’t have a satisfactory explanation beyond stochastic effects, possibly promoted by population bottlenecks: although we strived to maintain these populations at a high number of individuals at each generation, we cannot exclude that at a given generation only a relatively small fraction of individuals contributed to the next generation, leading to fluctuations in allelic frequencies. This would be possible particularly for populations 1 and 2, which were not monitored frequently between generations 10 and 18, at which point additional populations 5-8 were established and it was decided that close monitoring of all populations was important.

It seems to me populations 3-8 are new cage experiments by randomly picking mosquitoes from populations 1 and 2 (at a specific generation) and mixing them with WT individuals. Could the authors explain the reasoning for these experiments? I believe populations 3-8 deserves a different figure (main or supplementary) describing how they were seeded. It is confusing having everything together as these experiments were performed differently way and for a different reason compared to populations 1 and 2. Some cage schematics and drawings would help in understanding the protocol strategy for populations 3-8.

--- This is correct for populations 3 and 4 that indeed originated from randomly picking mosquitoes from populations 1 and 2 at generation 10 and mixing them with WT individuals. Populations 5, 6, 7 and 8 are crosses between generation 16 transgenic partners of one sex to WT of the other sex, as indicated above the COPAS diagrams provided in Suppl. File 2. We apologize for having insufficiently described how each population was assembled and now provide more details (lines 422-429, in the figure 5 legend, and G0 crosses spelled out on top of each population diagram). In setting up these populations, we wanted to test the effects of various routes by which the transgenes may be introduced into a wild mosquito population: release of unsorted transgenic males + females, or release of one sex only (probably males in the field, but the crosses with transgenic females as with transgenic males also served to re-quantify homing in the second generation of each cross).

The modified text reads as follows:

Populations 3 and 4 were established by mixing randomly selected transgenic mosquitoes (both males and females of generation 10) from populations 1 and 2, respectively, with wild-types, to mimic what may occur in a mixed-sex field release. Populations 5-8 were established by crossing single-sex transgenic mosquitoes to WT of the opposite sex, both to mimic a single-sex field release and to re-assess homing efficiency after 16 generations.

Also, could you add homozygous and heterozygous labels in the figure legend to help understanding the different lines.

--- As indicated on the side of the figure and in the figure legend, lines don’t represent homozygous vs. heterozygous frequency, but allele frequency (continuous lines), and frequency of mosquitoes carrying the transgene (dotted lines). In the figure legend we now provided the calculation formulas for gene frequency: [ 2 x (number of homozygotes) + (number of heterozygotes)] / 2 x (total number of larvae) for the autosomal Lp::2A10 transgene, and [ 2 x (number of homozygotes) + (number of heterozygotes) ] / 1.5 x (total number of larvae) for the X-linked SagGD transgene.

• Fig.6: The authors sequenced non-DsRed individuals from generations 3-4. The authors also mentioned they sequenced mosquitoes from generation 32 (Fig.7). Interestingly, they observed that these mosquitoes were missing a piece of the cassette (they contained 2 gRNAs instead of 7). Since the amplicons only cover the gRNA portion, a PCR covering the Zpg-Cas9 portion would be ideal to confirm that only the gRNAs are missing. Sampling DsRed+ mosquitoes from generations 3, 18 and 31 (populations 1 and 2) and carrying out these experiments is recommended. Although unlikely, I would be worried about the Cas9 being deleted due to unexpected DNA rearrangements; in that case, the cassette would contain the DsRed marker alone.

--- Thank you for this suggestion. We no longer have DNA samples from the earlier generations. Thus, we genotyped 7 DsRed positive male mosquitoes from each of current populations 1, 2 and 7 (generation 41 since transgenesis) for the presence of Cas9. We detected a Cas9-specific amplicon of 1.6 kb in 21/21 sampled DsRed positive mosquitoes, in parallel to the same shortened gRNA arrays detected in earlier generations. This suggests that the Cas9 part of the transgene was not affected by the loss of gRNA units. We made a panel C in Figure 7 showing these results and mentioned them on lines 537-538. Of note, the Cas9 moiety of the gene drive construct shows no repetitive sequence and should therefore not be as unstable as the gRNA multiplex array. The observed excisions of gRNA expression units were strictly due to recombinations between repeated U6 promoter sequences (Fig. 7).

The authors employ 3 different gRNAs that are 43 and 310 nts apart. It has been shown that only 20 nt lack of homology produces an important reduction on gene drive performance (Lopez del Amo et al 2020, Nat Comms). Also, it has been shown that gRNA multiplexing approaches should be kept with a low number of gRNAs, 2 being maybe the best one depending on the design (Samuel Champer 2020, Sciences Advances). This could be discussed more.

--- Thank you for this suggestion. These results were not published when this study was initiated, so that our gene drive constructs could only be designed on empirical bases. For gRNA numbers, see the new discussion point and inclusion of a reference to the study by S. Champer et al., on line 700-702. The reduction of drive performance with longer non-homologous stretches is indeed also a very important point, that we now discuss on lines 713-717, citing your study:

Finally, tighter clustering of gRNA target sites at target homing loci, especially Saglin, should improve gene drive performance by reducing the length of DNA sequences flanking the cut site that bear no homology to the repair template on the sister chromosome and need to be resected by the repair machinery to allow homing (López Del Amo et al., 2020)__.

Reviewer #4 (Significance):

There are different novelty aspects from my point of view in this work. While most of the scientists focus on developing CRISPR-based gene drives in An. Stephensi and gambiae, this work employs An. Coluzzii. Some limitations regarding fitness cost associated with the Lp gene were also noted and discussed by the authors.

--- To be fair, earlier gene drive studies were performed on the G3 laboratory strain, traditionally named A. gambiae, although it is probably itself a hybrid strain from gambiae and coluzzii. Still, the Ngousso strain from Cameroon that was used in this study is thought to be a bona fide A. coluzzii. We have also added a reference to a recent paper (Carballar-Lejarazu et al., 2023) that also describes a population modification GD in A. coluzzii.

First, they show that An. Coluzzii mosquitoes infect less when containing the antimalarial effector cassette inserted in their genomes. Second, a gene drive is showing super-Mendelian inheritance in An. Coluzzii, which would be the second example of a gene drive in these mosquitoes so far to my knowledge.

I believe this is the first manuscript experimentally using multiplexing approaches (multiple gRNAs) in mosquitoes (all previous works I saw were performed in flies). While previous gene-drive works employ only one gRNA in mosquitoes, this works explores the use of different gRNAs targeting nearby locations to potentially improve HDR rates and gene drive spread. Although they observe gene drive activity, they also show DNA rearrangements due to the intrinsic nature of multiplexing gene drives that can generate multiple DNA double-strand breaks, impeding proper HDR and clean replacement of the wildtype alleles. This is important from a technical point of view as it shows this approach requires optimization. They included 3 gRNAs targeting the Saglin gene, and trying 2gRNAs instead could be interesting for future investigations.

--- We now discussed optimization with the help of modeling, in response to Reviewer 1, on lines 701-702.

This work will be very useful for the CRISPR-based gene drive field, which seeks to develop genome editing tools to control mosquito populations and reduce the impact of vector-borne diseases such as malaria.

This reviewer intended to understand the work and provide constructive feedback to the best of my abilities. I apologize in advance if I misunderstood anything.

--- Thank you for your appreciation, insight, and constructive evaluation of our manuscript.