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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.

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

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Referee #1

Evidence, reproducibility and clarity

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.

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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.

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

Learn more at Review Commons

---

Referee #4

Evidence, reproducibility and clarity

The 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?
• Line 133-134: Reference?
• 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.
• 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.
• 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).
• Fig.3: Please, correct to A, B, C order. Current one is A, C, B.<br /> 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.
• 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.
• Line 357/Fig.4B: Could the authors explain in the text GFP+ vs. GFP++?
• 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?
• Line 362: No reference to figure nor table.
• Line 417: The text brings the reader back to Fig.3C. Could the authors move this panel for easier flow of the paper?
• Line 472-474: How many WT alleles were recovered? It is not stated unless I missed anything, which is possible.
• 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?

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.

Also, could you add homozygous and heterozygous labels in the figure legend to help understanding the different lines.

• 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.

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.

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.

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.

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.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

The study by 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:

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.
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?
3. Why is Vg mentioned? It is only mentioned once and doesn't have any other mention through the manuscript.
4. Please make it clearer for non-specialists why Cecropin wasn't used.
5. Why were homozygous and not heterozygous transgenics transfected if there is such as fitness cost to homozygous mosquitoes?
6. Line 211 - what was the average number of infected mosquitoes used per infection for each mosquito strain?
7. Line 219 - please be clearer regarding this being infection detected in the blood.
8. Line 320 - please clarify why the zpg promoter was used.
9. Line 375 - what was the rationale for using so many gRNAs?<br /> Line 555 - please state how long post bite back parasite appears in infected mice.

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.

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

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.

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.

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.

Minor comments:

Line 44 - female sterility but also female killing approaches to crash pop. like X shredder, if authors would like to expand

Lines 48-60 - Authors should add some references from the literature surrounding ethics and ecology studies related to gene drive release

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?

Line 126 -Can the authors provide rationale for expressing Sc2A10 with Lp instead of expressing it from salivary glands?

Line 140 - Can authors give any comment on why these regions of Lp were chosen to be recoded / targeted with gRNAs?

Line 171 - "stoichiometric"

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?

Line 211 - Why were 6 mosquitoes used for these assays, and 10 mosquitoes used in later assays (Line 223)?

Line 212 - I would also suggest using letters (Suppl. Table 2A,B,C etc) to refer the specific experiments and sections in the Table.

Line 225- 228 - The authors should mention in the text that homozygotes and heterozygotes do not differ in infection assays.

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?

Line 273 - Can the authors comment on why this may have occurred more frequently than the expected integration of the GD cassette?

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.

Line 407 - don't start new paragraph (same with 409)

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?

Line 558 - "10/12 mice" not immediately clear - the authors could be more specific about how data was combined here

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?

Line 659 - add some further detail to this - how do you envision this to occur?

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.

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?

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.

Line 737 - The suggestion of releasing laboratory-selected resistance alleles in the absence of further context may be provocative and unnecessary here.

Line 850 - unnecessary comma

Line 854 - change to "after infection, moquitoes were "

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.

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.

Figure 5 - It is unclear to me why some Populations were maintained for such different lengths 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.

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?

Line 1070 - 12 out of how many sequenced mosquitoes?

Line 1078 - Can remove some detail like % of agarose, and replication of results with different polymerase as these are already in methods.

Line 1098 - "Unbless"

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.

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Referee #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).

Line 69: A quick motivation for studying Anopheles coluzii should be added here (since gambiae is discussed immediately before this).

Introduction section: It might be helpful to break up the introduction into additional paragraphs, rather than just two.

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

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.

Line 283-287: I couldn't find the data for this.

Line 291: Replace "lied" with "was".

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?

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).

Lines 362-367: What data (figure/table) does this paragraph refer to?

Lines 405-406: There may be a typo or miscalculation for the DsRed inheritance and homing rate here. Should DsRed inheritance be 90.7%?

Figure 5: The horizontal axis font size for population 8 is a little smaller than the others.

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.

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.

Figure 6C: It may be nice to show the wild-type and functional resistance sequence side-by-side.

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.

A few comments on references to some of my studies:

Champer, Liu, et al. 2018a and 2018b citations are the same paper.

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

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).

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 recuse 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

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?

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).

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Reply to the reviewers

We are grateful to the Referees for their detailed evaluation of our data and insightful remarks. We have now addressed all comments and amended the manuscript accordingly. Below we detail how we have addressed each point.

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:

In this manuscript Lafzi et al. present a novel computational framework (ISCHIA) for the analysis of spatial occurrence patterns, be it of cells or transcript species, found in spatial transcriptomics datasets. The authors also show its applications in finding differentially co-occurring ligand-receptor pairs, as well as inter-species analysis to find conserved cell signalling pathways. ISCHIA consists of a well-documented R package and utilizes empirical probabilistic estimations of non-random co-occurrence, as used in the field of ecology, which to my knowledge is novel in the field. The authors also validate their predictions using an orthogonal technology (in situ hybridization-based spatial transcriptomics), which is a nice addition to the computational work presented in the manuscript.

Major:

When determining the composition classes, the authors discard 4 out of 8 clusters of composition classes, partly due to being highly patient-specific. It's unclear how sensitive ISCHIA is for batch effects which might affect the measured cellular fractions. Given that the presence of batch effects is highly likely with ST methods, due to the sample processing procedures, it would help the reader/potential user to estimate the impact these could have on the resulting output. It would also be useful to plot a version of the UMAP with sample labels as to see if the remaining clusters are properly mixed (at least between replicates of the same condition).

We thank the reviewer for the comment. We have included in Supplemental Figure S1c a UMAP colored by sample (patients), and a barplot in d) that illustrates how CC8 and CC4 are quite specific to patients 2 and 3. These graphs illustrate how the composition classes 1, 3, 5 and 6 are represented in all patients, albeit in different abundances. We would like to point out that the choice to exclude 4 out of 8 composition classes was not dictated by batch effects, but rather by the specific morphology of the samples available to us. Indeed, we excluded composition classes that were mapping to submucosal and muscular areas because only 2 out of 4 colon resections contained these anatomical compartments, and because we wanted to focus on cell type co-occurrences in the epithelial and subepithelial layers.<br /> Additionally, in order to explain the sensitivity of ISCHIA for batch effects or sample-specific variation, we performed principal component (PC) analysis, and measured the standard deviation explained by each PC on the cell type deconvolution matrix (which is used to calculate composition clusters). Next, we tried to find an association of the covariate “batch” with the PCs that explain a high amount of variation in the data. In the deconvoluted matrix, while the first 4 PCs explain more than 80% of the variation in the data, we couldn’t find association of the covariate “batch” to any of the first 4 PCs. We now include this analysis in the Result section:

Principal component analysis of the deconvolution matrix reveals no association of a particular sample with the first 4 principal components, which cumulatively explain 80% of the variance in the data (Supplemental Figure 2c, d). K-means clustering of the deconvolution matrix revealed 8 CCs of co-localizing cell types present in all samples (Fig 1c, d).

While other methods assign a cell-type identity to spots based on the most abundant cell type detected by deconvolution algorithm, ISCHIA summarizes spot gene expression data in a presence-absence matrix. ISCHIA is therefore robust to variation in expression levels due to batch effects. This was also recently reported in the analytical tool Starfysh (He et al. 2022), which performs similar clustering of spots based on cell type composition. This is included in the Discussion:

While preserving the complexity of the cell type composition of the analyzed tissue, composition-based clustering of spots also confers robustness towards variations in expression levels due to batch effects. Indeed, other spatial analysis methods such as Starfysh66 have found that finding inter-sample commonalities using composition-based clusters is easier compared to finding common transcriptome-based clusters between samples. Still, batch analysis and, if needed, correction of the ST data is recommended prior to analysis with ISCHIA.

Additionally, it would help to illustrate that the biological findings reported in the manuscript are supported across more than 1 biological replicate.

We agree with the reviewer that the sample size of Visium and Resolve datasets is limited, however greater than 1 (3 and 4 patients, respectively). ISCHIA is meant as a tool for hypothesis generation. Its findings require independent functional validation in model systems and bigger patient cohorts.

In the LR analysis, the authors state that ISCHIA's predictions are agnostic to gene expression levels, as the authors model expression as a Boolean (gene count threshold > 0). Wouldn't low expression levels result in increased drop-out due to imperfect sensitivity? This would likely inflate false negative predictions at low expression levels.

We agree with the reviewer that dropouts due to low capture rate of Visium will lead to false negative predictions. Indeed, we chose to set the threshold for gene count > 0 to account for the sparsity of captured transcripts. In single cell RNA sequencing analysis, gene expression is analyzed in cell clusters rather than in single cells. Similarly, ISCHIA calculates LR co-occurrence in composition classes, that is clusters of spots of similar cell composition. Aggregating spots in composition classes thus mitigates the effects of low capture rate and consequent false negative predictions. We now include a sentence explaining this concept in the Results section:

The count threshold is a user defined parameter that can be increased to restrict the co-occurrence analysis to highly expressed ligands and receptors. To account for the sparsity of ST data, ISCHIA calculates LR co-occurrence within composition classes, that is clusters of spots with similar cell mixtures. Aggregating spots in composition classes thus mitigates the effects of low transcript capture rate and consequent false negative predictions.

The authors show the enrichment of particular pathways/genesets in differential gene expression comparing interacting vs noninteracting spots (through LR expression) within the same CC. It is however unclear if this enrichment stems from a random sampling of the CC (with possible confounding factors such as batch effect, QC metrics, which might also have a spatial component such as localized tissue degradation) or from the actual interaction. Adding a measure of uncertainty, such as by permuting over interaction-labels to generate a proper null distribution, would help the user to ascertain the robustness of the results. For clarity, it would also be good to add how this is exactly computed to the Methods section.

We thank the reviewer for this remark and now perform a gene expression noise estimation. As suggested by the reviewer, we employed a permutation-based approach to assess the significance of differentially expressed genes (DEGs) identified by comparing spots that are double positive for expression of a ligand-receptor pair vs spots that are not expressing any of the genes in a specific CC. To do so, we performed 1000 random sampling of spots into two groups, and calculated DEGs between these groups, consequently generating a null distribution of DEGs. We next calculated Monte Carlo p-values for the LR-associated DEGs, comparing the initially computed p-values DEG with the null distribution, and adjusting them for multiple testing using FDR. Significant adjusted p-values were indicative of genes whose differential expression was robust and unlikely to result from random spot sampling.

From the Method section:<br /> For the calculation of L-R-associated DEGs, ISCHIA computes differential gene expression between spots that are double positive or double negative for a given L-R pair. The significant DEGs are then used for pathway enrichment with any tool of choice, such as EnrichR (https://bio.tools/enrichr). We employed a permutation-based approach to assess the significance of the obtained DEGs. Specifically, we generated a null distribution of DEGs (noise estimation) by 1000-fold random sampling of spots into two groups, and calculating DEGs between these groups. Next FDR-adjusted Monte Carlo p-values were calculated for each LR-associated DEG, comparing the initially computed p-values DEG from with the null distribution, and subsequently adjusting for multiple testing. DEGs with Monte Carlo FDRs < 0.05 are likely specific to the presence of a given LR and unlikely to result from random spot sampling.

It's unclear if the p-values in the manuscript are adjusted for multiple comparisons or not. Given the number of hypotheses being tested here, this is a crucial issue.

We agree with the reviewer that this is a crucial issue. In the ecology papers we consulted and in the original co-occur R package (Griffith et al. 2016), multiple testing correction was not applied when computing co-occurrence of species. We believe however, that it is necessary to correct p values when computing co-occurrence of ligands and receptor pairs, and now implement FDR correction in the ISCHIA pipeline. We have amended all the relative figures and tables.

The authors don't really mention any of the existing state-of-the-art methods (e.g. Squidpy, Spacemake, Giotto, ...). This doesn't necessitate a full benchmark, but at least the authors should then state qualitatively what the difference is between the chosen approach and already available packages, with their respective added advantages/disadvantages.

We thank the reviewer for the remark and we have compared the analysis performed by ISCHIA with other state-of-the-art tools. The main difference between ISCHIA with respect to other methods such as Spacemake (Sztanka-Toth et al. 2022), Squidpy (Palla et al. 2022) and Giotto (Del Rossi et al. 2022), is that ISCHIA computes cell-type and LR co-occurrence within individual spots, not between neighboring spots. We include here an extensive comparison with other methods for this reviewer, and now discuss the differences between ISCHIA and other tools in the manuscript.

For neighborhood analysis, Spacemake and Squidpy use spatial coordinates of spots to identify neighbors among them (neighborhood sets are defined as a fixed number of adjacent spots in a square or hexagonal grid). Squipdy computes co-occurrence of clusters in spatial dimensions, however it uses the coordinates of spots and clusters to calculate co-occurrence of entire clusters of spots, not of cell-types within spots. This approach ignores the missing data between spots, as well as the multicellular nature of each spot. Similarly to Squidpy, Giotto assigns a score of a cell type to each spot upon deconvolution, to further identify the spatial patterns of the major cell taxonomies across all the spots on the tissue. For image-based spatial technologies with single cell resolution, Giotto creates a neighborhood graph of the single-cells to study gene expression patterns. This is similar to the approach we used to validate our predictions from Visium data in the Resolve dataset.

Tangram (Biancalani et al. 2021) is a deep learning approach to harmonize sc/snRNA-seq data with in situ, histological, and anatomical data, toward a high-resolution, integrated atlas. Tangram focuses on learning spatial gene-expression maps transcriptome-wide at single-cell resolution, and relating those to histological and anatomical information from the same specimens. However, it does not address cell-cell and ligand receptor interactions, nor co-occurrences from spatial data. Therefore, Tangram can be used to improve the deconvolution step of ISCHIA, to improve the definition of cellular composition in multicellular spatial spots.

Starfysh (He et al. 2022) is a computational toolbox for joint modeling of ST and histology data, dissection of refined cell states, and systematic integration of multiple ST datasets from complex tissues. It uses an auxiliary deep generative model that incorporates archetypal analysis and any known cell state markers to avoid the need for a single-cell-resolution reference. Starfysh also clusters spots based on cell type composition, and terms group of spots with similar composition “spatial hubs”. They use spatial hubs to integrate multiple samples, and to uncover regions with varying composition of cell states. As we propose in ISCHIA, the Starfysh authors also suggest that finding inter-sample commonalities using spatial hubs is easier compared to finding common clusters between samples. Starfysh addresses the co-localization of cell states by calculating the spatial correlation index (SCI) within a certain hub and penalizing the calculated correlation with a weight matrix τ in a way that : τ_(between two spots i,j)=1 if the coordinate distance of spot i and spot j was less than √3 else τ_(between two spots i,j)=0 . While this approach provides a measure of cell state co-localization across a spatial hub, it looks at the problem from an inter-spot perspective, similar to Squipdy and Giotto. Again, this is different from ISCHIA that calculates co-occurrence within spots.

In conclusion, none of the current approaches focuses on addressing the co-occurrence of cell types and molecules within individual Visium spots. As the analysis is fundamentally different, we did not perform a full quantitative benchmark. We agree, however, that these differences need to be addressed in the manuscripts. To illustrate the different results obtained, we ran ISCHIA on a Visium slide of a coronal section of the mouse brain, which was also analyzed using Squidpy (https://squidpy.readthedocs.io/en/stable/notebooks/tutorials/tutorial_visium_hne.html) and Giotto (https://rubd.github.io/Giotto_site/articles/mouse_visium_brain_201226.html#part-9-spatial-network). We clustered the spots based on cell composition and then ran celltype co-occurrence analysis within each composition class (Supplementary Figure 1).

From the Results section:

State-of-the-art analysis tools for Visium data often treat every spot as a single datapoint, and compute co-localization, network or cell-cell interactions analysis between neighboring spots (inter-spot analysis). We hypothesized that CNs would be best reconstructed within individual spots (intra-spot analysis), as their mixed transcriptome contains information about locally occurring cell types, expressed ligands and receptors, and activated signaling pathways. As inferring CNs in each individual spot separately would be noisy, sparse, computationally intensive, and would lack statistical power, ISCHIA first divides the tissue into clusters of spots with similar cellular composition - termed composition classes (CCs) (Fig 1a). CCs are thus groups of spots containing similar mixtures of cells, or cellular communities, e.g, all spots capturing colonic crypts. To achieve the division of the tissue into CCs, spot transcriptomes are deconvoluted, yielding a cell type composition matrix (spot × contribution of each cell type), which is then subjected to dimensionality reduction and k-means clustering. ISCHIA allows for both reference-based deconvolution, with tools such as SPOTlight7 or RCTD8, and reference-free deconvolution9. Upon deconvolution, ISCHIA summarizes spot gene expression data in a cell type presence-absence matrix, where each listed cell type is associated with a probability to be present in a given spot (p > 0.1). Each spot is thus represented as a mixture of cell types, and similar mixtures are then clustered together in CCs. We applied ISCHIA on a publicly available Visium slide of a coronal section of the mouse brain (10x Genomics), using as a reference for deconvolution a scRNA-seq dataset of ~14,000 adult mouse cortical cells from the Allen Institute10. Composition-based clustering of the spots yielded 5 CCs, which broadly reflect the annotated anatomical regions (Supplemental Figure 1a). ISCHIA then computes cell type co-occurrence for every CC separately, identifying spatial association of cells in close proximity (Supplemental Figure 1b). Intra-spot analysis reconstructs cellular networks with cell types as nodes, and is distinct from inter-spot networks analysis employed by other tools on this sample, in which spots are used as nodes11,12.

We also discuss differences between ISCHIA and other tools in the Discussion:

ISCHIA differs from other analysis tools for Visium data in that it predicts CNs within spots and not across spots. Indeed, spot data from sequencing-based ST methods such as Visium, simultaneously captures information about 1) cell types, 2) expressed LR genes, and 3) associated transcriptional responses at multiple spatially restricted locations. As proximity is a prerequisite for juxtacrine and paracrine cell-cell communication, which in turn constitutes the basis for the coordinated function of CNs, we hypothesized that CNs would best be reconstructed within individual spots, rather than across neighboring spots. To increase robustness, spots are grouped in clusters of similar cellular composition, termed composition classes. Composition-based clustering of the tissue represents a major advantage of this method, and distinguished it from other methods, such as Squidpy11 or Giotto12, that assign an identity to each spot based on marker gene expression or on the most abundant cell type. While preserving the complexity of the cell type composition of the analyzed tissue, composition-based clustering of spots also confers robustness towards variations in expression levels due to batch effects. Indeed, other spatial analysis methods such as Starfysh66 have found that finding inter-sample commonalities using composition-based clusters is easier compared to finding common transcriptome-based clusters between samples. Still, batch analysis and, if needed, correction of the ST data is recommended prior to analysis with ISCHIA. Composition-based clustering of spots allows to restrict downstream analysis to similar mixtures of cells, filtering out transcriptome heterogeneity arising from distinct cellular compositions, which might act as a confounder variable when performing differential gene expression or cell-cell interaction predictions.<br /> To reconstruct CNs, ISCHIA performs co-occurrence analysis of cell types within CCs. Other tools build a neighborhood graph using spatial coordinates of spots and a fixed number of adjacent spots11,12,66, and therefore ignoring the missing data between spots as well as the multicellular nature of each spot, ISCHIA leverages the inherent proximity of mixed transcriptomes within individual spots to infer cellular neighborhoods. Hence, the cell types within the spots, rather than the spots themselves, are the nodes of the CN. This approach allows for reconstruction of much smaller CNs, operating in close spatial proximity, a prerequisite for juxtacrine and paracrine signaling between cells. ISCHIA further predicts LR interaction as edges connecting cell types within spots, not across multiple spots. Finally, by integrating co-occurrence of cell types, co-occurrence of LR pairs, and associated gene signatures, ISCHIA infers CN function.

Minor:

When a priori testing for LR interactions without restricting these interactions to predicted interactions, it would be informative to have an estimate of how many of the positively co-occurring interactions coincide with their predictions. As the authors state, it's hard to judge novel interactions without orthogonal validation, but a large overlap between predictions and the results presented here might instill confidence in the novel findings.

We thank the reviewer for the comment and now label in green, in Fig 4a, the positively co-occurring interactions that are also predicted by Omnipath, NicheNet or CellTalkDB.

Fig 4D: It's hard to judge very small p-values on this plot, might be better to plot -log10(pval).

We have now changed this plot to display the differential co-occurrence score, calculated as FDRinflamed - FDRnon-inflamed.

The axes on some of the plots should be better defined in the figure legends (e.g. Fig 4D, 5C)

We have included better axis descriptions.

I'm not an expert in inflammation or IBD biology, so I will defer that to other reviewers more suited to comment on this.

Reviewer #1 (Significance):

The proposed method provides a reasonable framework for studying co-occurences of cell types and transcripts (particularly ligand-receptor pairs), which are currently questions of great interest to the community applying novel spatial transcriptomics technologies in many different domains of life sciences. The manuscript is very well written, and provides a clear and consistent logical flow. The manuscript can be easily read and understood both by specialized users as well as biologist/clinical end-users wanting to apply the proposed technique. The addition of experimental data using an orthogonal technology to validate computational predictions illustrates nicely the power of the proposed approach.

Although the presented approach is methodologically rather simple (which is not necessarily a disadvantage), it is novel in the field as far as I know and a good implementation is likely to see great adoption by the field, especially if it's well documented, maintained and integrated into existing data processing workflows. The authors should however compare their approach fairly with the rest of the available packages in order to convince the reader.

Although the presented data seems convincing to me, the authors should take greater care of defining good practice statistical reporting of their findings. Even though these tools are often hypothesis-generating and predictions should always be experimentally validated, some end-users might interpret p-values literally. As such, proper multiple-testing correction and analysis of critical confounding factors should be carried out as to set an example.

I'm a computational biologist with expertise in method development (machine learning and statistical modelling) for spatial multi-omics assays. I'm not an expert in inflammation or IBD biology, so I will defer that to other reviewers more suited to comment on this.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors developed ISCHIA to study co-occurence of cell types and transcript species. This work was further extended to study cell-cell interactions based on ligand-receptor co-expression. The observation by ISCHIA was further validated using hybridization based spatial transcriptomics approaches. ISCHIA was applied to study healthy and inflamed human colons.

Referees cross-commenting

As the reviewer #1 pointed, there is no description about existing methods. The reviewer #1 only asked stating qualitative differences.

If the manuscript is mainly for IBD and ISCHIA is the bioinformatics steps they followed, I would agree with the reviewer #1. However, the authors wanted to say that it is a new software. I still think that full benchmarking is needed in this circumstance.

We thank the reviewer for the remark and we have compared the analysis performed by ISCHIA with other state-of-the-art tools. The main difference between ISCHIA with respect to other methods such as Spacemake (Sztanka-Toth et al. 2022), Squidpy (Palla et al. 2022) and Giotto (Del Rossi et al. 2022), is that ISCHIA computes cell-type and LR co-occurrence within individual spots, not between neighboring spots. We include here an extensive comparison with other methods for this reviewer, and now discuss the differences between ISCHIA and other tools in the manuscript.

For neighborhood analysis, Spacemake and Squidpy use spatial coordinates of spots to identify neighbors among them (neighborhood sets are defined as a fixed number of adjacent spots in a square or hexagonal grid). Squipdy computes co-occurrence of clusters in spatial dimensions, however it uses the coordinates of spots and clusters to calculate co-occurrence of entire clusters of spots, not of cell-types within spots. This approach ignores the missing data between spots, as well as the multicellular nature of each spot. Similarly to Squidpy, Giotto assigns a score of a cell type to each spot upon deconvolution, to further identify the spatial patterns of the major cell taxonomies across all the spots on the tissue. For image-based spatial technologies with single cell resolution, Giotto creates a neighborhood graph of the single-cells to study gene expression patterns. This is similar to the approach we used to validate our predictions from Visium data in the Resolve dataset.

Tangram (Biancalani et al. 2021) is a deep learning approach to harmonize sc/snRNA-seq data with in situ, histological, and anatomical data, toward a high-resolution, integrated atlas. Tangram focuses on learning spatial gene-expression maps transcriptome-wide at single-cell resolution, and relating those to histological and anatomical information from the same specimens. However, it does not address cell-cell and ligand receptor interactions, nor co-occurrences from spatial data. Therefore, Tangram can be used to improve the deconvolution step of ISCHIA, to improve the definition of cellular composition in multicellular spatial spots.

Starfysh (He et al. 2022) is a computational toolbox for joint modeling of ST and histology data, dissection of refined cell states, and systematic integration of multiple ST datasets from complex tissues. It uses an auxiliary deep generative model that incorporates archetypal analysis and any known cell state markers to avoid the need for a single-cell-resolution reference. Starfysh also clusters spots based on cell type composition, and terms group of spots with similar composition “spatial hubs”. They use spatial hubs to integrate multiple samples, and to uncover regions with varying composition of cell states. As we propose in ISCHIA, the Starfysh authors also suggest that finding inter-sample commonalities using spatial hubs is easier compared to finding common clusters between samples. Starfysh addresses the co-localization of cell states by calculating the spatial correlation index (SCI) within a certain hub and penalizing the calculated correlation with a weight matrix τ in a way that : τ_(between two spots i,j)=1 if the coordinate distance of spot i and spot j was less than √3 else τ_(between two spots i,j)=0 . While this approach provides a measure of cell state co-localization across a spatial hub, it looks at the problem from an inter-spot perspective, similar to Squipdy and Giotto. Again, this is different from ISCHIA that calculates co-occurrence within spots.

In conclusion, none of the current approaches focuses on addressing the co-occurrence of cell types and molecules within individual Visium spots. As the analysis is fundamentally different, we did not perform a full quantitative benchmark. We agree, however, that these differences need to be addressed in the manuscripts. To illustrate the different results obtained, we ran ISCHIA on a Visium slide of a coronal section of the mouse brain, which was also analyzed using Squidpy (https://squidpy.readthedocs.io/en/stable/notebooks/tutorials/tutorial_visium_hne.html) and Giotto (https://rubd.github.io/Giotto_site/articles/mouse_visium_brain_201226.html#part-9-spatial-network). We clustered the spots based on cell composition and then ran celltype co-occurrence analysis within each composition class (Supplementary Figure 1).

From the Results section:

State-of-the-art analysis tools for Visium data often treat every spot as a single datapoint, and compute co-localization, network or cell-cell interactions analysis between neighboring spots (inter-spot analysis). We hypothesized that CNs would be best reconstructed within individual spots (intra-spot analysis), as their mixed transcriptome contains information about locally occurring cell types, expressed ligands and receptors, and activated signaling pathways. As inferring CNs in each individual spot separately would be noisy, sparse, computationally intensive, and would lack statistical power, ISCHIA first divides the tissue into clusters of spots with similar cellular composition - termed composition classes (CCs) (Fig 1a). CCs are thus groups of spots containing similar mixtures of cells, or cellular communities, e.g, all spots capturing colonic crypts. To achieve the division of the tissue into CCs, spot transcriptomes are deconvoluted, yielding a cell type composition matrix (spot × contribution of each cell type), which is then subjected to dimensionality reduction and k-means clustering. ISCHIA allows for both reference-based deconvolution, with tools such as SPOTlight7 or RCTD8, and reference-free deconvolution9. Upon deconvolution, ISCHIA summarizes spot gene expression data in a cell type presence-absence matrix, where each listed cell type is associated with a probability to be present in a given spot (p > 0.1). Each spot is thus represented as a mixture of cell types, and similar mixtures are then clustered together in CCs. We applied ISCHIA on a publicly available Visium slide of a coronal section of the mouse brain (10x Genomics), using as a reference for deconvolution a scRNA-seq dataset of ~14,000 adult mouse cortical cells from the Allen Institute10. Composition-based clustering of the spots yielded 5 CCs, which broadly reflect the annotated anatomical regions (Supplemental Fig 1). ISCHIA then computes cell type co-occurrence for every CC separately, identifying spatial association of cells in close proximity (Supplemental Fig xx). Intra-spot analysis reconstructs cellular networks with cell types as nodes, and is distinct from inter-spot networks analysis employed by other tools on this sample, in which spots are used as nodes11,12.

We also discuss differences between ISCHIA and other tools in the Discussion:

ISCHIA differs from other analysis tools for Visium data in that it predicts CNs within spots and not across spots. Indeed, spot data from sequencing-based ST methods such as Visium, simultaneously captures information about 1) cell types, 2) expressed LR genes, and 3) associated transcriptional responses at multiple spatially restricted locations. As proximity is a prerequisite for juxtacrine and paracrine cell-cell communication, which in turn constitutes the basis for the coordinated function of CNs, we hypothesized that CNs would best be reconstructed within individual spots, rather than across neighboring spots. To increase robustness, spots are grouped in clusters of similar cellular composition, termed composition classes. Composition-based clustering of the tissue represents a major advantage of this method, and distinguished it from other methods, such as Squidpy11 or Giotto12, that assign an identity to each spot based on marker gene expression or on the most abundant cell type. While preserving the complexity of the cell type composition of the analyzed tissue, composition-based clustering of spots also confers robustness towards variations in expression levels due to batch effects. Indeed, other spatial analysis methods such as Starfysh66 have found that finding inter-sample commonalities using composition-based clusters is easier compared to finding common transcriptome-based clusters between samples. Still, batch analysis and, if needed, correction of the ST data is recommended prior to analysis with ISCHIA. Composition-based clustering of spots allows to restrict downstream analysis to similar mixtures of cells, filtering out transcriptome heterogeneity arising from distinct cellular compositions, which might act as a confounder variable when performing differential gene expression or cell-cell interaction predictions.

To reconstruct CNs, ISCHIA performs co-occurrence analysis of cell types within CCs. Other tools build a neighborhood graph using spatial coordinates of spots and a fixed number of adjacent spots11,12,66, and therefore ignoring the missing data between spots as well as the multicellular nature of each spot, ISCHIA leverages the inherent proximity of mixed transcriptomes within individual spots to infer cellular neighborhoods. Hence, the cell types within the spots, rather than the spots themselves, are the nodes of the CN. This approach allows for reconstruction of much smaller CNs, operating in close spatial proximity, a prerequisite for juxtacrine and paracrine signaling between cells. ISCHIA further predicts LR interaction as edges connecting cell types within spots, not across multiple spots. Finally, by integrating co-occurrence of cell types, co-occurrence of LR pairs, and associated gene signatures, ISCHIA infers CN function.

Reviewer #2 (Significance):

As the authors wanted to introduce ISCHIA as a new tool, discussion and comparison with the previous approaches are essential. The manuscript lacks discussion and the comparison with others. Co-localization has been discussed already in many articles including [PMID:325799]. It does not seem to require additional packages to study co-localization for cell type. There are many cell-cell interaction studies using ligand-receptor co-localization [ref; stLern, SpaGene, and many]. It is not well documented about the relationships with the previous works. Given the advances in algorithms for spatial transcriptomics, it is very uncertain that ISCHIA can provide additional knowledge or contribute to algorithmic development.

We agree with the reviews that there is an increasing body of work addressing co-localization of cell type and cell-cell interactions in spatial transcriptomic data. However, we assert that the introduction of our method holds substantial relevance and adds value to the field, notwithstanding its ostensible simplicity. Our method has been well-received within the scientific community, indicating its applicability and potential significance in deciphering complex cellular ecosystems. We believe our approach offers a distinct conceptual advantage by enabling the analysis of cellular communities within individual Visium spots, rather than solely between them, allowing for a more refined exploration of cellular interactions and co-localizations within specific spatial domains.

Previously, Visium data were generated by Elmentaite et al. (Nture 2021) against healty and IBD samples. what are the new findings of the manuscript?

Visium data generated by Elmentaite et al is from pediatric Crohn's disease, not adult Ulcerative colitis. Spatial analysis of IBD samples has been performed by Nanostring and by CODEX (Garrido-Trigo et al. 2022; Mayer et al. 2023). Publication of our datasets (both Visium and Resolve) will increase the body of patient data available to the community, and should be considered positively.

Here, we use our dataset to demonstrate the ability of ISCHIA to reconstruct cellular networks within Visium spots, and identify a M-cell-fibroblast network in inflamed regions of UC patients. We further identify differentially co-occurring LRs in the inflammatory CC5 centered around EDN1, SEMA3C, and CXCL5. We further reveal inflammation-induced, protective responses from the colonic crypt involving the complement cascade and the immuno-modulator SECTM1. Finally, we apply co-occurrence analysis to an independent mouse Visium dataset and uncover differentially co-occurring LR pairs shared between the inflamed human and murine colon. ISCHIA is an hypothesis generating tool, and its findings should be extensively characterized and validated in larger cohorts.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

The authors provide a framework to analyze spatial transcriptomics (ST) data in terms of spatial co-occurrence of cell types, and ligand-receptor pairs. The method was applied to an ulcerative colitis sequencing-based data set (10x Visium) and validated using a matched hybridization-based data set (Molecular Cartography).

Major Comments

The Visium data set consisted of a single slide with four samples. The authors should clarify if the current implementation of their method is limited to a single Visium slide.

We thank the reviewer for the remark and now state in the text that ISCHIA can be applied to any Visium, Resolve or other spatial transcriptomic dataset. Visium samples originating from different slides and datasets can be fed into the ISCHIA pipeline, as it is quite robust to batch effects. Indeed, while other methods assign a cell-type identity to spots based on the most abundant cell type detected by deconvolution algorithm, ISCHIA summarizes spot gene expression data in a presence-absence matrix. ISCHIA is therefore robust to variation in expression levels due to batch effects. This was also recently reported in the analytical tool Starfysh (He et al. 2022), which performs similar clustering of spots based on cell type composition. This is included in the Discussion:

While preserving the complexity of the cell type composition of the analyzed tissue, composition-based clustering of spots also confers robustness towards variations in expression levels due to batch effects. Indeed, other spatial analysis methods such as Starfysh66 have found that finding inter-sample commonalities using composition-based clusters is easier compared to finding common transcriptome-based clusters between samples. Still, batch analysis and, if needed, correction of the ST data is recommended prior to analysis with ISCHIA.

In Supplementary Table 1, I think it would be useful to include the minimum number of counts for the Ligand-Receptor genes. Given that the current threshold is 1, I think it warrants a discussion if the minimum number of counts has an effect on whether the ligand-receptor pair is significantly co-occurring (i.e. if ligand-receptor pairs with more counts are more likely to be significant).

We agree with the reviewer that increasing the threshold to >1 will reduce the number of significantly co-occurring LRs, but also increase false negative predictions. We chose to set the threshold for gene count > 0 to account for the sparsity of captured transcripts. Indeed, dropouts due to low capture rate of Visium will lead to false negative predictions. In single cell RNA sequencing analysis, gene expression is analyzed in cell clusters rather than in single cells. Similarly, ISCHIA calculates LR co-occurrence in composition classes, that is clusters of spots of similar cell composition. Aggregating spots in composition classes thus mitigates the effects of low capture rate and consequent false negative predictions. We now include a sentence explaining this concept in the Results section:

The count threshold is a user defined parameter that can be increased to restrict the co-occurrence analysis to highly expressed ligands and receptors. To account for the sparsity of ST data, ISCHIA calculates LR co-occurrence within composition classes, that is clusters of spots with similar cell mixtures. Aggregating spots in composition classes thus mitigates the effects of low transcript capture rate and consequent false negative predictions.

Given the effect of outliers in the Pearson correlation and the nature of the expression values for VIsium data, I think that the Spearman rank correlation is better suited to estimate the correlation between the expression values of the ligand-receptor pairs than the Pearson correlation (the default in R).

We thank the reviewer for the comment and now rank positively co-occurring LR based on Spearman correlation. See Fig 3a and Supplementary Table 1.

In the section titled "Differential co-occurrence identifies niche-specific response programs", it is unclear whether the spatial co-occurrence analysis was done within each CC.

We now specify that we computed co-occurrence analysis of ligands and receptor genes in all spots of our dataset across all CCs. We now include FDR corrected p-values in this analysis. Only after computing this broad co-occurrence analysis, we focus on differential co-occurrence comparing conditions or composition classes.

Minor Comments

I found a few typos in the manuscript

In the Abstract, "tecniquee" instead of "techniques"

On page 10, under "Integration and annotation of scRNASeq data.", "W" instead of "We"

On page 11, there is an equation rendering error: P(lt) = $p_lt

We thank the reviewer for these comments and have now corrected the typos.

Reviewer #3 (Significance):

The method proposed takes advantage of work done in ecology to leverage the spatial context of ST data. Furthermore, the methods proposed goes beyond describing spatial patterns present in the data, but allows for the comparison between two conditions of interest. The method proposed will be of interest to the growing number of researchers generating ST data.

My expertise is in statistical methods for single cell and spatial transcriptomics data. Furthermore, I have extensive experience analyzing single cell and spatial transcriptomics data in the context of liver diseases.

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Referee #3

Evidence, reproducibility and clarity

Summary

The authors provide a framework to analyze spatial transcriptomics (ST) data in terms of spatial co-occurrence of cell types, and ligand-receptor pairs. The method was applied to an ulcerative colitis sequencing-based data set (10x Visium) and validated using a matched hybridization-based data set (Molecular Cartography).

Major Comments

The Visium data set consisted of a single slide with four samples. The authors should clarify if the current implementation of their method is limited to a single Visium slide.

In Supplementary Table 1, I think it would be useful to include the minimum number of counts for the Ligand-Receptor genes. Given that the current threshold is 1, I think it warrants a discussion if the minimum number of counts has an effect on whether the ligand-receptor pair is significantly co-occurring (i.e. if ligand-receptor pairs with more counts are more likely to be significant).

Given the effect of outliers in the Pearson correlation and the nature of the expression values for VIsium data, I think that the Spearman rank correlation is better suited to estimate the correlation between the expression values of the ligand-receptor pairs than the Pearson correlation (the default in R).

In the section titled "Differential co-occurrence identifies niche-specific response programs", it is unclear whether the spatial co-occurrence analysis was done within each CC.

Minor Comments

I found a few typos in the manuscript

In the Abstract, "tecniquee" instead of "techniques"

On page 10, under "Integration and annotation of scRNASeq data.", "W" instead of "We"

On page 11, there is an equation rendering error: P(lt) = $p_lt

Significance

The method proposed takes advantage of work done in ecology to leverage the spatial context of ST data. Furthermore, the methods proposed goes beyond describing spatial patterns present in the data, but allows for the comparison between two conditions of interest. The method proposed will be of interest to the growing number of researchers generating ST data.

My expertise is in statistical methods for single cell and spatial transcriptomics data. Furthermore, I have extensive experience analyzing single cell and spatial transcriptomics data in the context of liver diseases.

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Referee #2

Evidence, reproducibility and clarity

The authors developed ISCHIA to study co-occurence of cell types and transcript species. This work was further extended to study cell-cell interactions based on ligand-receptor co-expression. The observation by ISCHIA was further validated using hybridization based spatial transcriptomics approaches. ISCHIA was applied to study healthy and inflamed human colons.

Referees cross-commenting<br /> As the reviewer #1 pointed, there is no description about existing methods. The reviewer #1 only asked stating qualitative differences.

If the manuscript is mainly for IBD and ISCHIA is the bioinformatics steps they followed, I would agree with the reviewer #1. However, the authors wanted to say that it is a new software. I still think that full benchmarking is needed in this circumstance.

Significance

As the authors wanted to introduce ISCHIA as a new tool, discussion and comparison with the previous approaches are essential. The manuscript lacks discussion and the comparison with others. Co-localization has been discussed already in many articles including [PMID:325799]. It does not seem to require additional packages to study co-localization for cell type. There are many cell-cell interaction studies using ligand-receptor co-localization [ref; stLern, SpaGene, and many]. It is not well documented about the relationships with the previous works. Given the advances in algorithms for spatial transcriptomics, it is very uncertain that ISCHIA can provide additional knowledge or contribute to algorithmic development.

Previously, Visium data were generated by Elmentaite et al. (Nture 2021) against healty and IBD samples. what are the new findings of the manuscript?

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript Lafzi et al. present a novel computational framework (ISCHIA) for the analysis of spatial occurrence patterns, be it of cells or transcript species, found in spatial transcriptomics datasets. The authors also show its applications in finding differentially co-occurring ligand-receptor pairs, as well as inter-species analysis to find conserved cell signalling pathways. ISCHIA consists of a well-documented R package and utilizes empirical probabilistic estimations of non-random co-occurrence, as used in the field of ecology, which to my knowledge is novel in the field. The authors also validate their predictions using an orthogonal technology (in situ hybridization-based spatial transcriptomics), which is a nice addition to the computational work presented in the manuscript.

Major:

• When determining the composition classes, the authors discard 4 out of 8 clusters of composition classes, partly due to being highly patient-specific. It's unclear how sensitive ISCHIA is for batch effects which might affect the measured cellular fractions. Given that the presence of batch effects is highly likely with ST methods, due to the sample processing procedures, it would help the reader/potential user to estimate the impact these could have on the resulting output. It would also be useful to plot a version of the UMAP with sample labels as to see if the remaining clusters are properly mixed (at least between replicates of the same condition). Additionally, it would help to illustrate that the biological findings reported in the manuscript are supported across more than 1 biological replicate.
• In the LR analysis, the authors state that ISCHIA's predictions are agnostic to gene expression levels, as the authors model expression as a Boolean (gene count threshold > 0). Wouldn't low expression levels result in increased drop-out due to imperfect sensitivity? This would likely inflate false negative predictions at low expression levels.
• The authors show the enrichment of particular pathways/genesets in differential gene expression comparing interacting vs noninteracting spots (through LR expression) within the same CC. It is however unclear if this enrichment stems from a random sampling of the CC (with possible confounding factors such as batch effect, QC metrics, which might also have a spatial component such as localized tissue degradation) or from the actual interaction. Adding a measure of uncertainty, such as by permuting over interaction-labels to generate a proper null distribution, would help the user to ascertain the robustness of the results. For clarity, it would also be good to add how this is exactly computed to the Methods section.
• It's unclear if the p-values in the manuscript are adjusted for multiple comparisons or not. Given the number of hypotheses being tested here, this is a crucial issue.
• The authors don't really mention any of the existing state-of-the-art methods (e.g. Squidpy, Spacemake, Giotto, ...). This doesn't necessitate a full benchmark, but at least the authors should then state qualitatively what the difference is between the chosen approach and already available packages, with their respective added advantages/disadvantages.

Minor:

• When a priori testing for LR interactions without restricting these interactions to predicted interactions, it would be informative to have an estimate of how many of the positively co-occurring interactions coincide with their predictions. As the authors state, it's hard to judge novel interactions without orthogonal validation, but a large overlap between predictions and the results presented here might instill confidence in the novel findings.
• Fig 4D: It's hard to judge very small p-values on this plot, might be better to plot -log10(pval).
• The axes on some of the plots should be better defined in the figure legends (e.g. Fig 4D, 5C)

I'm not an expert in inflammation or IBD biology, so I will defer that to other reviewers more suited to comment on this.

Significance

The proposed method provides a reasonable framework for studying co-occurences of cell types and transcripts (particularly ligand-receptor pairs), which are currently questions of great interest to the community applying novel spatial transcriptomics technologies in many different domains of life sciences. The manuscript is very well written, and provides a clear and consistent logical flow. The manuscript can be easily read and understood both by specialized users as well as biologist/clinical end-users wanting to apply the proposed technique. The addition of experimental data using an orthogonal technology to validate computational predictions illustrates nicely the power of the proposed approach.

Although the presented approach is methodologically rather simple (which is not necessarily a disadvantage), it is novel in the field as far as I know and a good implementation is likely to see great adoption by the field, especially if it's well documented, maintained and integrated into existing data processing workflows. The authors should however compare their approach fairly with the rest of the available packages in order to convince the reader.

Although the presented data seems convincing to me, the authors should take greater care of defining good practice statistical reporting of their findings. Even though these tools are often hypothesis-generating and predictions should always be experimentally validated, some end-users might interpret p-values literally. As such, proper multiple-testing correction and analysis of critical confounding factors should be carried out as to set an example.

I'm a computational biologist with expertise in method development (machine learning and statistical modelling) for spatial multi-omics assays. I'm not an expert in inflammation or IBD biology, so I will defer that to other reviewers more suited to comment on this.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Major comments:

• 1/ The model system used in this work is referred to as "organoids", with the premise that organoids, as representatives of the original tissue, can be used to study tissue development. However, the organoids presented in the study are spherical structures, and the paper does not provide any information about how and to what extent these organoids represent the original tissue. Furthermore, it would be difficult to expect these organoids to accurately represent human breast tissue, as they are derived, to the best of the reviewer's understanding (it is not explicitly noted, but rather the text refers the reader to several previous works), from primary human breast epithelial cells that had been cultured for 6 passages in 2D culture. The CD24/CD44 flow cytometry profile of these 2D cultures, as well as the organoids derived from them, shows a unimodal distribution of CD24 and CD44 expression, and does not show distinct cell populations, as typical in primary breast epithelial cells that have not been cultured in 2D

• Response 1:

  We understand the concern raised by the reviewer. Before initiating the study we have carefully characterized our model (See Revision Section part 2.2, for the revisions that have already been carried out).

  In parallel, to further address this point, we plan to perform an extensive characterization of our mammary primary cells as well as our 3D-matrigel embedded culture. This will be achieved through flow cytometry using other multiple lineage-specific surface markers for luminal progenitor cells (such as CD49f−/low/EpCAM+), and basal/myoepithelial cells (such as CD49f+/EpCAM−/low).

  Thus, overall our experiments will confirm that our growth conditions (which we intend to describe in greater details in the methods section) for multipotent mammary stem cells can generate multi-lineage organoids.

2/ There appears to be confusion between concepts: primarily confusing a basal phenotype with a stem cell phenotype, and progenitor activity with stem cell activity. Because the 3D organoid model does not display a replication of luminal differentiation, it cannot be used as a proxy for stem cell function. The results from the miRNA screen and the subsequent experiments support two conclusions: 1. miR-160b-3p leads to an enhanced mesenchymal phenotype, manifested by reduced CD24 and enhanced CD44 expression. 2. miR-160b-3p leads to increased organoid formation. The latter may be interpreted, at best, as higher basal progenitor activity, but is not a measure of stem cell activity, as that would require the cells to give rise to more than one lineage, which is not shown here.

• Response 2:

We agree with the reviewer on the confusions between several concepts that we did not discriminate enough. The planned characterization of our cultures will allow us to better define the nature of our primary cell population and avoid any confusion (See Response 1). Indeed, an organoid is a self-organized 3D tissue that typically originates from stem cells (pluripotent, fetal or adult). Therefore, we will replace the term “stem cell activity” through the article by “stem/progenitor activity”.

3/ Overall, the information from figures 1-4 indicate that miR-160b-3p is driving and is associated with mesenchymal differentiation, possibly with EMT.

Response 3:

We agree with the reviewer that our data suggest that miR-160b-3p is driving and is associated with mesenchymal differentiation. As suggested by reviewer, to further evaluate the possible involvement of EMT, we will analysed using RT-qPCR, as we described in Fessart et al, (May 30, 2016 https://doi.org/10.7554/eLife.13887), the expression of the main EMT genes in miR-106a-3p cells. These results will be also confirmed at the protein level.

4/ In contrast to the work in the breast 3D culture model, the experiments with hESCs are interesting and do support a role of this miR in stemness.

Response 4:

We would like to extend our gratitude to the reviewer for their valuable comments on this aspect of our work.

There are several relatively minor comments that cumulatively somewhat undermine the strength of the work:

5/ Abstract: the sentence "organoids can be directly generated from human epithelial cells by only one miRNA, miR-106a-sp" needs better clarification.

• We agree with the reviewer, this sentence will be modified accordingly.

6/ Page 5 line 103: HMECs is a term that generally refers to human mammary epithelial cells, not a specific derivation or subpopulation thereof.

• We will replace HMEC by human primary mammary epithelial cells.

7/ The graph in Fig. 1A is unnecessary, it shows only one bar.

• We will remove this panel in the revised version of the manuscript.

8/ It is unclear if all the HMECs were derived from the same donor, or several donors. There is no information about the donor and how the tissue and cells were derived. In general, it is not entirely clear how the cells were collected, processed, stored, and cultured from the time they were obtained from the donor until their use in the current study.

• We will include in the material section the details information on our primary cells and our culture conditions

9/ The key for Fig. 2D is unclear. The axes read "density" but the text refers to "intensity". Fluorescence intensity in flow cytometry is usually measured on a log scale. Differences on a linear scale are not usually considered meaningful. The authors should clarify why they chose a linear scale for this screen.

• The screening was conducted using a high throughput microscope that measures the relative signal intensity, thus the scale is based on linear signal intensity.

10/ In the miRNA screen, how long were the cells cultured after transfection, and was it enough time for them to shift phenotype?

• The timeline of the screening process is detailed in the Material section. The cells were cultured for 6 days following transfection for the CD44/CD24 staining and 8 days following transfection for the 3D culture, which provides sufficient time for shifting the phenotype.

11/ Page 6 line 154: The authors likely mean z-score, not z factor (two different things).

• We thank the reviewer for pointing this, this will be corrected.

12/ Page 7 line 161: "mir-106a-3p directly promotes the "transdifferentiation" of CD44low/CD24high cells phenotype into CD44high/CD24low cell phenotype" - is an unsupported statement, given that there could be several alternative explanations for the observed change in population ratios, including effects on survival or growth of cells of a certain population.

• Transdifferentiation (also known as lineage reprogramming, or -conversion), is a process in which one mature, specialized cell type changes into another without entering a pluripotent state. This process involves the ectopic expression of transcription factors and/or other stimuli. We agree with the reviewer's observation that we did not fully demonstrate the transdifferentiation process in terms of lineage. Therefore, we will use flow cytometry to analyse multiple lineage-specific surface markers for luminal progenitor cells (such as CD49f−/low/EpCAM+), and basal/myoepithelial cells (such as CD49f+/EpCAM−/low) following miR-106a-3p expression.
• Additionally, we acknowledge that there may be other alternative explanations; so we have already assessed the impact of mir-106a-3p on the population doubling time in culture to determine whether it affects the cells' survival or growth of the cells (See Section Part 2.2 for a description of experiments already carried out).

13/ There is need for quantification of the phenotypes described in Fig. 3C

• We thank the reviewer for this valuable suggestion and we will indeed characterize the 3D structure using flow cytometry.

14/ Figures 3 D-F it is not clear if the graphs display percentage or mean number (there is discrepancy between figure text and figure legend text), and when percentage, not clear for figure 3F out of what.

• We appreciate the reviewer's suggestion, and we have replaced the term 'axis' with 'Organoid Formation Capacity (OFC),' which is the commonly used nomenclature for this measure. OFC corresponds to the percentage of organoids per cell seeded, as explained in the legend.

15/ Fig. 5B, what is the statistical significance of the enrichment?

• In Figure 5B, the statistical significance of the enrichment is an FDR value of 0.024 and it is based on the multiple rotation gene-set testing (mroast) from the Limma R package (https://doi.org/10.1093/bioinformatics/btq401). This information will be included in the figure legend.

Reviewer #2 (Evidence, reproducibility and clarity):

In this work, Robert et al. utilize mammary organoid culture as an in vitro model of stem cell renewal and maintenance. Authors show that a putative mammary stem cell population, characterized as CD44high CD24low, is enriched in organoid culture relative to 2D monolayer culture. They conduct a microRNA (miR) screen and identify miR-106a-3p as a miRNA that enriches for stem cell (CD44high CD24low) and organoid formation capacity, confirming these findings using miR-106a-3p overexpressing cells. Authors also show that CBX7 overexpression achieves a similar enrichment in CD44high CD24low and organoid formation capacity in an miR-106a-3p dependent manner, though the rationale behind the connection between CBX7 and miR-106a-3p is not well defined. Finally, the manuscript conducts a transcriptomic analysis on miR-106a-3p-OE cells and aims to functionally validate its role in embryonic stem cells (ESCs) as a model that is versatile for renewal and differentiation studies. How this relates to mammary adult stem cells (ASCs) is not entirely clear. Overall, the manuscript contains significant technical and conceptual limitations, and the data presented do not support the major conclusions of the study. There are two overarching issues that question the validity of most of the findings in this study. Firstly, there is no clear demonstration that the structures reported as 3D organoids are indeed driven by multipotent stem cells (in all data and experimental approaches associated with this). Secondly, there is a lack of evidence to support the claim that CD44high CD24low cells are stem cells with an exclusive or enhanced capacity to generate multi-lineage organoids.

In addition to these general points, there are several specific major issues summarized below:

1/ Authors base their findings about mammary ASC renewal using a poorly defined organoid culture system that they claim is driven by ASC renewal and differentiation. These organoid growth conditions were originally developed to support growth of bronchial epithelial cells, and the authors have not presented data to objectively assess the validity of this extrapolation to expansion of mammary organoids. The authors did not present data to support the notion that these growth conditions generate multi-lineage organoids that expand from multipotent mammary stem cells.

• Response 1:
• This concern has been also raised by the 1st reviewer (See Response 12 from Reviewer 1).
• Our experiments will confirm that our growth conditions (which will be more comprehensively described in the methods section) can generate multi-lineage organoids from multipotent mammary stem cells. We will include these characterizations in the new version of the manuscript.

2/ Authors claim that miR-106a-3p downregulates stem cell differentiation and utilize 'organoid' culture to track the temporal expression of OCT4, SOX2 and NANOG during phases of organoid renewal and differentiation. However, mammary stem cell differentiation is associated with the emergence of luminal progenitor, mature luminal and myoepithelial lineages that are characterized by the expression of a well-defined set of markers. The authors did not investigate the expression of these markers in their 'differentiation' settings. Furthermore, modulators of major pathways reported to be critical for mammary ASC maintenance are lacking, including modulators of WNT, TGF/BMP, Notch and other pathways. As such, it is difficult to ascertain that organoids emerging under such culture conditions are the result of stem cell renewal and differentiation, as opposed to lineage-restricted proliferative non-ASCs, thus questioning the validity of many of the findings in this work.

• Response 2:

• As suggested by the reviewer, we will investigate the expression of emergence of luminal progenitor, mature luminal and myoepithelial lineages in our 'differentiation' settings using flow cytometry. This analysis will involve the examination of multiple lineage-specific surface markers, including CD49f−/low/EpCAM+ for luminal progenitor cells and CD49f+/EpCAM−/low for basal/myoepithelial cells in the 3D context.

• Secondly, we agree with the reviewer that major pathways such as Wnt, TGFb/BMP and Notch have been reported to be critical for mammary ASC maintenance. As suggested by the reviewer, to further evaluate the possible involvement of these pathways, we have analyzed our transcriptomic data, using PROGENy pathway, to investigate which pathways are regulated. The major pathways are depicted in a new figure and will be included in the manuscript (See Revision Section part 2.2, for the revisions that have already been carried out).

• There was significant enrichment indicating down-regulation of TGFβ, MAPK, WNT, PI3K genes along with gene sets representing other oncogenic pathways, are up-regulated such as the hypoxia response, JAK/STAT pathway, and p53 pathway activity (Figure A and B). Stem cells possess self-renewal activities and multipotency, characteristics that tend to be maintained under hypoxic microenvironments [1], thus this is not surprising to observe an up-regulation of Hypoxia pathway and activation of HIF1α transcription factor. In mammary stem cells, it has also been shown that p53 is critical to control the maintenance of a constant number of stem cells pool [2, 3]. Remarkably, it has been shown that cell sorting of the cells with a putative cancer stem cell phenotype (CD44+/CD24 low) express a constitutive activation of Jak-STAT pathway [4], which we observed as up-regulated along with STAT1 and STAT2 transcription factors. In parallel, we observe a down-regulation of Wnt signaling as well as PI3K pathways. Wnt is known to play important role in the maintenance of stem cells; its inhibition has been shown to lead to the inactivation of PI3 kinase signaling pathways to ensures a balance control of stem cell renewal [5]. Moreover, we observe a down-regulation of SMAD4 and SMAD3 transcription factors correlated with a down-regulation of TGFβ pathway. Signals mediated by TGF-β family members have been implicated in the maintenance and differentiation of various types of somatic stem cells [6].

• References

• Semenza GL. Dynamic regulation of stem cell specification and maintenance by hypoxia-inducible factors. Molecular aspects of medicine2016 Feb-Mar;47-48:15-23.

• Solozobova V, Blattner C. p53 in stem cells. World journal of biological chemistry2011 Sep 26;2(9):202-14.
• Cicalese A, Bonizzi G, Pasi CE, Faretta M, Ronzoni S, Giulini B et al. The tumor suppressor p53 regulates polarity of self-renewing divisions in mammary stem cells. Cell2009 Sep 18;138(6):1083-95.
• Hernandez-Vargas H, Ouzounova M, Le Calvez-Kelm F, Lambert MP, McKay-Chopin S, Tavtigian SV et al. Methylome analysis reveals Jak-STAT pathway deregulation in putative breast cancer stem cells. Epigenetics2011 Apr;6(4):428-39.
• He XC, Zhang J, Tong WG, Tawfik O, Ross J, Scoville DH et al. BMP signaling inhibits intestinal stem cell self-renewal through suppression of Wnt-beta-catenin signaling. Nature genetics2004 Oct;36(10):1117-21.
• Watabe T, Miyazono K. Roles of TGF-beta family signaling in stem cell renewal and differentiation. Cell research2009 Jan;19(1):103-15.

3/ The authors base their work on the claim that CD44high CD24low cells represent bona fide mammary ASCs. This claim is not support by functional work to show that organoid generation is exclusive to or enhanced in CD44high CD24low cells relative to other cells. The claim of differentiation of this stem cell population in vitro is not supported by data to show emergence of luminal progenitor, mature luminal and myoepithelial lineages that are characterized by the expression of a well-defined set of reported markers as abovementioned. Although miR-106a-3p is claimed to downregulate stem cell differentiation based on a gene set enrichment analysis, authors did not investigate the expression of mammary differentiation markers or the association of miR-106a-3p-transfected HMECs with gene set pathways involved in mammary gland differentiation.

• Response 3:
• This concern has been also raised by the 1st reviewer (See Response 1 from Reviewer 1). As explained in response 1, to address this point, we will perform an extensive characterization of our mammary primary cells as well as our 3D-matrigel embedded cultures using flow cytometry This analysis will involve multiple lineage-specific surface markers, including luminal alveolar progenitor (such as CD49f−/low/EpCAM+) and basal/myoepithelial cells (such as CD49f+/EpCAM−/low).
• Secondly, as suggested by the reviewer, we will investigate the expression of mammary differentiation markers or the association of miR-106a-3p-transfected human mammary epithelial cells with gene set pathways involved in mammary gland differentiation by bioinformatics using our transcriptomic data.

4/ Line 129: "Together, these results indicate that cells grown as organoids acquired a CD44high / CD24low expression pattern similar to that of stem/progenitor cells, which suggests that 3D organoids can be used to enrich breast stem cell markers for further screening". This conclusion is not supported by the data presented. It is not clear if the expression of these markers was acquired upon 3D culture. It could be that 3D culture better maintained and expanded already existing CD44high CD24low cells in 2D culture. It is also unclear if these cells are indeed organoid-forming. Authors have not isolated and tested the organoid-forming capacity of CD44high CD24low cells relative to other cells. Along the same line, the conclusion that " mir-106a-3p directly promotes the "transdifferentiation" of CD44low/CD24high cell phenotype into CD44high/CD24low cell phenotype" isn't justified. Experiments required to conclude that 'transdifferentiation' is involved are lacking. miR-106a-3p overexpression could be creating conditions that are permissive for expansion of already existing CD44high CD24low cells as opposed to 'transdifferentiation' of other cell types into this phenotype. The authors could FACS-isolate CD44low CD24low cells and treat these with control or miR-106a-3p to conclusively establish 'transdifferentiation'.

• Response 4:
• This concern has been also raised by the 1st reviewer (See Response 12 from Reviewer 1). Transdifferentiation (lineage reprogramming, or -conversion), is a process in which one mature, specialized cell type changes into another without entering a pluripotent state. This process involves the ectopic expression of transcription factors and/or other stimuli. We agree with the reviewer that we did not demonstrate the transdifferentiation process in terms of lineage. Therefore, we will use flow cytometry to analyze multiple lineage-specific surface markers for luminal progenitor (CD49f−/low/EpCAM+), and basal/myoepithelial cells (CD49f+/EpCAM−/low) following miR-106a-3p expression.
• Additionally, we cannot exclude the possibility that the 3D culture better maintained and expanded the pre-existing CD44high CD24low cells, as suggested by the reviewer. The reviewer recommends FACS-isolating CD44low CD24low cells. We apologise for any lack of clarity in our description. Technically, our primary cells have a low percentage of colony-forming efficiency (CFE) in 3D and not enough cells for FACS isolation of CD44low and CD24low cells. Therefore, we leveraged our knowledge that the expression of CBX7 potentiates the growth of 3D structures. We decided to FACS-isolate the different subpopulations of CD44 and CD24 cells to further elucidate the expression of miR-106a-3p in the different CD44/CD24 cell subpopulations. CBX7-transfected human mammary epithelial cells showed enrichment in CD44high/CD24low cells as compared to empty vector-transfected human mammary epithelial cells (Figure 4A-B). Subsequently, we separated the CD44high/CD24low (green) population from the CD44high/CD24high cell populations (blue) using flow cytometry to analyze the role of the endogenous expression of miR-106a-3p. The CD44high/CD24low population was the only one to exhibit endogenous expression of miR-106a-3p (Figure 4C). Blocking the endogenous expression of miR-106a-3p with LNA-anti-miR-106a-3p or LNA-control (Figure 4D) impacted organoid generation (Figure 4E-F). We will modify the text accordingly to include this point and this figure will be moved in the supplemental figure.

5/ Line 242: "These data demonstrate that miR-106a-3p is involved in the early cell differentiation process into the three germ layers ". The authors have not conducted functional or mechanistic work to show that miR-106a-3p is involved in morphological or transcriptomic differentiation changes in ESCs. This and other data would be necessary to substantiate this conclusion.

• Response 5:
• Indeed, we agree that we cannot conclude that the miR-106a-3p is involved in the early cell differentiation process into the three germ layers without demonstrating the differentiation changes in ESCs through transcriptomic analysis. To clarify the take-home message, we did not include the transcriptomic characterization of the differentiation changes in ESCs. Instead, we focused on assessing the impact on Oct4, Sox2, and Nanog expression. However, to further understand the impact of miR-106a-3p depletion on hESCs differentiation, we have also monitored the expression of specific genes upon induction of the three embryonic germ layers (See Section Part 2.2 for a description of the experiments already carried out).

Selected technical points:

6) Figure 1A: The Y-axis label is misleading and suggests multiple organoids seeded per cell? Organoid Formation Efficiency (OFE) or Organoid Formation Capacity (OFC) are the commonly used nomenclature for this.

• Response 6:
• Since reviewer 1 found that the graph in Fig. 1A to be unnecessary, we have decided to remove this panel in the revised version of the manuscript. Furthermore, as suggested, we will replace the axis “Number of organoids per cell seeded” with “Organoid Formation Capacity” (OFC), which is the commonly used nomenclature for this measure in the article.

7) Figure 2G: X-axis unclear. Is this meant to investigate the percentage of cells expressing CD44/CD24 as double high, double low, high/low and low/high?

• Response 7:
• We thank the reviewer for this careful examination of the manuscript. We apologize for this error, and will make the corresponding adjustment in Figure 2G.

8) Figure 4C: In HMEC-CBX7 cells, it is unclear whether the high miR-106a-3p levels in CD44high CD24low cells are due to CBX7 expression. An important control, HMEC-Control Vector, is missing.

• Response 8:
• This control has been done (see Section 3, for details on experiments that have been carried out).

Reviewer #3 (Evidence, reproducibility and clarity):

In this study the authors identify miR-106a-3p as a potent inducer of organoid formation from HMECs. Overexpression of miR-106a-3p induced formation of more organoids, increased the number of stem/progenitor cells and overall positively affected the stemness properties of the organoids, likely by affecting SOx2, Oct4 and Nanog expression.

Major comments:

1/ the flow of the paper is confusing, it appears that the authors are trying to combine several non-completed studies into one paper. It is not immediately evident how is the rationale or the conclusion supported by published data. For example, is there published evidence that Sox2/Oct4/Nanog are expressed in healthy mammary gland stem cells in vivo, or whether they have a role in establishment of stem cell population?

• Response 1:
• There is still a controversy about the existence of unipotent, bipotent or multipotent stem cells in mammary gland tissue [7-9]. Notably, OCT4, SOX2, and NANOG collectively form the core transcriptional network responsible for maintaining pluripotency in embryonic stem cells [10]. Evidence has accumulated over the past few years, accumulating evidence has supported the presence of stem cells in both mouse and human mammary [11]. Various strategies have been used to identify and isolate human breast stem/progenitor cells, including FACS sorting based on cell surface antigen expression. In addition, an in vitro cell culture system has been described allowing the propagation of human mammary epithelial cells in an undifferentiated state through their ability to proliferate in suspension as non-adherent mammospheres [12].. Simoe et al have demonstrated that stem cells isolated from both normal human breast and breast tumor cells display an increased expression of the embryonic stem cell genes NANOG, OCT4 and SOX2 [13]. Moreover, they have shown that the ectopic expression of any one of these factors, but in particular NANOG and SOX2, in breast cancer cells increases the pool of stem cells and enhances the cells' ability to form mammospheres. They observed higher expression of NANOG, OCT4, and SOX2 in the stem cell populations CD44+CD24−/low and EMA+CALLA+ compared to the rest of the sample population. Cells overexpressing these factors displayed an increase in the stem cell populations, thereby confirming the role of Nanog, Oct4, and Sox2 in the maintenance of human mammary stem cells. We will include this rationale in the manuscript.

• References

• Van Keymeulen A, Rocha AS, Ousset M, Beck B, Bouvencourt G, Rock J et al. Distinct stem cells contribute to mammary gland development and maintenance. Nature2011 Oct 9;479(7372):189-93.

• Deome KB, Faulkin LJ, Jr., Bern HA, Blair PB. Development of mammary tumors from hyperplastic alveolar nodules transplanted into gland-free mammary fat pads of female C3H mice. Cancer research1959 Jun;19(5):515-20.
• Shackleton M, Vaillant F, Simpson KJ, Stingl J, Smyth GK, Asselin-Labat ML et al. Generation of a functional mammary gland from a single stem cell. Nature2006 Jan 5;439(7072):84-8.
• Boyer LA, Lee TI, Cole MF, Johnstone SE, Levine SS, Zucker JP et al. Core transcriptional regulatory circuitry in human embryonic stem cells. Cell2005 Sep 23;122(6):947-56.
• LaMarca HL, Rosen JM. Minireview: hormones and mammary cell fate--what will I become when I grow up? Endocrinology2008 Sep;149(9):4317-21.
• Dontu G, Abdallah WM, Foley JM, Jackson KW, Clarke MF, Kawamura MJ et al. In vitro propagation and transcriptional profiling of human mammary stem/progenitor cells. Genes & development2003 May 15;17(10):1253-70.
• Simoes BM, Piva M, Iriondo O, Comaills V, Lopez-Ruiz JA, Zabalza I et al. Effects of estrogen on the proportion of stem cells in the breast. Breast cancer research and treatment2011 Aug;129(1):23-35.

2/ The organoids are all spherical, while mammary gland is characterized by branching. Therefore, the organoids are not recapitulating the gland morphology and the validation should include wider range of molecular markers.

• Response 2:
• This concern has been also raised by both reviewers 1 and 2. As explained in response 1 to reviewer 1, we will perform a comprehensive characterization of our mammary primary cells as well as our 3D-matrigel embedded culture culture using flow cytometry to examine multiple lineage-specific surface markers, including luminal alveolar progenitor (such as CD49f−/low/EpCAM+), and basal/myoepithelial cells (such as CD49f+/EpCAM−/low). As a result, our experiments will collectively confirm that our growth conditions (which will be more thoroughly described in the methods section) for multipotent mammary stem cells can indeed generate multi-lineage organoids.

3/ The choice of control is not clear. For example, why was miR-106a-5p chosen as a control? And why choose miR-106a-5p when a better candidate would be miR-106b-3p, that produces very high number of organoids as well? And how did the other miRNAs affected the CD44/24 profile?

• Response 3:
• We apologize for any lack of clarity in our description. It's important to note that miRNAs consist of two strands, -5p and -3p, and both strands can coexist and play distinct roles. For example, paired species of members in the let-7 and mir-126 families coexist and have different regulatory functions in reprogramming and differentiation of embryonic stem cells [1]. Several deep sequencing studies have demonstrated the coexistence of 5p/3p pairs in approximately half of the miRNA populations analyzed [2, 3]. Therefore, to determine whether the biological effect specifically resulted from the -3p strand, we also assessed the -5p strand.

• References

• Koh W, Sheng CT, Tan B, Lee QY, Kuznetsov V, Kiang LS et al. Analysis of deep sequencing microRNA expression profile from human embryonic stem cells derived mesenchymal stem cells reveals possible role of let-7 microRNA family in downstream targeting of hepatic nuclear factor 4 alpha. BMC genomics2010 Feb 10;11 Suppl 1(Suppl 1):S6.

• Jagadeeswaran G, Zheng Y, Sumathipala N, Jiang H, Arrese EL, Soulages JL et al. Deep sequencing of small RNA libraries reveals dynamic regulation of conserved and novel microRNAs and microRNA-stars during silkworm development. BMC genomics2010 Jan 20;11:52.
• Kuchenbauer F, Mah SM, Heuser M, McPherson A, Ruschmann J, Rouhi A et al. Comprehensive analysis of mammalian miRNA* species and their role in myeloid cells. Blood2011 Sep 22;118(12):3350-8.

4/ What is the CD44/CD24 profile in the organoid cultures from Figure 7?

• Response 4:
• The CD44/CD24 profile from the organoid cultures from Figure 7 will be assessed in the revised manuscript.

Part 2.2 Following the experiment that have been already carried out that will be included in the manuscript after revisions.

Reviewer #1 (Evidence, reproducibility and clarity):

Major comments:

The model system used in this work is referred to as "organoids", with the premise that organoids, as representatives of the original tissue, can be used to study tissue development. However, the organoids presented in the study are spherical structures, and the paper does not provide any information about how and to what extent these organoids represent the original tissue. Furthermore, it would be difficult to expect these organoids to accurately represent human breast tissue, as they are derived, to the best of the reviewer's understanding (it is not explicitly noted, but rather the text refers the reader to several previous works), from primary human breast epithelial cells that had been cultured for 6 passages in 2D culture. The CD24/CD44 flow cytometry profile of these 2D cultures, as well as the organoids derived from them, shows a unimodal distribution of CD24 and CD44 expression, and does not show distinct cell populations, as typical in primary breast epithelial cells that have not been cultured in 2D.

• Response:
• First, we assessed the aldehyde dehydrogenase activity (ALDH) [14] in our primary cells to demonstrate that these culture conditions preserve stem/progenitor properties (See Figure A, below). Additionally, we conducted immuno-staining of primary cells in 2D culture for lineage-specific luminal markers (CK18, MUC1) and basal markers (CK14, CK5), which revealed the heterogeneity of our population (See Figure B, below).

FIGURE FOR REVIEWERS

• Reference

• Ginestier C, Hur MH, Charafe-Jauffret E, Monville F, Dutcher J, Brown M et al. ALDH1 is a marker of normal and malignant human mammary stem cells and a predictor of poor clinical outcome. Cell stem cell2007 Nov;1(5):555-67.

• For the characterization of the 3D culture, we have presented early time points of 3D cell growth, which are mainly spherical (until Day 8). However, differentiation occurs in a stepwise manner, where single stem cells proliferate to form small spheroids before undergoing multilineage differentiation into organoids that initiate branching (Day 10). Subsequently, ducts undergo budding and lobule formation (Day 20). We have included a time-course representation of this 3D growth to illustrate the differentiation process (See Figure 1C).

• Under these culture conditions, the 3D structure retains its self-renewal activity and the ability to reseed and regenerate secondary tissues. We have also assessed the self-renewal capacity of our 3D structure (See Figure 1D).

FIGURE FOR REVIEWERS<br />

Page 7 line 161: "mir-106a-3p directly promotes the "transdifferentiation" of CD44low/CD24high cells phenotype into CD44high/CD24low cell phenotype" - is an unsupported statement, given that there could be several alternative explanations for the observed change in population ratios, including effects on survival or growth of cells of a certain population.

• Indeed, we cannot exclude the possibility of other alternative explanations. Therefore, we have already assessed the impact of miR-106a-3p on population doubling in culture to determine whether it has an effect on the survival or growth of the cells. We observed that miR-V cells stopped growing after approximately 15 population doublings, indicating their limited proliferative potential. In contrast, we found that miR-106a extended the lifespan of the cells, suggesting an effect on cell survival (Figure below). We will include this information in the manuscript.

FIGURE FOR REVIEWERS

• Why was GATA3 not included in the last analysis depicted in Fig. 7?

• We apologize for any lack of clarity in our description. It's important to note that GATA3 was not included in Figure 7. As explained in the text, GATA3 plays a role in regulating Nanog expression. However, it's worth noting that the cells did not form organoids when GATA3 was depleted, as illustrated in the results below. We will include these results in the revised version of the manuscript.

FIGURE FOR REVIEWERS

Reviewer #2:

2/ Authors claim that miR-106a-3p downregulates stem cell differentiation and utilize 'organoid' culture to track the temporal expression of OCT4, SOX2 and NANOG during phases of organoid renewal and differentiation. However, mammary stem cell differentiation is associated with the emergence of luminal progenitor, mature luminal and myoepithelial lineages that are characterized by the expression of a well-defined set of markers. The authors did not investigate the expression of these markers in their 'differentiation' settings. Furthermore, modulators of major pathways reported to be critical for mammary ASC maintenance are lacking, including modulators of WNT, TGF/BMP, Notch and other pathways. As such, it is difficult to ascertain that organoids emerging under such culture conditions are the result of stem cell renewal and differentiation, as opposed to lineage-restricted proliferative non-ASCs, thus questioning the validity of many of the findings in this work.

• We agree with the reviewer that major pathways such as Wnt, TGFβ/BMP and Notch have been reported to be critical for mammary ASC maintenance. As suggested by the reviewer, to further evaluate the possible involvement of these pathways, we have analyzed our transcriptomic data, using the PROGENy R package (version 1.16.0) (https://doi.org/10.1038/s41467-017-02391-6) and DoRothEA (version 1.6.0)-decoupleR (version 2.1.6) computational pipeline (https://doi.org/10.1101/gr.240663.118, https://doi.org/10.1093/bioadv/vbac016), to investigate the differential activation of major signaling pathways and transcriptional factors. The major pathways are depicted in the figure below and will be included in the manuscript.

FIGURE FOR REVIEWERS

• There was significant enrichment indicating down-regulation of TGFβ, MAPK, WNT, PI3K genes along with gene sets representing other oncogenic pathways, are up-regulated such as the hypoxia response, JAK/STAT pathway, and p53 pathway activity (Figure A and B). Stem cells possess self-renewal activities and multipotency, characteristics that tend to be maintained under hypoxic microenvironments [15], thus this is not surprising to observe an up-regulation of Hypoxia pathway and activation of HIF1α transcription factor. In mammary stem cells, it has also been shown that p53 is critical to control the maintenance of a constant number of stem cells pool [16,17]. Remarkably, it has been shown that cell sorting of the cells with a putative cancer stem cell phenotype (CD44+/CD24 low) express a constitutive activation of Jak-STAT pathway [18], which we observed as up-regulated along with STAT1 and STAT2 transcription factors. In parallel, we observe a down-regulation of Wnt signaling as well as PI3K pathways. Wnt is known to play important role in the maintenance of stem cells; its inhibition has been shown to lead to the inactivation of PI3 kinase signaling pathways to ensure a balance control of stem cell renewal [19]. Moreover, we observe a down-regulation of SMAD4 and SMAD3 transcription factors correlated with a down-regulation of TGFβ pathway. Signals mediated by TGF-β family members have been implicated in the maintenance and differentiation of various types of somatic stem cells [20].

• References

• Semenza GL. Dynamic regulation of stem cell specification and maintenance by hypoxia-inducible factors. Molecular aspects of medicine2016 Feb-Mar;47-48:15-23.

• Solozobova V, Blattner C. p53 in stem cells. World journal of biological chemistry2011 Sep 26;2(9):202-14.
• Cicalese A, Bonizzi G, Pasi CE, Faretta M, Ronzoni S, Giulini B et al. The tumor suppressor p53 regulates polarity of self-renewing divisions in mammary stem cells. Cell2009 Sep 18;138(6):1083-95.

• Hernandez-Vargas H, Ouzounova M, Le Calvez-Kelm F, Lambert MP, McKay-Chopin S, Tavtigian SV et al. Methylome analysis reveals Jak-STAT pathway deregulation in putative breast cancer stem cells. Epigenetics2011 Apr;6(4):428-39.

• He XC, Zhang J, Tong WG, Tawfik O, Ross J, Scoville DH et al. BMP signaling inhibits intestinal stem cell self-renewal through suppression of Wnt-beta-catenin signaling. Nature genetics2004 Oct;36(10):1117-21.

• Watabe T, Miyazono K. Roles of TGF-beta family signaling in stem cell renewal and differentiation. Cell research2009 Jan;19(1):103-15.

5) Line 242: "These data demonstrate that miR-106a-3p is involved in the early cell differentiation process into the three germ layers ". The authors have not conducted functional or mechanistic work to show that miR-106a-3p is involved in morphological or transcriptomic differentiation changes in ESCs. This and other data would be necessary to substantiate this conclusion.

• Response:
• Indeed, we cannot conclude that miR-106a-3p is directly involved in the early cell differentiation process into the three germ layers without demonstrating the differentiation changes in ESCs through transcriptomic analysis. To clarify the take-home message, it's important to note that we did not include the transcriptomic characterization of differentiation changes in ESCs. Instead, we focused on assessing the impact of miR-106a-3p depletion on the expression of Oct4, Sox2, and Nanog. However, to gain a deeper understanding of the effects of miR-106a-3p depletion on hESCs differentiation, we also monitored the expression of specific genes upon the induction of the three embryonic germ layers (see Figure A, B, and C below). We observed that the expression of endodermal genes was not or only weakly affected by the level of miR-106a-3p expression (Figure A), whereas the expression of mesoderm- and ectoderm-specific genes increased upon miR-106a-3p down-regulation (Figure B and C). We will include these findings in the manuscript.

FIGURE FOR REVIEWERS

Reviewer 2 (Minor points)

3) Figure 4C: In HMEC-CBX7 cells, it is unclear whether the high miR-106a-3p levels in CD44high CD24low cells are due to CBX7 expression. An important control, HMEC-Control Vector, is missing.

• Response
• The control HMEC-Vector is shown in panel Figure 4A for the FACS analysis. In Figure 4C, we did not include the control since there is no expression of miR-106a-3p, but it's important to note that this control was included in the experiment. As illustrated, there is no miR-106a-3p expression in the HMEC control cells. We intend to include this panel in Figure 4 of the manuscript.

FIGURE FOR REVIEWERS

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Referee #3

Evidence, reproducibility and clarity

In this study the authors identify miR-106a-3p as a potent inducer of organoid formation from HMECs. Overexpression of miR-106a-3p induced formation of more organoids, increased the number of stem/progenitor cells and overall positively affected the stemness properties of the organoids, likely by affecting SOx2, Oct4 and Nanog expression.

Major comments: the flow of the paper is confusing, it appears that the authors are trying to combine several non-completed studies into one paper. It is not immediately evident how is the rationale or the conclusion supported by published data. For example, is there published evidence that Sox2/Oct4/Nanog are expressed in healthy mammary gland stem cells in vivo, or whether they have a role in establishment of stem cell population?<br /> The organoids are all spherical, while mammary gland is characterized by branching. Therefore, the organoids are not recapitulating the gland morphology and the validation should include wider range of molecular markers.<br /> The choice of control is not clear. For example, why was miR-106a-5p chosen as a control? And why choose miR-106a-5p when a better candidate would be miR-106b-3p, that produces very high number of organoids as well? And how did the other miRNAs affected the CD44/24 profile?<br /> What is the CD44/CD24 profile in the organoid cultures from Figure 7?

Significance

The study provides a novel methodology to enrich for the mammary stem cells. However, many of the experiments need further clarification.

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

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Referee #2

Evidence, reproducibility and clarity

In this work, Robert et al. utilize mammary organoid culture as an in vitro model of stem cell renewal and maintenance. Authors show that a putative mammary stem cell population, characterized as CD44high CD24low, is enriched in organoid culture relative to 2D monolayer culture. They conduct a microRNA (miR) screen and identify miR-106a-3p as a miRNA that enriches for stem cell (CD44high CD24low) and organoid formation capacity, confirming these findings using miR-106a-3p overexpressing cells. Authors also show that CBX7 overexpression achieves a similar enrichment in CD44high CD24low and organoid formation capacity in an miR-106a-3p dependent manner, though the rationale behind the connection between CBX7 and miR-106a-3p is not well defined. Finally, the manuscript conducts a transcriptomic analysis on miR-106a-3p-OE cells and aims to functionally validate its role in embryonic stem cells (ESCs) as a model that is versatile for renewal and differentiation studies. How this relates to mammary adult stem cells (ASCs) is not entirely clear.

Overall, the manuscript contains significant technical and conceptual limitations, and the data presented do not support the major conclusions of the study. There are two overarching issues that question the validity of most of the findings in this study. Firstly, there is no clear demonstration that the structures reported as 3D organoids are indeed driven by multipotent stem cells (in all data and experimental approaches associated with this). Secondly, there is a lack of evidence to support the claim that CD44high CD24low cells are stem cells with an exclusive or enhanced capacity to generate multi-lineage organoids.

In addition to these general points, there are several specific major issues summarized below:

1. Authors base their findings about mammary ASC renewal using a poorly defined organoid culture system that they claim is driven by ASC renewal and differentiation. These organoid growth conditions were originally developed to support growth of bronchial epithelial cells, and the authors have not presented data to objectively assess the validity of this extrapolation to expansion of mammary organoids. The authors did not present data to support the notion that these growth conditions generate multi-lineage organoids that expand from multipotent mammary stem cells.
2. Authors claim that miR-106a-3p downregulates stem cell differentiation and utilize 'organoid' culture to track the temporal expression of OCT4, SOX2 and NANOG during phases of organoid renewal and differentiation. However, mammary stem cell differentiation is associated with the emergence of luminal progenitor, mature luminal and myoepithelial lineages that are characterized by the expression of a well-defined set of markers. The authors did not investigate the expression of these markers in their 'differentiation' settings. Furthermore, modulators of major pathways reported to be critical for mammary ASC maintenance are lacking, including modulators of WNT, TGF/BMP, Notch and other pathways. As such, it is difficult to ascertain that organoids emerging under such culture conditions are the result of stem cell renewal and differentiation, as opposed to lineage-restricted proliferative non-ASCs, thus questioning the validity of many of the findings in this work.
3. The authors base their work on the claim that CD44high CD24low cells represent bona fide mammary ASCs. This claim is not support by functional work to show that organoid generation is exclusive to or enhanced in CD44high CD24low cells relative to other cells. The claim of differentiation of this stem cell population in vitro is not supported by data to show emergence of luminal progenitor, mature luminal and myoepithelial lineages that are characterized by the expression of a well-defined set of reported markers as abovementioned. Although miR-106a-3p is claimed to downregulate stem cell differentiation based on a gene set enrichment analysis, authors did not investigate the expression of mammary differentiation markers or the association of miR-106a-3p-transfected HMECs with gene set pathways involved in mammary gland differentiation.
4. Line 129: "Together, these results indicate that cells grown as organoids acquired a CD44high / CD24low expression pattern similar to that of stem/progenitor cells, which suggests that 3D organoids can be used to enrich breast stem cell markers for further screening".

This conclusion is not supported by the data presented. It is not clear if the expression of these markers was acquired upon 3D culture. It could be that 3D culture better maintained and expanded already existing CD44high CD24low cells in 2D culture. It is also unclear if these cells are indeed organoid-forming. Authors have not isolated and tested the organoid-forming capacity of CD44high CD24low cells relative to other cells. Along the same line, the conclusion that " mir-106a-3p directly promotes the "transdifferentiation" of CD44low/CD24high cell phenotype into CD44high/CD24low cell phenotype" isn't justified. Experiments required to conclude that 'transdifferentiation' is involved are lacking. miR-106a-3p overexpression could be creating conditions that are permissive for expansion of already existing CD44high CD24low cells as opposed to 'transdifferentiation' of other cell types into this phenotype. The authors could FACS-isolate CD44low CD24low cells and treat these with control or miR-106a-3p to conclusively establish 'transdifferentiation'.<br /> 5. Line 242: "These data demonstrate that miR-106a-3p is involved in the early cell differentiation process into the three germ layers "

The authors have not conducted functional or mechanistic work to show that miR-106a-3p is involved in morphological or transcriptomic differentiation changes in ESCs. This and other data would be necessary to substantiate this conclusion.

Selected technical points:

1. Figure 1A: The Y-axis label is misleading and suggests multiple organoids seeded per cell? Organoid Formation Efficiency (OFE) or Organoid Formation Capacity (OFC) are the commonly used nomenclature for this.
2. Figure 2G: X-axis unclear. Is this meant to investigate the percentage of cells expressing CD44/CD24 as double high, double low, high/low and low/high?
3. Figure 4C: In HMEC-CBX7 cells, it is unclear whether the high miR-106a-3p levels in CD44high CD24low cells are due to CBX7 expression. An important control, HMEC-Control Vector, is missing.

Significance

The findings in this report do not represent a sufficient conceptual advance in mammary stem cell biology. There are some interesting data on the role of miR-106a-3p in differentiation and regulation of pluripotency-inducing factors OCT4, SOX2 and NANOG. This is, however, more relevant to ESC biology. The data presented do not sufficiently explain the proposed transcriptional and molecular influences of miR-106a-3p on ESC maintenance and differentiation. Furthermore, there are multiple instances in the manuscript of overstating conclusions in a manner that is not supported by the data presented, as well as several instances of a conceptually premature extrapolation of various aspects of ESC biology to mammary ASC biology. It is not clear what literature or experimental findings serve as the basis for the author's connection between these two developmentally and temporally distinct aspects of tissue biology.

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Referee #1

Evidence, reproducibility and clarity

Major comments:

• The model system used in this work is referred to as "organoids", with the premise that organoids, as representatives of the original tissue, can be used to study tissue development. However, the organoids presented in the study are spherical structures, and the paper does not provide any information about how and to what extent these organoids represent the original tissue. Furthermore, it would be difficult to expect these organoids to accurately represent human breast tissue, as they are derived, to the best of the reviewer's understanding (it is not explicitly noted, but rather the text refers the reader to several previous works), from primary human breast epithelial cells that had been cultured for 6 passages in 2D culture. The CD24/CD44 flow cytometry profile of these 2D cultures, as well as the organoids derived from them, shows a unimodal distribution of CD24 and CD44 expression, and does not show distinct cell populations, as typical in primary breast epithelial cells that have not been cultured in 2D.
• There appears to be confusion between concepts: primarily confusing a basal phenotype with a stem cell phenotype, and progenitor activity with stem cell activity. Because the 3D organoid model does not display a replication of luminal differentiation, it cannot be used as a proxy for stem cell function. The results from the miRNA screen and the subsequent experiments support two conclusions: 1. miR-160b-3p leads to an enhanced mesenchymal phenotype, manifested by reduced CD24 and enhanced CD44 expression. 2. miR-160b-3p leads to increased organoid formation. The latter may be interpreted, at best, as higher basal progenitor activity, but is not a measure of stem cell activity, as that would require the cells to give rise to more than one lineage, which is not shown here.
• Overall, the information from figures 1-4 indicate that miR-160b-3p is driving and is associated with mesenchymal differentiation, possibly with EMT.
• In contrast to the work in the breast 3D culture model, the experiments with hESCs are interesting and do support a role of this miR in stemness.<br /> There are several relatively minor comments, that cumulatively somewhat undermine the strength of the work:
• Abstract: the sentence "organoids can be directly generated from human epithelial cells by only one miRNA, miR-106a-sp" needs better clarification.
• Page 5 line 103: HMECs is a term that generally refers to human mammary epithelial cells, not a specific derivation or subpopulation thereof.
• The graph in Fig. 1A is unnecessary, it shows only one bar.
• It is unclear if all the HMECs were derived from the same donor, or several donors. There is no information about the donor and how the tissue and cells were derived. In general, it is not entirely clear how the cells were collected, processed, stored, and cultured from the time they were obtained from the donor until their use in the current study.
• The key for Fig. 2D is unclear. The axes read "density" but the text refers to "intensity". Fluorescence intensity in flow cytometry is usually measured on a log scale. Differences on a linear scale are not usually considered meaningful. The authors should clarify why they chose a linear scale for this screen.
• In the miRNA screen, how long were the cells cultured after transfection, and was it enough time for them to shift phenotype?
• Page 6 line 154: The authors likely mean z-score, not z factor (two different things).
• Page 7 line 161: "mir-106a-3p directly promotes the "transdifferentiation" of CD44low/CD24high cells phenotype into CD44high/CD24low cell phenotype" - is an unsupported statement, given that there could be several alternative explanations for the observed change in population ratios, including effects on survival or growth of cells of a certain population.
• There is need for quantification of the phenotypes described in Fig. 3C
• Figures 3 D-F it is not clear if the graphs display percentage or mean number (there is discrepancy between figure text and figure legend text), and when percentage, not clear for figure 3F out of what.
• Fig. 5B, what is the statistical significance of the enrichment?
• Why was GATA3 not included in the last analysis depicted in Fig. 7?

Significance

This manuscript describes experiments that aim to explore the role of miR-160b-3p in stem cells. It uses primarily a model of breast epithelial cells in 3D Matrigel culture, termed organoids.

The first part of the paper describes a screen that identified miR-160b-3p as changing the expression profile of the two surface markers CD24 and CD44 in breast epithelial cells, which the authors refer to as a stem cell population, and enhancing organoid formation capability, which the authors interpret as stem cell capacity. In the second part of the paper, the experiments use another cell model - human embryonic stem cells (ESCs). In the second part, the authors link the expression of miR-160b-3p to the expression of Nanog, Sox2, and Oct4, which are key transcription factors that play essential roles in maintaining pluripotency and self-renewal of ESCs.<br /> The premise of the work is strong, namely that genetic screens that use an organoid model have the potential to uncover genes and pathways that direct tissue development and regulate stem cell fate and function. Several issues make it difficult to draw conclusions about stem cell function from the first part of the paper, namely the experiments with breast epithelial organoids. The second part of the paper is stronger and more convincing of the main claim, which is that miR-160b-3p has a role in stem cell maintenance.

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Reply to the reviewers

'The authors do not wish to provide a response at this time.' The response has been included in a PDF

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript attempts to answer how the maternal and paternal chromosomes are organized, and probe the determinants of this organization.

The authors use two divergent strains of worms - Bristol(N2) and Hawaiian - and hybrids progeny to study this as there are large regions of sequence variants between chromosome V in the two strains, making it an ideal candidate to design specific FISH probes. The authors build on their previously published work and optimize a protocol to trace chromosomes by using a multiple-probe FISH approach to investigate chromosome architecture. This approach is well illustrated in Figure 1.

Overall, this manuscript does a good job of describing a potentially useful technique with wide application. The claims about differences (and similarities) require statistical analysis to be appreciated, and much work is necessary to make the analysis approachable to readers outside the immediate field.

Major comments:

Nearly all claims regarding the organization, compactness and pair-wise distances of chromosomes lack any statistical measures of significance. This is particularly important for the clustering and scaling analysis. This makes interpretation of the claims made in the text impossible. For example, claims such as "the step size remained virtually unchanged" or "the paternal chromosomes adopt the maternal conformation in hybrids" cannot be currently analyzed.

Throughout the manuscript (including in the abstract), the authors use the term "sister chromosomes" to (presumably) refer to the maternal and paternal chromosomes. This is a confusing term, since "sister chromatids" usually refers to the identical products of DNA replication, and "homologous chromosomes" is usually used to describe the parental chromosomes. The term would ideally be changed, and at the very least, it should be clearly defined.

Presentation: The manuscript in its current state (excluding figure one) is essentially impossible to interpret by readers who are unfamiliar with this subfield. The authors could include a blurb on the methodology behind each data type to help the manuscript reach a larger audience. The pipeline, meaning, and potential caveats of the clustering analysis should also be explicated.

Other suggestions:

The use of Hi-C-like heatmaps is good, since they are commonly used and are clear and easy to understand. However, it would be best to explain how the FISH data were used to construct the maps. The implications of the map could also be better explained (e.g., that the red cluster means relatively looser regions, and the blue means more tightly compacted ones).

The last sentence in the Introduction does not make clear sense. How does the similarity between N2 & HI open up the possibility of interrogating inheritance effects?

Several of the additional analysis that could improve the paper are: 1. Measure the nucleus diameter in N2/HI hybrid and HI/N2 hybrid. 2. Normalize the spatial distance to the nucleus size, rather than directly using the distance. 3. Explore some of the patterns in the spatial distance plots (e.g., red/blue lines and boxes). Are the sequences that are in them any different between N2 and HI in a way that might be able to account for these patterns?

Significance

The manuscript introduces a technical advance in the study of chromosomal territories - an important area of study that benefitted from recent advances in microscopy and in development of FISH approaches. However, it lacks mechanistic analysis and remains almost purely descriptive. It is also not clear what motivated the work beyond the technical feasibility. These issues make it impossible to assign biological significance to the seemingly minor differences that are documented.

However, as a report of a technical advance, it could be useful to many chromosome biologists who might apply it to diverse organisms and biological questions.

I am a chromosome biologist working on worms. However, my research does not directly deal with parental effects or with the development of novel FISH methodologies, so I did not examine claims regarding these specific points.

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Referee #2

Evidence, reproducibility and clarity

Building on their previous work using sequential fluorescent in situ hybridization (FISH) to follow the path of entire chromosomes in C. elegans (Sawh et al. 2020; Sawh and Mango 2020), the authors developed and then applied a method that distinguishes maternal and paternal homologs. In particular, they designed probes specific for ChrV in two strains, N2 and HI, and then demonstrated their effectiveness in homozygotes and hybrids. They found that HI ChrV is more compact in HI homozygotes as compared to N2 homozygotes, but decompacts in the F1 of N2 hermaphrodites x HI males. A different outcome was observed with respect to decompaction in the reverse cross, where both N2p and HIm ChrV chromosomes (p=paternal, m=maternal) exhibit decompaction. Through unsupervised clustering, the authors further found both dominant and minor patterns of chromosome-wide organization, with maternal chromosomes similar in terms of their dominant clusters regardless of the direction of the cross, but paternal chromosomes less so. Finally, the authors measured the degree to which homologous chromosomes interact, concluding that, although homologs overlap quite frequently, they rarely align (pair).

In sum, the significance of the authors' work lies in its chromosome-level observations and the application of computationally designed probes that distinguish homologs by targeting strain-specific insertions. While homolog distinction by FISH has been previously demonstrated, this study is the first to demonstrate this approach in C. elegans as well as implement it via insertions in a chromosome-wide manner. As such, the manuscripts should be of interest to a broad range of researchers, especially those in the fields of genetics, genomics, and 3D genome organization. That said, the study falls short in several ways, and we recommend the authors i) present a more thorough summary of what is known about homolog positioning across species, ii) describe how homologs have been previously distinguished by FISH and, thus, more clearly elucidate the specific advances they have enabled, iii) ground their work in more rigorous quantitation, and iii) provide a better description of the technologies (strengths as well as limitations) carried over from their previous studies so that readers can better evaluate the current study. We detail our suggestions and questions, below:

Major Comments:

1. Page 1: We suggest the authors broaden the reach of their introduction to include well-known examples outside of C. elegans of the impact of parent-of-origin on 3D genome organization. Such examples would include X-inactivation, selective silencing of paternal genomes, the physical elimination of paternal chromosomes, and the like.
2. Page 1: We also suggest the authors consider including mention of observations from the following research publications and review:

Mayer W et al. Spatial separation of parental genomes in preimplantation mouse embryos. 2003 PMC2169371

Reichmann J et al. Dual-spindle formation in zygotes keeps parental genomes apart in early mammalian embryos. 2018 PMID: 30002254

Nagele R, Freeman T, McMorrow L, Lee HY. Precise spatial positioning of chromosomes during prometaphase: evidence for chromosomal order. 1995 PMID: 8525379

Hua LL et al. Mitotic antipairing of homologous and sex chromosomes via spatial restriction of two haploid sets. 2018 PMID: 30530674

Hua LL, Casas CJ, Mikawa T. Mitotic antipairing of homologous chromosomes. 2022 PMC9731508 3. Page 5: The authors designed their strain-specific probes to target 172 insertions that are over 1 kb in size and distributed across ChrV. We ask the authors to describe these insertions in greater detail, especially as, later in the manuscript, the authors touch on the possibility that sequence differences between the two strains may account for differences in chromatin architecture. How many insertions were on the N2 and HI chromosomes, respectively? What is the range and distribution of insertion sizes for all insertions as well as specifically for the N2 and HI ChrV chromosome? Do the insertions contain repetitive sequences, or are they predominantly composed of unique sequences? What is their distribution with respect to genes, active regions, TADs? Is there an explanation for why some are clustered? If they contain genes, are the genes enriched in certain GO categories? Do the insertions differ in their characteristics across the different chromosomes? This information could be included as graphs and/or tables. 4. Page 5: Given that N2 and HI ChrV chromosomes differ by the number of insertions and, ultimately, probes, how might these differences have skewed the authors' results, especially with respect to overlap between the homologs? Here, simulations of different ratios of insertions between N2 and HI could be clarifying. 5. What difficulties were encountered when tracing the paths of overlapping homologs, and how were these difficulties accounted for and/or solved? Did the different numbers and distributions of insertions between N2 and HI exacerbate the challenge? What confidence levels accompanied their findings? 6. Page 4: It would be helpful if the authors to put their insertion-based method into the context of other studies that have developed and used FISH to distinguish homologs. 7. Pag 6: It would clarifying if the authors provided details about the mis-annotation of the Thompson genome and how it is pertains to probe design. 8. Page 6: The authors state that "...N2 and HI...harbor sequence differences, some of which are predicted to affect chromatin architecture" and that HI lacks ppw-1. We ask the authors to provide a more thorough discussion. To what extent might such predictions rest on the insertional differences between the strains? 9. Page 7: How much smaller is the HI genome and what percent of this difference is due to insertions (deletions)? Related to this, how much smaller is the HI ChrV chromosome as compared to N2? 10. Page 7 and throughout: For those readers who have not read Sawh and Mango 2020 and Sawh et al. 2020, or who are unfamiliar with the broader category of imaging technologies that support the current study, we ask the authors to provide much more background and citations to key methods. Without this information, many readers will neither sufficiently understand the strategies used for imaging acquisition, processing, and analysis nor grasp the relevance of terms such as step size, polymer step size, power-law fitting, etc. and therefore be less able to assess the authors' data and conclusions. 11. General statement: When the authors infer similarity or differences between power-law fittings, scaling exponents, step sizes, etc. what is the statistical significance of those comparisons? 12. Experiments in general: We suggest the authors provide considerably more quantitation. For example, we urge them to provide the number of trials, sample sizes, numbers of embryos examined for all experiments. Equally important would be information regarding the stage of embryos examined and, where more than one embryonic stage was involved, the number of embryos for each stage. Are there stage-specific changes? We are also concerned about the impact of mixed populations of embryos on studies using unsupervised clustering. In other words, what was the contribution of developmental stage to the outcome of the clustering? Furthermore, if not all nuclei in an embryo were captured, we ask the authors to give the percent of nuclei captured from an embryo and reasons why only a subset of nuclei were included in the analysis. 13. With regard to cluster analyses both here and elsewhere, will the authors please include statements of statistical significance whenever they note differences and/or similarities? 14. Page 8: It would be helpful if the authors explained how they implemented the nearest-neighbor approach, including caveats and limitations (success rates, drop-out rates, etc.) and providing statistical assessment wherever possible. 15. Page 8: "In some instances (6-8% of traces), traces were ambiguous and excluded from further analysis". We ask the authors to provide more detail. For example, what does ambiguous mean and, with respect to the 6-8% value, what was the total number of traces? What was the distribution of all traces (prior to filtering) with respect to percent of targets detected? Also, how coincident were the two homologs of a nucleus to each other in terms of capturing all the targets? 16. Page 8: "...we classified traces into N2 or HI based on whether the trace was located closest to a strain marking volume for N2 or HI." Will the authors please quantify "closest" and explain what this means, whether there was a cut-off and, if there had been, how it was determined and implemented? What percent of cells were problematic, and were there traces that did not overlap the strain marking volumes at all? As stated in the Materials and Methods, only a subset of traced chromosomes were analyzed for overlap - why were only a subset analyzed for overlap, how was the subset selected, and how many/what percentage did these traces represent? It would also be helpful if the authors provided a quantitative summary of the traces. 17. Page 8: Did the authors account for chromatic aberration and, if so, what protocol did they use? 18. Page 8: "...counting how often more than two N2 or HI traces were detected in one nucleus." This is puzzling, and we suggest that the authors include explanations for how this might have happened. Did the nuclei not contain signal from the other strain marking probe at all? Was there a bias for this to happen with N2 or HI chromosomes? Could this have been a consequence of biology or of the algorithm for tracing? The authors' observations are reminiscent of the many implications raised by Jia et al. (2023; A spatial genome aligner for resolving chromatin architectures from multiplexed DNA FISH. PMID: 36593410), and we ask the authors to comment on the relevance of their observations to those in this recent publication. 19. Page 8: "We found only a minority of 2% of HI traces and 7% of N2 traces were mis-assigned and excluded these from downstream analysis." 2% and 7% of what total? 20. Page 8: How do pairwise distances remain almost identical between N2 and HI and yet generate different scaling exponents? 21. Page 9: Figure 1F shows images of embryos derived from N2 hermaphrodites x HI males. It would be helpful if the authors added analogous images from the reciprocal cross as a supplementary figure. 22. Page 2, 9, 9, and 12: The authors make several comments regarding the action of factors in trans: "... factors from the mother impact chromosome folding in trans (p. 2)"; "... the HIp decompacts when subjected to the N2m environment and implies that the paternal chromosome is influenced by the maternal environment in trans (p. 9)"; "...N2 chromosomes influence HI chromosomes in trans, while N2 chromosome structure seems to be resistant to influences by the HI chromosomes (p. 9)"; and "...implicating maternal factors that act in trans (p. 12). While provocative, these statements call for more concrete consideration. Are the authors using "in trans" in lieu of "indirectly", or are they alluding to factors, such as ppw-1, or direct physical contact? Without further substantiation or argument, mention of in trans activity might best be reserved for the Discussion. 23. Page 10: "While HIp subpopulations were characterized by folding of one or the other chromosome arm, N2p clusters were more open and a subpopulation with a highly folded right arm was not present" (Figure 5CD). Was there a significant correlation between left vs. right arm folding and overall genome organization and function? 24. Page 11: Will the authors please provide a more explicit definition of alignment as well as a more detailed description of how alignment is quantified in the main text? 25. Page 11: With respect to direct physical contact, the authors mention transvection, which they conclude in the abstract is unlikely because pairing between homologs was observed to be rare. As transvection and pairing can both be short-lived, and the data are not compelling, the statement may need to be toned down considerably and/or be moved to the discussion. 26. Page 11: The authors draw a distinction between % territory overlap and physical distances between homologs. In particular, the differences between % overlap across different stages is quite interesting and potentially suggests embryo stage-specific changes. Could the authors explore this further by breaking down mean pairwise distances into different embryo stages (Figure 6B and C)? 27. Pages 2, 11-13: When the authors use "sisters", do they mean "homologs"? If the latter, we recommend they use "homologs", only, as "sisters" refers to the sister chromatids after replication. If, however, the authors are using "sisters" to mean sister chromatids, will they please explain how their data can distinguish sisters? 28. Discussion: We encourage the authors to speculate further regarding the basis of decompaction. Is it a hybrid-specific phenomenon?

Minor comments:

1. Page 1: Although the introduction focuses on C. elegans, the genome length that is mentioned (2 meters) is more aligned with that of mammalian species. The authors could cite a range of lengths or make more clear which species is being discussed.
2. Page 5: As the figures label the strains as Hawaiian and Bristol, the authors might wish to include this nomenclature in the main text. Curiously, the authors use several different spellings for the Hawaiian/Hawai'ian/Hawaiin/Hawaii strain.
3. Page 5: Will the authors please explain why the common whole-chromosome tracing probes have only one tail, while the strain-specific probes have two tails, as shown in Figure 1D?
4. Figures in general: The axes of a number graphs and heat maps need to be labeled.
5. Materials and Methods: The section on "Cluster analysis" is missing units for the resolution.
6. Page 8: Will the authors please give a reference for and explain watershed segmentation?

Significance

In sum, the significance of the authors' work lies in its chromosome-level observations and the application of computationally designed probes that distinguish homologs by targeting strain-specific insertions. While homolog distinction by FISH has been previously demonstrated, this study is the first to demonstrate this approach in C. elegans as well as implement it via insertions in a chromosome-wide manner. As such, the manuscript should be of interest to a broad range of researchers, especially those in the fields of genetics, genomics, and 3D genome organization. That said, the study falls short in several ways, and we recommend the authors i) present a more thorough summary of what is known about homolog positioning across species, ii) describe how homologs have been previously distinguished by FISH and, thus, more clearly elucidate the specific advances they have enabled, iii) ground their work in more rigorous quantitation, and iii) provide a better description of the technologies (strengths as well as limitations) carried over from their previous studies so that readers can better evaluate the current study.

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Referee #1

Evidence, reproducibility and clarity

The authors designed an elegant series of FISH probes taking advantage of insertions that are divergent between HI and N2 strains of C. elegans to identify the maternal versus paternal chromosomes in hybrid embryos. Overall, the conclusions are well supported by the data. I only have minor comments, which are numbered below in relation to each figure.

In figure 1 they demonstrate that the probes can specifically recognize their corresponding chromosome in hybrid embryos

In figure 2 they demonstrate that overall chromosome 5 adopts a similar shape from both strains.

In figure 3, they demonstrate that in the hybrids, the chromosomes are generally the same as in the homozygous embryos. However, when the HI chromosome is brought in paternally in the hybrids, it is more decompacted. In this cross, the maternal N2 chromosome is normal. In figure 5, when the N2 chromosome is now brought in paternally, it is similarly decompacted. However, in this cross, the HI chromosome that is brought in maternally is also decompacted. This appears to be the biggest difference, but is somewhat mitigated by a decrease in the scaling component, which I believe means it takes a straighter path? This is in contrast to the reciprocal cross where the maternal N2 chromosome is normal.

1. In figures 2-4, it is important to note what stages of embryos are being analyzed and whether any analysis was done to determine if the chromosomes varied with embryonic stage?
2. The authors need to clearly define chromosomal step size, scaling coefficient and pair wise distance and then describe the difference between these measurements. For example, it would be nice in relation to figure 4F if it was described exactly what it means to have an increase in step size along with a decrease in scaling exponent. This will enable the reader to more easily interpret the results.
3. Is there any way to determine if changes in the step size and scaling are significant? It would be good to know if the changes are actually significant.

In figure 5, the authors examine sub-clusters of where individual chromosomes locate. 4. In figure 5 (and maybe in earlier figures as well), it would also be helpful to mark the different clusters in the figures to show what is meant by a folder arm or a compacted central domain and refer to every panel in the text (only some descriptions in the text reference specific panels).

In figure 6, the authors determine whether the two chromosomes 5's overlap in nuclear territory and whether they the align along the length of the chromosome. From this analysis, they conclude that the chromosomes overlap a fair amount of time, but do not align. This makes it unlikely that transvection might occur. 5. In figure 6, the authors need to do a better job of describing how the data is being presented. The % overlap is being graphed by density, but density of what? Also, the text mentions the total number of nuclei that overlap, but how is that number derived from the presented data? Finally, the data are broken down by embryonic stage, but there is no mention of this in the text. It is not mentioned until the discussion. Overall, this makes it very difficult to determine what the data are showing. 6. In the discussion, the authors perhaps should spend more time interpreting their results in light of others work on the maternal and paternal inheritance of chromatin in C. elegans. For example, Arico et al 2011 Plos Genetics from the Kelly Lab. In addition to examining chromatin in the early embryo, in this paper the authors examine translocations, which might be interesting to look at using the technique presented here. Also, a number of recent papers from the Strome lab have examined chromatin inheritance from sperm. It would be interesting to interpret the finding that paternal chromosomes are influenced by the maternal environment, in light of this work.

Significance

These studies are the important extension of the elegant chromosome tracing that the Mango lab has pioneered. The authors have clearly demonstrated that the technique works well to identify individual chromosomes in a hybrid background. This provides the opportunity for the system to be used in numerous different ways, not just in C. elegans. This is the most significant advance of this paper and should be of interest to a fairly broad audience. However, using this technique, the authors also provide the initial characterization of sister chromosomes in C. elegans embryos and draw important initial conclusions, such as finding that the chromosomes do not pair, as they do in Drosophila. This makes the paper of interest to the C. elegans audience, as well as the general field of chromosomal organization. My expertise is in C. elegans biology and chromatin biology in general. I also am familiar with the field of chromosome biology. As a result, I believe I am capable of judging the significance of this paper in these areas.

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Reply to the reviewers

Point-by-point response to reviewers, including our plans for the revision:

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

* Summary: In this manuscript by the Sanson group, Lye and colleagues try to definitively answer the question of whether pulling forces from the ventral mesoderm have significant effects on convergent extension in the Drosophila germband (germband extension). While germband extension does occur in mutant embryos lacking mesoderm invagination, it has long been an open question in the field as to whether ventral pulling forces from the mesoderm have significant effects (positive or negative) on cell intercalation during germband extension. To definitely address this question, Lye and colleagues generated high-quality, directly comparable datasets from wild-type and twist mutant embryos, and then systematically assessed nearly all aspects of cell intercalation, myosin recruitment, and tissue elongation over time. They demonstrate that pulling forces from the ventral mesoderm have negligible impacts on the course of germband extension. While there are indeed some interesting differences between wild-type and twist embryos with respect to cell intercalation and myosin recruitment, such differences are relatively minor. They conclude that the events of germband extension neither require nor are strongly affected by external forces from the mesoderm. While this is largely a negative results paper, I believe that it should be published and that it will be an impactful paper within the field. Namely, it will settle once and for all the question of whether mesoderm invagination is required for optimal germband extension in the early Drosophila embryo, and it suggests that tissues are largely autonomous developmental units that are buffered from outside mechanical inputs.*

• * *Major comments: *

* It seems to me that the one obvious omission from this paper is a general measure of convergent extension over time. I think it would be useful to the reader to include some measure of change in tissue aspect ratio over time between wild-type and twist embryos. This could be included in Figure 5 or 6. *

• *

We are happy to include a graph with what we call “tissue strain rate”, which measures the deformation of the germ-band in the direction of extension (along AP) over time, and propose to add it as a panel in Supplementary Figure 6. Note that in our measures, the “tissue” strain rate is decomposed into contributions from two cell behaviors, the “cell intercalation” strain rate and the “cell shape” strain rate (Blanchard et al., 2009). “Tissue” and “cell shape” strain rate are directly measured, and “cell intercalation” strain rate is what remains when “cell shape” strain rate is removed from “tissue” strain rate. The “cell intercalation” strain rate calculated in that way is a “continuous” measure of cell intercalation, measuring the progressive shearing of cells during convergent extension. We also use a “discrete” measure of cell intercalation, which measures the number of cell neighbor exchanges, also called T1 swaps. We found that both “continuous” and “discrete” measures of cell intercalation are unchanged in twist mutant compared to wild-type embryos (Fig. 6F and 6E, respectively). In contrast, we find that the “cell shape” strain rate is increased in twist mutants (Fig. 5B and Fig. 5S1A). Consistent with this finding, the “tissue” strain rate is also increased in twist mutants (see graph below).

Otherwise, I have no major comments on the experimental approach or the findings of this manuscript. It seems to me a straightforward and systematic approach for determining whether mesoderm invagination affects germband extension. I do have several minor comments that should be addressed prior to publication (below).

*Minor comments: *

*I understand why cells would initially stretch more along the DV axis in wild-type embryos compared with twist embryos, but why do cells become so much more stretched along the AP axis (and become smaller apically) after 10 minutes of GBE in wild type compared with twist (Figure 2C and E). *

*I think this is an interesting and non-intuitive result that would warrant a bit of explanation/conjecture. *

This is not what Fig. 2C and E show, and we realize now that our schematics on the graphs might have been confusing. We will work on those to improve their clarity (or remove them), and also review our text.

Figure 2C shows how cells deform along DV (cell shape strain rate projected onto the DV axis). So the graph does not show that the cells are elongating in AP, as only the DV component of the strain rate is shown in this figure. In the wild type, the DV strain rate is positive (the cells are elongating in DV) at developmental times when the mesoderm invaginate (from about -10 minutes to until 7.5 minutes). The DV strain shows an acceleration until about 5 mins, then decelerates, crossing the x-axis to become negative at 7.5 minutes. From this timepoint and until the end of GBE, the DV strain rate is negative (the cells are contracting along DV). Mirroring the positive section of the curve, the DV contraction of the cells accelerate until about 12 mins and then slows down. The strong rate of DV contraction between 7.5 and 20 mins could in part be due to the endoderm invagination pulling in the orthogonal direction (AP) and helping the cells regaining a more isotropic shape. We could add a mention about this in the discussion.

In Figure 2E, the rate of change in cell area follows a similar time course in the wild type, showing that the cells are increasing their areas until about 10 mins (positive values) and then reduce their areas again until the end of GBE (negative values). Note that the graph does not show raw (instantaneous) cell areas as suggested by the comment, but rather a rate of change.

So in wild type, the cells get stretched by the invaginating mesoderm, and once the mesoderm is not pulling anymore, the cells appear to relax back. As there is no stretching in twist mutants, there is no equivalent relaxation of the cells along DV. Note that in twist, there is a milder increase in cell area in the first 15 mins of GBE (Fig. 2E). This could again be caused by the pull from endoderm invagination stretching the cells along AP, which, as we have shown before, increases both cell shape strain rates along AP and cell areas (Butler et al., 2009). So the pull from endoderm invagination (along AP) will have an impact on cell area rates of change and possibly also, indirectly, on DV cell shape strain rates, in both twist and wild type embryos, during most of GBE. Therefore cell area and DV cell shape strain rates are affected by more than one process during GBE. In this paper, we are focusing on the impact of mesoderm invagination, which happens around the start of GBE, so have focused our analysis of the graphs in the results section to this period, and the differences between wildtype and *twist. *

*I don't understand how you are defining cell orientation in Figure 2G. How are you choosing the cell axis that you are then comparing with the body axis? Is it the long axis, or something more complicated than that? I think you should briefly provide this information in the results section. If it is included in the methods, I wasn't able to locate it. *

Yes, it is the orientation of the long axis of the cell relative to the antero-posterior embryonic axis. We will clarify this in the text, in particular in the Methods, and also try improve our schematics.

Figure 2: Since you have the space, it might help the reader if you simply wrote out "strain rate" for panels B, D, and F, rather that used the abbreviation "SR." Thank you for this suggestion, we will reduce use of abbreviations where space permits.

*Please ensure that all axis labels are fully visible in the final figures. In several figures, the Y-axis labels were cut off (e.g., Fig 2I, 4A, 4D, 6B, 6C). *

These were visible to us in our submitted version, but of course we will ensure everything is visible on the final version.

*Where space permits, I would suggest using fewer abbreviations in axis labels to increase readability of the figures (e.g., in Figures 3H or 4D). *

Thank you for this suggestion, will do.

* In Figure 7, I would move the wild-type panels to the left and the twist panels to the right. I think it is more conventional to describe the normal wild-type scenarios first, and then contrast the mutant state.*

Will do.

To be consistent with the literature, "wildtype" should be hyphenated (wild-type) when used as an adjective, or two separate words (wild type) when used as a noun. Thank you, we will change this.

Review*er #1 (Significance (Required)): *

* Advance: The advances in this manuscript are largely methodological, but the experiments and analyses are quite rigorous and allow the authors to make strong conclusions concerning their hypotheses. Their findings are based on a high-quality collection of movies from control and twist mutant embryos expressing a cell membrane marker and knock-in GFP-tagged myosin. Importantly, I think the researchers were correct in choosing to analyze twist single-mutant embryos (as opposed to snail or twist, snail double-mutant embryos), as the overall embryo geometry of these mutants is fairly similar to wild-type embryos, allowing the researchers to directly compare cell behaviors and myosin dynamics during germband extension. This approach also allows them to avoid indirect effects on the germband due to a completely non-internalized mesoderm. *

*

Audience: The primary audience for this article will be basic science researchers working in the early Drosophila embryo who are interested in the interplay between the germband and neighboring tissues. Secondary audiences will include developmental biologists more broadly who are interested in biomechanical coupling (or in this case decoupling) of neighboring tissues. *

*

Describe your expertise: I have been a Drosophila developmental geneticist for over twenty years, and I have been working directly on Drosophila germband extension for over a decade. I have published numerous papers and reviews in this field, and I am very familiar with the genetic backgrounds and types of experimental analyses used in this manuscript. Therefore, I believe I am highly qualified to serve as a reviewer for this manuscript.*

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

*

In the present manuscript, Lye et al. describe a highly detailed quantification of cell shape changes during germband extension in Drosophila melanogaster early embryo. During this process, ectodermal tissue contracts along the dorso-ventral axis, simultaneously expanding along the perpendicular antero-posterior direction, migrating from the ventral to the dorsal surface of the embryo as it extends. This important morphogenetic event is preceded by ventral furrow formation when mesodermal tissue (located in the ventral part of the embryo) contracts along the dorso-ventral axis and invaginates into the embryonic interior. The study compares cell shape dynamics in the wildtype Drosophila with that in the twist mutant, which largely lacks mesoderm and does not form ventral furrow. The major motivation of the study is to examine whether cellular behaviors and myosin recruitment in the ectoderm is cell autonomous, or if those cellular behaviors depend on mechanical interactions between mesoderm and ectoderm.*

• The authors first examine whether transcriptional patterning of key genes involved in germband extension is different between the wildtype and the twist mutant and find no significant difference. Next, the authors thoroughly quantify cellular behaviors and patterns of myosin recruitment in the two genetic backgrounds. A number of different measures are investigated, notably the rate of change in the degree of cellular asymmetry, rate of cell area change, rate of change of cell orientation, differences in myosin recruitment to cell edges of various orientation, as well as the rates of growth, shrinkage, and re-orientation of the various cellular interfaces. It is thoroughly documented how these quantities change as a function of developmental timing and spatial position within the embryo. These data serve basis for quantitative comparison between cellular dynamics in the two genetic backgrounds considered.*

• Overall, the study shows that cellular behaviors observed in the ectoderm are largely the same during the period of time following ventral furrow formation, as would be expected if those cellular behaviors were predominantly cell autonomous and not dependent on stresses generated in the mesoderm.*

• The data presented in the manuscript are of excellent quality and presentation is very clear.

Minor comments: none *

* Reviewer #2 (Significance (Required)): *

* I find that the study provides a thorough quantification of cell behaviors in a widely studied important model of morphogenesis. The work may be of particular interest for future model-to-data comparison, perhaps providing a basis for future modeling work. I therefore certainly think that this work warrants publication.*

• However, the results of the study largely parallel previous findings and do not appear novel or surprising. It is well established that in snail mutant that lack mesoderm entirely, germband extension proceeds largely normally. This well-established fact suggests that since tissue dynamics in complete absence of mesoderm are largely unaffected, behaviors of individual cells are likely to not be affected either*.

*The work is pretty much entirely observational, and for most part provides a more detailed documentation/quantification of previous findings. I do not think it is appropriate for high profile publication. *

We are not sure which evidence the reviewer is referring to here specifically. We agree that the single mutants twist or snail, or the double twist snail mutants do extend their germ-band. However, the question we are asking here, is how well do they extend their germband and to answer this question, quantitation is needed. The first quantitation of GBE were performed by (Irvine and Wieschaus, 1994). While they quantified GBE in various mutant contexts, they did not perform quantitation for snail, twist, or twist snail mutants. Instead, they refer to these mutants once in p839, with the following sentence: ”Additionally, twist and snail mutant embryos, which lack mesoderm, extend their germbands almost normally (Leptin and Grunewald, 1990; Simpson, 1983)*.” *

Following these earlier qualitative observations, various studies have quantified different aspects of GBE in mesoderm invagination mutants, with contradictory results. For example, some studies, including from our own lab, report a reduction in cell intercalation in the absence of mesoderm invagination (Butler et al., 2009; Wang et al., 2020), but there have also been reports that tissue extension and T1-transistions occur normally (Farrell et al., 2017)(see also introduction of our manuscript). These contradictory results have motivated our present study, and we have implemented rigorous comparison between wild type and mesoderm invagination mutants, being careful i) to check that the regions analyzed were comparable in terms of cell fate, and ii) to control for any confounding effects between experiments (see also response to reviewer 4, main question 2). We have also considered which mesoderm invagination mutants to use. We rejected snail or twist snail mutants because the absence of snail means that the mesodermal cells do not contract and thus stay at the surface of the embryo, which changes the spatial configuration of the embryo considerably and would make a fair quantitative comparison very difficult. Instead, we decided to use twist mutants, as in those, cell contractions still happen so the cells do not take as much space at the surface of the embryo, but the contractions are uncoordinated which means that there is no invagination (and we demonstrate here, no significant pulling on the ectoderm). We note that reviewer 1 highlights the merit of settling the question of the impact of mesoderm invagination on GBE and the pertinence of choosing twist mutants versus the alternatives (see also response to reviewer 4, suggestion 1).

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

During morphogenesis, the final shape of the tissue is not only dictated by mechanical forces generated within the tissue but can also be impacted by mechanical contributions from surrounding tissues. The way and extent to which tissue deformation is influenced by tissue-extrinsic forces are not well understood. In this work, Lye et al. investigated the potential influence of Drosophila mesoderm invagination on germband extension (GBE), an epithelial convergent extension process occurring during gastrulation. Drosophila GBE is genetically controlled by the AP patterning system, which determines planar polarized enrichment of non-muscle myosin II along the DV-oriented adherens junctions. Myosin contractions drive shrinking of DV-oriented junctions into 4-way vertices, followed by formation of new, AP-oriented junctions. This process results in cell intercalation, which causes tissue convergence along the DV-axis and extension along the AP-axis. In addition, GBE is facilitated by tissue-extrinsic pulling forces produced by invagination of the posterior endoderm. Interestingly, some recent studies suggest that the invagination of the mesoderm, which occurs immediately prior to GBE, also facilitates GBE. In the proposed mechanism, invaginating mesoderm pulls on the germband tissue along the DV-axis; the resulting strain of the germband cells generates a mechanotransduction effect that promotes myosin II recruitment to the DV-oriented junctions, thereby facilitating cell intercalation. Here, the authors revisited this proposed mechanotransduction effect using quantitative live imaging approaches. By comparing the wildtype embryos with twist mutants that fail to undergo mesoderm invagination, the authors show that although the DV-oriented strain of the germband cells was greatly reduced in the absence of mesoderm pulling, this defect had a negligible impact on junctional myosin density, myosin planar polarity, the rate of junction shrinkage or the rate of cell intercalation during GBE. A mild increase in the rate of new junction extension and a slight defect in cell orientation were observed in twist mutants, but these differences did not cause obvious defects in cell intercalation. The authors conclude that myosin II-mediated cell intercalation during GBE is robust to the extrinsic mechanical forces generated by mesoderm pulling.

• * *Overall, I found that the results described here are very interesting and of high quality. The data acquisition and analyses were elegantly performed, statistics were appropriately used, and the manuscript was clearly written. However, there are a few points where some further explanation or clarification is necessary, as detailed below: *

• The main conclusion of the manuscript relies on appropriate quantification of myosin intensity at cell junctions. It is therefore important that the methods of quantification are well justified. Below are a few questions regarding the methods used in the analyses:*

• -For myosin quantification, the authors state that "Background signal was subtracted by setting pixels of intensities up to 5 percentile set to zero for each timepoint" [Line826]. The rationale for selecting 5 percentile as the threshold for background should be explained. Also, how does this background value change over time? *

• *

For our normalization method, we stretched the intensity histogram of images to use the full dynamic range for quantification and enable meaningful comparison of intensities between different movies. The 5th percentile was chosen to set to zero intensity as this removed background signal without removing any structured Myosin signal (i.e., non-uniform, low level fluorescence - this was assessed by eye). We will provide some before and after normalization images at different timepoints to illustrate this (See reviewer 3, minor point 4 below). Since the cytoplasmic signal is uniform, it is difficult to discern from true ‘background’, therefore some cytoplasmic signal might be set to zero with this method, but all medial and junctional Myosin structures will still be visible and have none-zero intensity values. However, since cytoplasm takes up a large majority of pixels in the image, and we only set 5% of pixels to zero, the majority of the cytoplasm will have non-zero pixel values. ‘Background’ changes increases slightly as Myosin II levels increase in general over time, as expected from the embryo accumulating Myosin II as they develop.

-The authors mention that "Intensities varied slightly between experiments due to differences in laser intensity and therefore histograms of pixel intensities were stretched" [Line828]. The method of intensity justification should be justified. For example, does this normalization result in similar cytoplasmic myosin intensity between control and twist mutant embryos?

• *

As stated above, we stretched the intensity histogram of images to enable meaningful comparison of intensities between different movies, as stretching the histograms would bring Myosin II structures of similar intensities into the same pixel value range. We chose to stretch histograms using a reference timepoint (30 minutes, the latest timepoint analyzed), rather than on a per timepoint basis, because we saw a general increase in Myosin II over time, and we wanted to ensure that this increase was preserved in our analysis.

• *

Note that we quantify Myosin from 2 µm above to 2 µm below the level of the adherens junctions (see Methods), not throughout the entire cell, and therefore we have no true measure of cytoplasmic Myosin. However, we can plot non-membrane Myosin from this same apicobasal position in the cell. Non-membrane Myosin will include both the cytoplasmic signal and the Myosin II medial web (see above). When plotting these, we find that Myosin II intensities in this pool are similar in wildtype and twist (see graph below, dotted lines show standard deviations), confirming that that we are not inappropriately brightening one set of images compared to the other (e.g., twist versus wildtype).

Finally, our observations of rate of junction shrinkage and intercalation are consistent with our Myosin II quantification results (see Figures 4A, 4D and 6F). This further validates our methods.

• *

• *

- A previous study demonstrates that the accumulation of junctional myosin is substantially reduced in twist mutant embryos compared to the wild type (Gustafson et al., 2022). In that work, junctional myosin was quantified as (I_junction - I_cytoplasm)/I_cytoplasm. In contrast, the cytoplasmic myosin intensity does not appear to be subtracted from the quantification in this study. How much of the difference in the conclusions of the two studies can be explained by this difference in myosin quantification?

        As explained above, we choose to normalize our data by stretching histograms, rather than subtracting and dividing intensities between different pools of Myosin. The setting pixels of intensities up to 5 percentiles set to zero for each will have a similar effect to subtracting a small fraction of the cytoplasmic pool. We note that the intensity measurements in (Gustafson et al., 2022) are in the apical-top 5µm of the cell, and therefore their ‘cytoplasmic’ signal is likely to also include the apical medial web of Myosin. Also, after subtraction they use division by the cytoplasmic intensity in an attempt to bring pixel intensities between different movies into a comparable range, whereas we do this by stretching the histograms themselves (see above).  We carefully designed our method to preserve the increase in Myosin levels that we see over time in our post-normalization data. This is something that their method of normalization would not be predicted to capture, if their ‘cytoplasmic’ signal increase over time as well as their junctional signal.  Indeed, in FigS6D of their paper, Myosin II levels do not appear to increase over time in these (presumably normalized) images.

Additionally, we note that in (Gustafson et al., 2022), not all Myosin II is fluorescently tagged since they use a sqhGFP transgene located on the balancer chromosome. This means that the line they use will have a pool of exogeneous Myosin tagged with GFP (expressed from the CyO balancer) and a pool of endogenous Myosin (expressed from the sqh gene on the X chromosome. It is not known whether endogenous and exogeneous GFP-tagged Myosin II will be recruited equally to cell junctions when in competition with each other. Therefore, in their genetic background, the ratio of junctional/cytoplasmic sqhGFP might not reflect the true ratio. To avoid this potential caveat, in our study we have used a new knock-in of Myosin, which tags the sqh gene at the endogenous locus (Proag et al., 2019). The line is homozygous viable and thus all the molecules of Myosin II Regulatory Light Chain (encoded by sqh), and thus the Myosin II mini-filaments, are labelled with GFP.

Additionally, we note that when comparing their images of Myosin II in wildtype and twist (Figure 5D and D’), the overall Myosin signal appears reduced in twist mutants (including in the head and posterior midgut, which is outside the area that they are claiming Myosin II is recruited in response to mesoderm invagination). This suggests that Myosin II is generally reduced in their twist mutants (or images thereof), which is not expected and might indicate issues with their methods.

Therefore differences in the methods may explain the discrepancies between studies. Importantly, we have quantified junctional shrinkage rates and intercalation, and our analysis of these rates is consistent with our Myosin II quantification results (see above).

-The authors used the tissue flow data to register the myosin channel and the membrane channel, which were acquired at slightly different times. The accuracy of this channel registration should be demonstrated.

As stated in our methods: “the channel registration was corrected post-acquisition in order that information on the position of interfaces in the Gap43 channel could be used to locate them in the Myosin channel. Therefore the local flow of cell centroids between successive pairs of time frames in the Gap43 channel is used to give each interface/vertex pixel a predicted flow between frames. A fraction of this flow is applied, equal to the Myosin II to Gap43 channel time offset, divided by the frame interval. Because cells deform as well as flow, the focal cell’s cell shape strain rate is also applied, in the same fractional manner as above.”

The images in Figure 3C and C’ show the Myosin II, with quantified membrane Myosin superimposed on the image as a color-code. Images in Figure 3B and B’ show the (normalized) Myosin II. Comparison of these images demonstrates that the channel registration is accurate. We will add a reference to these images in the methods.

• The authors show that cell intercalation is not influenced in twist mutant embryos. However, a previous study demonstrates that the speed of GBE is substantially reduced in twist mutants (Gustafson et al., 2022). It would be interesting to see whether a similar reduction in the speed of GBE was observed in this study. *

We do not see a reduction in the speed of GBE as reported by (Gustafson et al., 2022), we will add “tissue strain rate” graphs to demonstrate this. On the contrary, we find a slight increase in the “tissue strain rate”, because there is a slight increase in the “cell shape strain rate” contributing to extension (while “cell intercalation strain rate” is unchanged). See also response to Reviewer 1 (major comment) .

• It has been previously shown that contractions of medioapical myosin in germband cells also contribute to cell intercalation. The authors should explain why medioapical myosin was not included in the comparison between wildtype and twist mutant embryos. *

• *

Indeed, it has been shown that there is a flow of medial Myosin towards the junctions (Rauzi et al., 2010). However, and as described in that paper, this flow ‘feeds’ the enrichment of Myosin II at shrinking junctions, and thus the junctional Myosin II can be taken as a readout of polarized Myosin II behavior. Additionally, medial flows are more technically challenging to quantify, especially when quantification is required in a large number of cells as is the case for our study.

Importantly, our junctional Myosin II and junctional shrinkage rate results are consistent with each other, therefore it is very unlikely that analyzing medial Myosin II would lead us to form a different conclusion. We will add a sentence to explain why we chose to quantify junctional, and not medial, Myosin II.

*Minor points: *

1. * Fig. 1-S1 panel C: the number of cyan cells changes non-monotonically. It first decreases from -10 min to 10 min, then increases from 10 min to 20 min. This is confusing since in theory the number of tracked cells should not increase over time if the cells are tracked from the beginning of the movie. *
2. *

The cyan cells highlight tracked mesodermal and mesectodermal cells, which are not included in the analysis. The low number of mesodermal cells highlighted at 10mins germband extension is because mesodermal and mesectodermal cells are not always tracked successfully at this time. Note that the legend includes a note that ‘”Unmarked cells are poorly tracked and excluded from the analysis”. Also see Methods: “Note on number of cells in movies, for notes on changes to the number of tracked ectodermal cells throughout the timecourse of the movies.”

• Fig. 1-S2: the vnd band in panel A appears to be much narrower than in panel B. *

• *

These are fixed embryos, therefore this could be (at least partially) due to slight differences in exact developmental age of the embryo. Note that we wanted to check that vnd and ind are expressed in the correct places in the ectoderm. We were motivated to check this because the width of mesoderm is reduced in twist, so we thought it was important to verify that there is not a population of ‘ectodermal’ cells with a strange fate (i.e., negative for both vnd and ind). Our experiments show that vnd abuts the mesoderm/mesectoderm in twist as in wildtype, and that the cells immediately lateral to the vnd cell population express ind as expected.

It is possible that there is a slight difference in the number of vnd cells in twist mutants compared to wildtype, but we see no differences in Myosin II bipolarity that would coincide with the vnd/ind boundary (Fig3-S1). Therefore, this would not change the interpretation of our results. Counting the number of rows of vnd cells prior to any cell intercalation (the number of rows will reduce as cells intercalate) would be technically challenging as the lateral border of vnd expression is hard to discern at this time due to lower levels of vnd expression laterally within the vnd expression domain.

• The schematic in Fig. 2J suggests that at the onset of mesoderm pulling the germband cells have a uniform angle of rotation (towards bottom right). Is this the case?*

• *

No, this schematic is purely supposed to show that as cells stretch, they also reorient. Note that we will review our schematics in Fig. 2 to increase clarity (see response to reviewer 1, first minor comment).

• The description of myosin intensity normalization in the Methods section is somewhat difficult to follow [Line 829 - 832]. It would be helpful if the authors can show one or two images before and after intensity normalization as examples. *

We will add some examples of before and after normalization images to this section. We will also review the Methods to improve the text’s clarity.

• Line 704: "Z-stacks for each channel were collected sequentially" - the step size in Z-axis should be reported. *

Thank you for this, the step size was 1µm. We will add this information.

• Fig. 4C: what are the thin, black lines in the image? *

This image is a 2D representation of the Gap43Cherry signal at the level of the adherens junctions extracted for tracking, not a simple confocal z-slice. When viewing these representations, you can see lines showing borders between where information from different z-stacks was used for the tracking layer. Unfortunately, our software does not allow us to remove these lines, but they do not affect tracking, quantification etc.

Reviewer #3 (Significance (Required)):

While most previous work on tissue mechanics and morphogenesis focuses on tissue-intrinsic mechanical input, recent studies have started to emphasize the contribution of tissue-extrinsic forces. An important challenge in understanding the function of tissue-extrinsic forces lies in the difficulties in properly comparing the wild type and the mutant samples that disrupt extrinsic forces, in particular when cell fate specification is altered in the mutants. In this work, the authors addressed this challenge by employing a number of approaches to warrant a parallel comparison between genotypes, including examining the AP- and DV-patterning of the tissue, selecting sample regions with comparable cell fate for analysis, and carefully aligning the stage of the movies. With these approaches, the authors provide compelling evidence to support their main conclusions. By teasing apart the role of the intrinsic genetic program and the extrinsic tissue forces, the work provides important clarifications on the function of mesoderm pulling in GBE and adds new insights into this well-studied tissue morphogenetic process. This work should be of interest to the broad audience of epithelial morphogenesis, tissue mechanics and myosin mechanobiology.

• *

Review____er #4 (Evidence, reproducibility and clarity (Required)):

*Lye and colleagues investigate the impact of tissue-tissue interactions on morphogenesis. Specifically, they ask how disrupting mesoderm internalization affects convergence and extension of the ectoderm (germband) in Drosophila embryos. Using twi mutants in which mesoderm invagination fails, the authors find that the invagination of the mesoderm deforms germband cells, but does not significantly contribute to patterning, cell alignment, myosin polarization and cell-cell contact disassembly (which drive germband convergence). The authors find modest effects of mesoderm invagination on new junction formation and orientation (which drive extension), but these changes do not have a significant effect on germband elongation. The authors conclude that germband extension is robust to external forces from the invagination of the mesoderm. *

*MAIN 1. The authors clearly show that myosin density is not different in wild-type and twi mutant embryos, and subsequently argue that the pulling force from the mesoderm does not elicit a mechanosensitive response in early germband extension. But if the cell density is constant, doesn't that mean that the longer, DV-oriented interfaces in the wild type accumulate more total myosin than their shorter counterparts in twi mutants? Assuming that the total number of myosin molecules per cell is not greater in the wild type, wouldn't increased total myosin at the membrane suggest a response to the increased deformation? Certainly the cells are able to maintain the same cell density despite the pulling force from the mesoderm, so can the authors rule out a mechanosensing mechanism? *

• *

We do not rule out a mechanosensing mechanism. We agree the total Myosin at stretched interfaces is higher than at unstretched interfaces and proposed a homeostatic mechanism to maintain Myosin II density on the cortex upon rapid stretching (summarized in Fig. 7). Indeed it is possible that this mechanism could itself be due to mechanosensitive recruitment of Myosin II (though there are also other possibilities). We have tried to address this in our discussion (under “Mechanisms regulating Myosin II density at the cortex and consequences for cell intercalation” and “Restoration of DV cell length after being stretched by mesoderm invagination”), but we will amend the wording the make the possibility of mechanosensitive recruitment of Myosin II to maintain cortical density more explicit.

*What happens to the Gap43mCherry signal? From Figure 2A, it seem to be diluted ventrally in the wild type as compared to twi mutants? Comparing myosin and Gap43 dynamics may shed light on whether myosin accumulates more or less than one would expect simply on the basis of having longer contacts. *

We quantify the density of Myosin, rather than the total amount. Therefore, the length of the contact should not matter. The suggestion of comparing Myosin density to Gap43Cherry density is in principle a good one, as it would allow us to compare a protein which is not diluted as cell contact length increases (Myosin) to one which appears to be (Gap43). However, it is not essential for the conclusions that we make. However, in practice quantifying the Gap43Cherry signal would not be straightforward on our existing movies due to the imaging parameters used. We capture the Gap43Cherry channel (but not the Myosin channel) with a ‘spot noise reducer’ tuned on in the camera software, due to very occasional bright spot noise, which confuses the tracking software. Therefore, our Gap43Cherry signal is manipulated during acquisition and to quantify from these images would not be appropriate. Therefore, we would have to acquire, track and quantify some new movies, which is not possible within the timeframe of a revision.

In summary, we think that we have sufficient evidence from our analysis that Myosin II is not diluted upon junctional stretching without comparing to quantification of Gap43Cherry, and the time investment required to quantify the Gap43Cherry would not be worthwhile as it would require more data to be acquired and processed.

• The authors previously argued that mesoderm invagination was required for the fast phase of cell intercalation [Butler et al., 2009]. However, here the authors interpret that loss of twi does not significantly slow down interface contraction, but accelerates the elongation of junctions and cells along the AP axis, which overall would mean that mesoderm invagination is (slightly) detrimental for axis elongation. The discrepancy between their previous and current results should be discussed. *

We are happy to add more information about these discrepancies in the discussion. In a nutshell, we think that these discrepancies arise from the challenges of comparing wildtype and twist mutant embryos relative to each other, and as a consequence we have made various improvements to our methods since (Butler et al., 2009). These improvements included using markers that would be expressed at the same levels in wildtype and twist embryos. Additionally, we did not use overexpressed cadherin-FPs (namely, the ubi-CadGFP transgene), which may have confounding effects, and we used a knock-in sqhGFP to ensure we could all Myosin II molecules were labelled by GFP. We also carefully controlled the temperature at which we acquired the movies, standardized the level at which to track cells and quantify Myosin between movies, as well as improving the accuracy of our image segmentation and cell type identification since our previous study (Butler et al., 2009). See also response to reviewer 2.

• Related to the previous point, it is surprising that the differences shown in Figure 4A-B are not significant. This is particularly troubling when in Figure 5B the authors claim a significant difference in cell elongation rate, which is higher in twi mutants (but only in very short time intervals and actually switches sign at the end of germband extension). These are just two examples, but I think the analysis of significance on a per-time point basis is problematic. *

*Have the authors considered analyzing their results as time series rather than comparing individual time points? Or perhaps integrating the different metrics over the duration of germband extension (e.g. using areas under the curve)? That way they would not have to arbitrarily decide if significant differences in a few time points should or not be interpreted as significant overall differences. *

• *

For graphs plotted against time of germband extension, we do not think it is appropriate to analyze as a time series rather than comparing individual time points, since different developmental events (such as mesoderm invagination) occur at different times. For graphs plotted against time to/from cell neighbor swap, these can also change over time (e.g., ctrd-ctrd orientation, Fig6D). Therefore we do not feel that it appropriate to run statistical analyses as a timeseries for these comparisons either. Statistically cut-offs are by their nature arbitrary. We have tried to highlight non-significant trends throughout the text (including for Fig4A&B), in addition to stating where we see significant differences to highlight where there may be minor (but not significant) differences.

---

• While the number of cells analyzed is impressive, the number of embryos is relatively low, particularly for the wild type (only four embryos analyzed). If I understood correctly (if not, please clarify) the authors ran their statistics using cells and not embryos as their measurement unit. But I could not find any evidence that cells from the same embryo can be considered as independent measurements. This could be easily done by demonstrating that the variance of any of the measurements (e.g. elongation, area change rate, etc.) for cells in an embryo is comparable to that calculated when mixing cells from different embryos. *

• *

We do not simply use the number of cells as an n for our experiments. We use a mixed effects model for our statistics as previously (Butler et al., 2009; Finegan et al., 2019; Lye et al., 2015; Sharrock et al., 2022; Tetley et al., 2016). This estimates the P value associated with a fixed effect of differences between genotypes, allowing for random effects contributed by differences between embryos within a given genotype. We will make sure that this is clear in the Methods.

MINOR 1. Figure 4D: the authors show no difference in the proportion of neighbor swaps per minute between wild-type and twi- mutant embryos. But how about the absolute number of neighbour swaps per minute? Does that change in twi mutants (and if so, why?).

The number of interfaces involved in a T1 swap are expressed as a proportion of the total number of DV-oriented interfaces for all tracked ectodermal germband cells, to take account of differences in the number of tracked cells between different timepoints and different movies. Presenting the absolute number of swaps per minute could lead to misleading interpretations.

• I was a bit confused about the reason why in Figure 4A the authors measure the rate of interface contraction in units of “proportion/min”, but in Figure 5A they measure interface elongation in units of “um/min”. Unless there is a good reason not to, these two metrics should be reported using the same units. Is there a difference in the rate of interface contraction when measured in absolute units (um/min)? *

Thank you, we will amend so that both measures are expressed in the same units.

• The discussion of previous work on cell deformation within the mesoderm (page 16, first paragraph) should probably include recent work from Adam Martin's lab (e.g. [Heer et al., 2017]; or [Denk-Lobnig et al., 2021]). *

Thank you, and apologies for this oversight, we will add these references__.__

SUGGESTIONS 1. While I appreciate the arguments that the authors provide to use twi mutants rather than sna mutants or twi sna double mutants, as the authors indicate, in twi mutants there is still contractility in the mesoderm (albeit not ratcheted). Therefore, it is possible that contractile pulses from the mesoderm in twi mutants could still facilitate cell alignment and polarization of myosin in the germband. Given the previous results from the Zallen lab using twi sna double mutants (see above) this is unlikely to be the case, but the findings in this manuscript would be significantly stronger if they included similar analysis in the double mutants.

We had concerns about using sna or twi sna double mutants due to the large amount of space the un-internalized mesoderm takes up on the exterior of the embryo. This concern is also shared by reviewer 1 “Importantly, I think the researchers were correct in choosing to analyze twist single-mutant embryos (as opposed to snail or twist, snail double-mutant embryos), as the overall embryo geometry of these mutants is fairly similar to wild-type embryos, allowing the researchers to directly compare cell behaviors and myosin dynamics during germband extension. This approach also allows them to avoid indirect effects on the germband due to a completely non-internalized mesoderm.” * In addition to this concern, imaging of snail or twist snail* embryos by confocal imaging to include the ventral midline (which is required to define embryonic axes) is problematic as the un-constricted mesodermal cells occupy virtually all the field of view, leaving very few ectodermal cells to analyze.

Whilst we acknowledge that there are some (un-ratcheted) contractions of mesodermal cells in twist mutants, we have clearly shown that there is no DV stretch and very little reorientation of cells. Therefore, any residual contractile activity in the mesodermal cells of twist mutants does not appear to have a mechanical impact on the ectoderm. We cannot exclude the possibility that there is some transmission of forces between contracting cells of the mesoderm and the ectoderm in twist mutants. However, our evidence suggests that the large tissue scale force that transmits to the ectoderm from the invaginating mesoderm is missing in twist mutants, and it was the effects of that force that we wished to investigate (See also response to reviewer 2).

Review*er #4 (Significance (Required)): *

*This is an interesting study, with careful quantitative analysis of cellular and subcellular dynamics. The results follow previous findings from Jennifer Zallen and the authors themselves. The Zallen lab showed that cell alignment, myosin polarization and germband extension are normal in sna twi mutants [Fernandez-Gonzalez et al., 2009], a result that the authors fail to cite. The results in the present manuscript are similar, but the analysis is much more in depth here, so the findings by Lye and colleagues certainly warrant publication. *

We did not specifically cite this result from (Fernandez-Gonzalez et al., 2009), because the subject of their study is the formation of multicellular rosettes, not whether a pull from mesoderm affects Myosin II polarity and cell intercalation. The formation of multicellular rosettes occurs later in germband extension, and therefore these results are not directly relevant to our study. Additionally, their measures of alignment are defined as linkage to other approximately DV oriented interfaces, rather than directly measuring orientation compared to the embryonic axes as we do here, as a different question is being addressed. Specifically, the quoted sna twi experiment is interpreted as extrinsic forces from the mesoderm not being required for linkage of Myosin enriched DV-oriented interfaces together. Myosin II quantification is more rudimentary with edges being assigned as Myosin positive or Myosin negative, as opposed to quantifying the density of Myosin on each interface and we cannot see any comparison of Myosin II quantification between wildtype and twist embryos.­

So, although the results are consistent with each other, they are not directly comparable due to methods used and we are happy that the reviewer acknowledges that our analysis is more in depth, which was necessary to address the specific questions that we investigate in our study.

        In general, there have been inconsistencies in results between previous studies, leading reviewer one to recognize that *“…it should be published and that it will be an impactful paper within the field. Namely, it will settle once and for all the question of whether mesoderm invagination is required for optimal germband extension in the early Drosophila embryo.”  *The high amount of conflicting information in the literature led us to not exhaustively describe individual findings, but we will ensure the results from the Zallen lab are appropriately cited.

However, there are a number of experimental points that I think need to be addressed to solidify the manuscript, particularly in terms of statistical analysis.

Please see more details above (main points 3 and 4) regarding specific concerns about experimental points and statistics. Additionally, we note that reviewer 3 states “statistics were appropriately used”, and our statistical methods are the same as we have used in previous studies comparing live imaging data (Butler et al., 2009; Finegan et al., 2019; Lye et al., 2015; Sharrock et al., 2022; Tetley et al., 2016).

• *

__REFERENCES

__

Blanchard, G. B., Kabla, A. J., Schultz, N. L., Butler, L. C., Sanson, B., Gorfinkiel, N., Mahadevan, L. and Adams, R. J. (2009). Tissue tectonics: morphogenetic strain rates, cell shape change and intercalation. Nat Methods 6, 458-464.

Butler, L. C., Blanchard, G. B., Kabla, A. J., Lawrence, N. J., Welchman, D. P., Mahadevan, L., Adams, R. J. and Sanson, B. (2009). Cell shape changes indicate a role for extrinsic tensile forces in Drosophila germ-band extension. Nat Cell Biol 11, 859-864.

Farrell, D. L., Weitz, O., Magnasco, M. O. and Zallen, J. A. (2017). SEGGA: a toolset for rapid automated analysis of epithelial cell polarity and dynamics. Development 144, 1725-1734.

Fernandez-Gonzalez, R., Simoes Sde, M., Roper, J. C., Eaton, S. and Zallen, J. A. (2009). Myosin II dynamics are regulated by tension in intercalating cells. Dev Cell 17, 736-743.

Finegan, T. M., Hervieux, N., Nestor-Bergmann, A., Fletcher, A. G., Blanchard, G. B. and Sanson, B. (2019). The tricellular vertex-specific adhesion molecule Sidekick facilitates polarised cell intercalation during Drosophila axis extension. PLoS Biol 17, e3000522.

Gustafson, H. J., Claussen, N., De Renzis, S. and Streichan, S. J. (2022). Patterned mechanical feedback establishes a global myosin gradient. Nat Commun 13, 7050.

Irvine, K. D. and Wieschaus, E. (1994). Cell intercalation during Drosophila germband extension and its regulation by pair-rule segmentation genes. Development 120, 827-841.

Leptin, M. and Grunewald, B. (1990). Cell shape changes during gastrulation in Drosophila. Development 110, 73-84.

Lye, C. M., Blanchard, G. B., Naylor, H. W., Muresan, L., Huisken, J., Adams, R. J. and Sanson, B. (2015). Mechanical Coupling between Endoderm Invagination and Axis Extension in Drosophila. PLoS Biol 13, e1002292.

Proag, A., Monier, B. and Suzanne, M. (2019). Physical and functional cell-matrix uncoupling in a developing tissue under tension. Development 146.

Rauzi, M., Lenne, P. F. and Lecuit, T. (2010). Planar polarized actomyosin contractile flows control epithelial junction remodelling. Nature 468, 1110-1114.

Sharrock, T. E., Evans, J., Blanchard, G. B. and Sanson, B. (2022). Different temporal requirements for tartan and wingless in the formation of contractile interfaces at compartmental boundaries. Development 149.

Simpson, P. (1983). Maternal-Zygotic Gene Interactions during Formation of the Dorsoventral Pattern in Drosophila Embryos. Genetics 105, 615-632.

Tetley, R. J., Blanchard, G. B., Fletcher, A. G., Adams, R. J. and Sanson, B. (2016). Unipolar distributions of junctional Myosin II identify cell stripe boundaries that drive cell intercalation throughout Drosophila axis extension. Elife 5.

Wang, X., Merkel, M., Sutter, L. B., Erdemci-Tandogan, G., Manning, M. L. and Kasza, K. E. (2020). Anisotropy links cell shapes to tissue flow during convergent extension. Proc Natl Acad Sci U S A 117, 13541-13551.

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Referee #4

Evidence, reproducibility and clarity

Lye and colleagues investigate the impact of tissue-tissue interactions on morphogenesis. Specifically, they ask how disrupting mesoderm internalization affects convergence and extension of the ectoderm (germband) in Drosophila embryos. Using twi mutants in which mesoderm invagination fails, the authors find that the invagination of the mesoderm deforms germband cells, but does not significantly contribute to patterning, cell alignment, myosin polarization and cell-cell contact disassembly (which drive germband convergence). The authors find modest effects of mesoderm invagination on new junction formation and orientation (which drive extension), but these changes do not have a significant effect on germband elongation. The authors conclude that germband extension is robust to external forces from the invagination of the mesoderm.

Main

1. The authors clearly show that myosin density is not different in wild-type and twi mutant embryos, and subsequently argue that the pulling force from the mesoderm does not elicit a mechanosensitive response in early germband extension. But if the cell density is constant, doesn't that mean that the longer, DV-oriented interfaces in the wild type accumulate more total myosin than their shorter counterparts in twi mutants? Assuming that the total number of myosin molecules per cell is not greater in the wild type, wouldn't increased total myosin at the membrane suggest a response to the increased deformation? Certainly the cells are able to maintain the same cell density despite the pulling force from the mesoderm, so can the authors rule out a mechanosensing mechanism? What happens to the Gap43mCherry signal? From Figure 2A, it seem to be diluted ventrally in the wild type as compared to twi mutants? Comparing myosin and Gap43 dynamics may shed light on whether myosin accumulates more or less than one would expect simply on the basis of having longer contacts.
2. The authors previously argued that mesoderm invagination was required for the fast phase of cell intercalation [Butler et al., 2009]. However, here the authors interpret that loss of twi does not significantly slow down interface contraction, but accelerates the elongation of junctions and cells along the AP axis, which overall would mean that mesoderm invagination is (slightly) detrimental for axis elongation. The discrepancy between their previous and current results should be discussed.
3. Related to the previous point, it is surprising that the differences shown in Figure 4A-B are not significant. This is particularly troubling when in Figure 5B the authors claim a significant difference in cell elongation rate, which is higher in twi mutants (but only in very short time intervals and actually switches sign at the end of germband extension). These are just two examples, but I think the analysis of significance on a per-time point basis is problematic. Have the authors considered analyzing their results as time series rather than comparing individual time points? Or perhaps integrating the different metrics over the duration of germband extension (e.g. using areas under the curve)? That way they would not have to arbitrarily decide if significant differences in a few time points should or not be interpreted as significant overall differences.
4. While the number of cells analyzed is impressive, the number of embryos is relatively low, particularly for the wild type (only four embryos analyzed). If I understood correctly (if not, please clarify) the authors ran their statistics using cells and not embryos as their measurement unit. But I could not find any evidence that cells from the same embryo can be considered as independent measurements. This could be easily done by demonstrating that the variance of any of the measurements (e.g. elongation, area change rate, etc.) for cells in an embryo is comparable to that calculated when mixing cells from different embryos.

Minor

1. Figure 4D: the authors show no difference in the proportion of neighbor swaps per minute between wild-type and twi-mutant embryos. But how about the absolute number of neighbour swaps per minute? Does that change in twi mutants (and if so, why?).
2. I was a bit confused about the reason why in Figure 4A the authors measure the rate of interface contraction in units of "proportion/min", but in Figure 5A they measure interface elongation in units of "um/min". Unless there is a good reason not to, these two metrics should be reported using the same units. Is there a difference in the rate of interface contraction when measured in absolute units (um/min)?
3. The discussion of previous work on cell deformation within the mesoderm (page 16, first paragraph) should probably include recent work from Adam Martin's lab (e.g. [Heer et al., 2017]; or [Denk-Lobnig et al., 2021]).

Suggestions

1. While I appreciate the arguments that the authors provide to use twi mutants rather than sna mutants or twi sna double mutants, as the authors indicate, in twi mutants there is still contractility in the mesoderm (albeit not ratcheted). Therefore, it is possible that contractile pulses from the mesoderm in twi mutants could still facilitate cell alignment and polarization of myosin in the germband. Given the previous results from the Zallen lab using twi sna double mutants (see above) this is unlikely to be the case, but the findings in this manuscript would be significantly stronger if they included similar analysis in the double mutants.

Significance

This is an interesting study, with careful quantitative analysis of cellular and subcellular dynamics. The results follow previous findings from Jennifer Zallen and the authors themselves. The Zallen lab showed that cell alignment, myosin polarization and germband extension are normal in sna twi mutants [Fernandez-Gonzalez et al., 2009], a result that the authors fail to cite. The results in the present manuscript are similar, but the analysis is much more in depth here, so the findings by Lye and colleagues certainly warrant publication. However, there are a number of experimental points that I think need to be addressed to solidify the manuscript, particularly in terms of statistical analysis.

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Referee #3

Evidence, reproducibility and clarity

During morphogenesis, the final shape of the tissue is not only dictated by mechanical forces generated within the tissue but can also be impacted by mechanical contributions from surrounding tissues. The way and extent to which tissue deformation is influenced by tissue-extrinsic forces are not well understood. In this work, Lye et al. investigated the potential influence of Drosophila mesoderm invagination on germband extension (GBE), an epithelial convergent extension process occurring during gastrulation. Drosophila GBE is genetically controlled by the AP patterning system, which determines planar polarized enrichment of non-muscle myosin II along the DV-oriented adherens junctions. Myosin contractions drive shrinking of DV-oriented junctions into 4-way vertices, followed by formation of new, AP-oriented junctions. This process results in cell intercalation, which causes tissue convergence along the DV-axis and extension along the AP-axis. In addition, GBE is facilitated by tissue-extrinsic pulling forces produced by invagination of the posterior endoderm. Interestingly, some recent studies suggest that the invagination of the mesoderm, which occurs immediately prior to GBE, also facilitates GBE. In the proposed mechanism, invaginating mesoderm pulls on the germband tissue along the DV-axis; the resulting strain of the germband cells generates a mechanotransduction effect that promotes myosin II recruitment to the DV-oriented junctions, thereby facilitating cell intercalation. Here, the authors revisited this proposed mechanotransduction effect using quantitative live imaging approaches. By comparing the wildtype embryos with twist mutants that fail to undergo mesoderm invagination, the authors show that although the DV-oriented strain of the germband cells was greatly reduced in the absence of mesoderm pulling, this defect had a negligible impact on junctional myosin density, myosin planar polarity, the rate of junction shrinkage or the rate of cell intercalation during GBE. A mild increase in the rate of new junction extension and a slight defect in cell orientation were observed in twist mutants, but these differences did not cause obvious defects in cell intercalation. The authors conclude that myosin II-mediated cell intercalation during GBE is robust to the extrinsic mechanical forces generated by mesoderm pulling.

Overall, I found that the results described here are very interesting and of high quality. The data acquisition and analyses were elegantly performed, statistics were appropriately used, and the manuscript was clearly written. However, there are a few points where some further explanation or clarification is necessary, as detailed below:

1. The main conclusion of the manuscript relies on appropriate quantification of myosin intensity at cell junctions. It is therefore important that the methods of quantification are well justified. Below are a few questions regarding the methods used in the analyses:
   • For myosin quantification, the authors state that "Background signal was subtracted by setting pixels of intensities up to 5 percentile set to zero for each timepoint" [Line826]. The rationale for selecting 5 percentile as the threshold for background should be explained. Also, how does this background value change over time?
   • The authors mention that "Intensities varied slightly between experiments due to differences in laser intensity and therefore histograms of pixel intensities were stretched" [Line828]. The method of intensity justification should be justified. For example, does this normalization result in similar cytoplasmic myosin intensity between control and twist mutant embryos?
   • A previous study demonstrates that the accumulation of junctional myosin is substantially reduced in twist mutant embryos compared to the wild type (Gustafson et al., 2022). In that work, junctional myosin was quantified as (I_junction - I_cytoplasm)/I_cytoplasm. In contrast, the cytoplasmic myosin intensity does not appear to be subtracted from the quantification in this study. How much of the difference in the conclusions of the two studies can be explained by this difference in myosin quantification?
   • The authors used the tissue flow data to register the myosin channel and the membrane channel, which were acquired at slightly different times. The accuracy of this channel registration should be demonstrated.
2. The authors show that cell intercalation is not influenced in twist mutant embryos. However, a previous study demonstrates that the speed of GBE is substantially reduced in twist mutants (Gustafson et al., 2022). It would be interesting to see whether a similar reduction in the speed of GBE was observed in this study.
3. It has been previously shown that contractions of medioapical myosin in germband cells also contribute to cell intercalation. The authors should explain why medioapical myosin was not included in the comparison between wildtype and twist mutant embryos.

Minor points:

1. Fig. 1-S1 panel C: the number of cyan cells changes non-monotonically. It first decreases from -10 min to 10 min, then increases from 10 min to 20 min. This is confusing since in theory the number of tracked cells should not increase over time if the cells are tracked from the beginning of the movie.
2. Fig. 1-S2: the vnd band in panel A appears to be much narrower than in panel B.
3. The schematic in Fig. 2J suggests that at the onset of mesoderm pulling the germband cells have a uniform angle of rotation (towards bottom right). Is this the case?
4. The description of myosin intensity normalization in the Methods section is somewhat difficult to follow [Line 829 - 832]. It would be helpful if the authors can show one or two images before and after intensity normalization as examples.
5. Line 704: "Z-stacks for each channel were collected sequentially" - the step size in Z-axis should be reported.
6. Fig. 4C: what are the thin, black lines in the image?

Significance

While most previous work on tissue mechanics and morphogenesis focuses on tissue-intrinsic mechanical input, recent studies have started to emphasize the contribution of tissue-extrinsic forces. An important challenge in understanding the function of tissue-extrinsic forces lies in the difficulties in properly comparing the wild type and the mutant samples that disrupt extrinsic forces, in particular when cell fate specification is altered in the mutants. In this work, the authors addressed this challenge by employing a number of approaches to warrant a parallel comparison between genotypes, including examining the AP- and DV-patterning of the tissue, selecting sample regions with comparable cell fate for analysis, and carefully aligning the stage of the movies. With these approaches, the authors provide compelling evidence to support their main conclusions. By teasing apart the role of the intrinsic genetic program and the extrinsic tissue forces, the work provides important clarifications on the function of mesoderm pulling in GBE and adds new insights into this well-studied tissue morphogenetic process. This work should be of interest to the broad audience of epithelial morphogenesis, tissue mechanics and myosin mechanobiology.

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Referee #2

Evidence, reproducibility and clarity

In the present manuscript, Lye et al. describe a highly detailed quantification of cell shape changes during germband extension in Drosophila melanogaster early embryo. During this process, ectodermal tissue contracts along the dorso-ventral axis, simultaneously expanding along the perpendicular antero-posterior direction, migrating from the ventral to the dorsal surface of the embryo as it extends. This important morphogenetic event is preceded by ventral furrow formation when mesodermal tissue (located in the ventral part of the embryo) contracts along the dorso-ventral axis and invaginates into the embryonic interior. The study compares cell shape dynamics in the wildtype Drosophila with that in the twist mutant, which largely lacks mesoderm and does not form ventral furrow. The major motivation of the study is to examine whether cellular behaviors and myosin recruitment in the ectoderm is cell autonomous, or if those cellular behaviors depend on mechanical interactions between mesoderm and ectoderm. The authors first examine whether transcriptional patterning of key genes involved in germband extension is different between the wildtype and the twist mutant and find no significant difference. Next, the authors thoroughly quantify cellular behaviors and patterns of myosin recruitment in the two genetic backgrounds. A number of different measures are investigated, notably the rate of change in the degree of cellular asymmetry, rate of cell area change, rate of change of cell orientation, differences in myosin recruitment to cell edges of various orientation, as well as the rates of growth, shrinkage, and re-orientation of the various cellular interfaces. It is thoroughly documented how these quantities change as a function of developmental timing and spatial position within the embryo. These data serve basis for quantitative comparison between cellular dynamics in the two genetic backgrounds considered. Overall, the study shows that cellular behaviors observed in the ectoderm are largely the same during the period of time following ventral furrow formation, as would be expected if those cellular behaviors were predominantly cell autonomous and not dependent on stresses generated in the mesoderm.

The data presented in the manuscript are of excellent quality and presentation is very clear.

Minor comments: none

Significance

I find that the study provides a thorough quantification of cell behaviors in a widely studied important model of morphogenesis. The work may be of particular interest for future model-to-data comparison, perhaps providing a basis for future modeling work. I therefore certainly think that this work warrants publication. However, the results of the study largely parallel previous findings and do not appear novel or surprising. It is well established that in snail mutant that lack mesoderm entirely, germband extension proceeds largely normally. This well-established fact suggests that since tissue dynamics in complete absence of mesoderm are largely unaffected, behaviors of individual cells are likely to not be affected either. The work is pretty much entirely observational, and for most part provides a more detailed documentation/quantification of previous findings. I do not think it is appropriate for high profile publication.

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Referee #1

Evidence, reproducibility and clarity

Summary: In this manuscript by the Sanson group, Lye and colleagues try to definitively answer the question of whether pulling forces from the ventral mesoderm have significant effects on convergent extension in the Drosophila germband (germband extension). While germband extension does occur in mutant embryos lacking mesoderm invagination, it has long been an open question in the field as to whether ventral pulling forces from the mesoderm have significant effects (positive or negative) on cell intercalation during germband extension. To definitely address this question, Lye and colleagues generated high-quality, directly comparable datasets from wild-type and twist mutant embryos, and then systematically assessed nearly all aspects of cell intercalation, myosin recruitment, and tissue elongation over time. They demonstrate that pulling forces from the ventral mesoderm have negligible impacts on the course of germband extension. While there are indeed some interesting differences between wild-type and twist embryos with respect to cell intercalation and myosin recruitment, such differences are relatively minor. They conclude that the events of germband extension neither require nor are strongly affected by external forces from the mesoderm. While this is largely a negative results paper, I believe that it should be published and that it will be an impactful paper within the field. Namely, it will settle once and for all the question of whether mesoderm invagination is required for optimal germband extension in the early Drosophila embryo, and it suggests that tissues are largely autonomous developmental units that are buffered from outside mechanical inputs.

Major comments:

It seems to me that the one obvious omission from this paper is a general measure of convergent extension over time. I think it would be useful to the reader to include some measure of change in tissue aspect ratio over time between wild-type and twist embryos. This could be included in Figure 5 or 6.

Otherwise, I have no major comments on the experimental approach or the findings of this manuscript. It seems to me a straightforward and systematic approach for determining whether mesoderm invagination affects germband extension. I do have several minor comments that should be addressed prior to publication (below).

Minor comments:

I understand why cells would initially stretch more along the DV axis in wild-type embryos compared with twist embryos, but why do cells become so much more stretched along the AP axis (and become smaller apically) after 10 minutes of GBE in wild type compared with twist (Figure 2C and E). I think this is an interesting and non-intuitive result that would warrant a bit of explanation/conjecture.

I don't understand how you are defining cell orientation in Figure 2G. How are you choosing the cell axis that you are then comparing with the body axis? Is it the long axis, or something more complicated than that? I think you should briefly provide this information in the results section. If it is included in the methods, I wasn't able to locate it.

Figure 2: Since you have the space, it might help the reader if you simply wrote out "strain rate" for panels B, D, and F, rather that used the abbreviation "SR."

Please ensure that all axis labels are fully visible in the final figures. In several figures, the Y-axis labels were cut off (e.g., Fig 2I, 4A, 4D, 6B, 6C).

Where space permits, I would suggest using fewer abbreviations in axis labels to increase readability of the figures (e.g., in Figures 3H or 4D).

In Figure 7, I would move the wild-type panels to the left and the twist panels to the right. I think it is more conventional to describe the normal wild-type scenarios first, and then contrast the mutant state.

To be consistent with the literature, "wildtype" should be hyphenated (wild-type) when used as an adjective, or two separate words (wild type) when used as a noun.

Significance

Advance: The advances in this manuscript are largely methodological, but the experiments and analyses are quite rigorous and allow the authors to make strong conclusions concerning their hypotheses. Their findings are based on a high-quality collection of movies from control and twist mutant embryos expressing a cell membrane marker and knock-in GFP-tagged myosin. Importantly, I think the researchers were correct in choosing to analyze twist single-mutant embryos (as opposed to snail or twist, snail double-mutant embryos), as the overall embryo geometry of these mutants is fairly similar to wild-type embryos, allowing the researchers to directly compare cell behaviors and myosin dynamics during germband extension. This approach also allows them to avoid indirect effects on the germband due to a completely non-internalized mesoderm.

Audience: The primary audience for this article will be basic science researchers working in the early Drosophila embryo who are interested in the interplay between the germband and neighboring tissues. Secondary audiences will include developmental biologists more broadly who are interested in biomechanical coupling (or in this case decoupling) of neighboring tissues.

Describe your expertise: I have been a Drosophila developmental geneticist for over twenty years, and I have been working directly on Drosophila germband extension for over a decade. I have published numerous papers and reviews in this field, and I am very familiar with the genetic backgrounds and types of experimental analyses used in this manuscript. Therefore, I believe I am highly qualified to serve as a reviewer for this manuscript.

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Reply to the reviewers

1. General Statements

We thank the editors for sending our manuscript for peer review and the reviewers for careful reading and their critical comments to improve the manuscript. Below, we describe the experiments that have been carried out in response to the reviewers and incorporated in the preliminary revision. We also describe our plan for the revisions that will address the remaining comments of the reviewers. Most of the comments are addressable with additional experiments (some of which are already ongoing) and these experiments will surely strengthen the study reported in this manuscript without affecting the fundamental findings. We would require up to 4-6 weeks to complete these experiments.

2. Description of the planned revisions

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

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

­Summary: The authors used a conditional transgenic mouse model to demonstrate that deletion of serum response factor (SRF) from adult astrocytes provides neuroprotection in various insult/ diseases contexts without promoting any obvious phenotypic deficiencies. The work builds on the group’s previous study where SRF was embryonically deleted from astrocytes and their precursor cells. Given the role of SRF in promoting glial cell differentiation, the adult conditional KO used in the current study was designed to circumvent the limitations of the previous approach. The authors used a variety of complementary approaches (including immunohistochemistry, electrophysiology, transcriptomics, and behavior) to demonstrate the therapeutic potential of their approach. However, I have questions regarding the validity of the behavioral analyses as well as some of the imaging results that dampen my overall enthusiasm.

Major Comment #1

The synaptogenic factors probed in Figure 3C (e.g. glypicans, thrombospondins, etc.) are not likely to play major roles in the adult brain in a non-injury context, so I do not know that these analyses provide any significant insight into potential functional changes in the mutant mice. Along the same lines, the analysis of synapse count (Figure 3D-E) seems inconsequential given that SRF was knocked out well after the period of developmental synaptogenesis. It would have been much more interesting to have performed these analyses following insult (such as the kainate injury model used by the authors) or in one of the disease models presented later in the manuscript. As it stands, I don't think they add very much to the study.

Response: We are grateful to the reviewer for the careful reading of the manuscript. Astrocytes are known to regulate the formation, maintenance, and elimination of synapses. It has been previously shown that LPS-induced reactive astrocytes exhibit reduced expression of several synaptogenic factors, were unable to promote synapse formation and showed reduced phagocytic activity (PMID: 28099414). We wanted to determine whether the SRF-deficient reactive-like astrocytes were likely compromised in their ability to produce pro-synaptogenic factors and/or adversely affect synapse maintenance. We agree with the reviewer that analysis of synapses in the adult brain may not address the role of these mutant astrocytes in synaptogenesis. But our results indicate that the mutant astrocytes are likely not affecting synapse maintenance or exhibit altered phagocytotic activity that would result in increased or decreased synapse numbers. We will make this clearer in the revised manuscript.

Minor Comment #2:

The authors should note that the use of GluA1 as a postsynaptic marker will not identify silent synapses (i.e. structurally "normal" but functionally inert).

Response: We agree with the reviewer that GluA1 will not identify silent synapses. To study silent vs functional synapses, we will stain for Piccolo (presynaptic) and NMDA receptor NR1 subunit (post-synaptic) to label all synapses and compare this with Piccolo/GluA1 co-localized synapses to identify the functional synapses.

Reviewer #2 (Significance (Required):

The manuscript addresses the important area of the cellular mechanisms that underlie neuroprotection. The ms adds to our understanding of genetic control of neuroprotection and should be of significant interest to others in the field. The experimental approach systematic and the data presented are generally of high quality and believable. While the ms presents quite a bit of overall cellular data that underlies various areas of neuronal and brain function that may be affected by loss of SRF, it is still somewhat descriptive. It is unclear what aspect of astrocyte reactivity is determinative, how mechanistically in normal cells SRF suppresses reactivity, and how SRF -negative reactive astrocytes confer such broad neuroprotection. While the latter is well beyond the scope of this study, the authors do propose SRF may be involved in regulating oxidative stress and amyloid plaque clearance as a potential pathway to account for SRF's role, however a more systematic discussion based on the gene expression data and known pathways would be welcome. Overall, this is a high quality ms that should be of interest to the field that identifies a SRF as a novel player in neuroprotection.

Response: We thank the reviewer for the careful reading of the manuscript and for the positive comments. We will include a more detailed discussion on the genes and pathways based on our gene expression data that may provide insights into how SRF may regulate astrocyte reactivity and neuroprotection.

Additional considerations:

1. Quantification of the extent of SRF loss in astrocytes in conditional tamoxifen knockout would strengthen the quality of the data.

Response: We will provide this data in the revised manuscript.

While the authos did use a Sholl analysis to show hypertophic changes in SRF negative astrocytes, given that SRF is an important regulator of actin and other cytoskeletal related proteins in other cell types, and that cytoskeletal components can play an important role in cell signaling, it is somewhat surprising that the gene array analysis did not include actin and other cytoskeletal proteins, nor did the authors consider a more careful analysis of intracellular cytoskeletal changes and the potential mechanistic implications of this for observed reactivity and neuroprotection.

Response: We agree with the reviewer that SRF is a well-established regulator of actin cytoskeleton. However, we did not any significant changes in gene expression for actin or actin-regulatory proteins. We would have expected a decrease in astrocyte morphology similar to the neurite/axon defects exhibited by SRF-deficient neurons. It is unclear whether the hypertrophic morphology is due to transcriptional regulation of actin/actin-binding proteins or due to astrocyte reactivity. This would be a very interesting question and we will investigate these aspects in future studies.

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

Summary: The study by Thumu et al., suggests that astrocytic specific deletion of SRF in mice results in morphological changes in these cells that does not affect neuronal survival, synapse number, plasticity or cognition. However, in in vivo mouse models of excitotoxic damage and neurodegenerative disease, deletion of SRF reduced neurotoxicity. The authors provide sufficient evidence to suggest that astrocytic SRF contributes to neurotoxicity in various models however some claims are made that are currently not supported by evidence.

Major comments:

2) The authors claim that SRF KO astrocytes undergo hypertrophy. However, the quantification of the number of intersections gives information about morphology rather than hypertrophy. Quantification of cell size (area of S100B staining) should be provided.

Response: We will provide the data suggested by the reviewer.

6) For the RNAseq of isolated astrocytes did the authors confirm that other cell types (e.g microglia) did not contaminate their samples?

Response: We will provide the information requested by the reviewer.

Reviewer #3:

Minor comments:

1) The authors say that in Figure 1B many astrocytes did not show any SRF expression. However, overall averages of SRF intensity are plotted in Figure 1C. It would support their claim to instead to calculate the percentage of SRF expressing cells above a certain threshold in each condition, rather than plotting the mean intensity. As a control for their method of quantifying SRF intensity in Figure 1B, demonstrating no change in SRF in neurons would provide confidence for the specificity of the knockout.

Response: We will provide the quantification of the extent of SRF loss in astrocytes (percent astrocytes that are deleted for SRF) as suggested by Reviewer 2. We will also provide SRF intensity from neurons as suggested by the reviewer.

2) The authors use the term "reactivation" throughout the manuscript. This could be misconstrued as re-activation and so I would suggest using the terms "reactivity" or "reactive transformation". Furthermore, only one region is quantified in Figure 1C while in later figures multiple regions are quantified. The authors should justify this decision or update the figures with data from missing regions.

Response: We will make this change in using the term “reactivity” as suggested by the reviewer.

3) In Figure S2 the authors should provide a positive control for their staining.

Response: We will provide the positive control data for this experiment.

4) Can the authors explain the large amount of variability in number of synapses in 15 mpi in Figure 3E?

Response: We will perform more immunostainings and update the data presented in this figure.

5) Images in Figure 2C are poorly visible and should be improved in terms of either quality or magnification.

Response: We will provide better quality image for Figure 2C.

8) The authors should provide a list of differentially expressed genes from RNAseq of SRF KO mice. No information is currently given in the text about the number of differentially expressed genes in the conditional knockout.

Response: We will include this information in the revised manuscript.

9) In figure 5A data would be better illustrated as a volcano plot (similar to Fig. S7C).

Response: We will provide this in the revised manuscript.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer #1: Major Comment #2

There is considerable variability in the behavioral results, particularly the fear conditioning and Barnes maze tasks (Figures 4F-G). Given the extremely low sample size for mouse behavior (n=5 in on group, n=7 in the other), it is highly likely that the behavioral tests were done with a single cohort of animals (which would be far from ideal) and that these experiments are significantly underpowered. Furthermore, it does not appear that the fear conditioning task was properly optimized. For example, in the control mice in context A, there were two animals that were at or very close to 0 percent freezing; these were likely outliers, or even an indication that the foot shock conditioning protocol was not working as it should. The highest percent freezing of either group was ~70%, which would have been an ideal starting place as an average for the control group. In addition, sex of the animals was not reported for these experiments. If the authors combined sexes as they did in other analyses in this paper, it is possible that they missed reaching the appropriate reaction threshold for the foot shock for some of the animals, as sex differences have previously been demonstrated in mice (DOI: 10.1037/bne0000248). Given the age at which the animals are assessed with these tasks, these specific revisions would require greater than 6 months to complete. However, as currently presented, there simply are not enough data points to make any conclusions regarding behavior.

Response: We have performed the behavioural experiments with an additional cohort of animals for both control and mutant groups and reanalysed the data. We now have n=11 for control and n=9 for mutant group. Only males were used for the behaviour experiments, and we do not see any significant difference in behaviour between the two groups. These results are included in revised Figure 4E-G in the Preliminary Revision of the manuscript. However, we are waiting to perform the remote recall memory for the fear conditioning experiment and will include this date in the revised manuscript.

Minor Comment #1:

The representative GFAP images (Figure 1 E/G) do not appear to have been taken at the same magnification. This was particularly apparent in the comparison between the control and CKO hippocampus at 12mpi. It is difficult to say with certainty, due to the lack of fiducial markers in many of the images. Inclusion of a nuclear stain (DAPI) would be highly beneficial to allow the reader to make a more informed comparison.

Response: These images were taken at the same magnification. We have included the DAPI staining for these images in Suppl. Figure 2 in the Preliminary Revision of the manuscript.

**Referees cross-commenting**

After reading the comments of the other reviewer, I think we're in agreement that the cellular and molecular data, while descriptive, is of mostly excellent quality. Moreover, the significance of the study is high, and the potential readership broad. However, I stand by my initial assessment of the behavioral data and find the manuscript quite lacking in this regard. Proper revisions would take at least half a year or more, so the authors may be disinclined to go this route. That being said, if the behavioral data were to be excised, I would be happy to sign off on the rest of the manuscript provided that the other major criticisms are addressed.

Response: We thank the reviewer for the appreciation of our work. We have increased the number of animals in the behavioural experiments and do not see any significant difference between the two groups. These results are included in revised Figure 4E-G in the Preliminary Revision of the manuscript.

In response cross-comment of Rev 2:

Agreed that if properly conducted and presented, the behavioral data would indeed provide a nice functional correlate to the cellular work. In its current state, I'm afraid that it is instead a hindrance to the study and I would recommend that they just remove it if they choose not to address my concerns with the quality (particularly the extreme variability and the complete lack of freezing by several of the animals, especially in the controls).

Response: We hope that the revised behaviour data would provide a strong functional correlate to the other findings in the study.

Additional cross-comments:

I agree with the added criticisms raised by Reviewer #3, and I think that the manuscript would be greatly improved by revisions that address those and the original criticisms from myself and Reviewer #2. I still think that the behavioral data should be omitted, provided that the authors are not capable or willing to appropriately address those concerns within a reasonable time frame.

Response: We will address all the concerns raised by the reviewers with the required experiments to further strengthen the findings in this study.

Reviewer #3

Major Comment

3) In Figure S1 the authors provide evidence showing lack of B-gal in cell types other than astrocytes (neurons/OPCs). However, microglia are missing, which could be important as later they show that microglia undergo changes in the SRF knockout model. This staining should be provided.

Response: We have performed double immunostaining for b-gal and IbaI and do not see any overlap between IbaI and b-gal, suggesting that there is no Cre expression in microglia. We have included this data in revised Figure S1F in the Preliminary Revision of the manuscript.

5) The authors claim in the text that microglia have thicker processes and an amoeboid shape however no evidence of this is provided in Figure S5.

Response: We have provided data to show larger microglia area and morphology in revised Figure S5 in the Preliminary Revision of the manuscript.

7) In the text "Enrichment analysis of Gene Ontology terms for Biological Process (GO BP) revealed that Srf deficient astrocytes showed enrichment of pathways related to cellular response to beta amyloid and beta-amyloid clearance." This is not shown in fig 5. It would be more accurate to say that there is a downregulation of genes involved in B amyloid metabolic process.

Response: We apologize for the omission in showing that this data was presented in Suppl. Fig. S8E. We have now indicated this in the main text.

Minor Comments:

4) Figure 1E is missing body weight data noted in the figure legend.

Response: We apologize for this oversight. This data was actually included in Suppl. Figure S3E and not in Figure 1. We have made the appropriate correction to Figure legend 1.

6) In Figure 2B figure labels are missing.

Response: We thank the reviewer for pointing out this omission. We have added the missing labels.

7) Details of houskeeping gene normalisation are missing from qPCR data.

Response: We apologize for not providing this information. We have included this in the revised Methods section.

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

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

Reviewer #3, Major Comment 1:

1) The title of the manuscript is "SRF-deficient astrocytes provide neuroprotection in mouse models of excitotoxicity and neurodegeneration". It would be more accurate to say that SRF is involved in neurotoxicity in these models. To make a comment on the role of SRF in neuroprotection, experiments should be performed in spinal cord injury or ischaemia, where deficiency of SRF would be hypothesised to worsen recovery.

Response: We disagree with the reviewer with this assessment. There is no evidence to suggest that SRF is involved in neurotoxicity. What our data suggests is that SRF deficiency results in a reactive astrocyte state that is neuroprotective in these models. We hypothesize that in injury/infection/disease conditions that would result in generation of neuroprotective astrocytes, SRF expression or function may be negatively regulated. It would be interesting to see whether the SRF-deficient astrocytes alleviate or exacerbate pathology and recovery following spinal cord injury and ischaemia.

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Referee #3

Evidence, reproducibility and clarity

Summary: The study by Thumu et al., suggests that astrocytic specific deletion of SRF in mice results in morphological changes in these cells that does not affect neuronal survival, synapse number, plasticity or cognition. However, in in vivo mouse models of excitotoxic damage and neurodegenerative disease, deletion of SRF reduced neurotoxicity. The authors provide sufficient evidence to suggest that astrocytic SRF contributes to neurotoxicity in various models however some claims are made that are currently not supported by evidence.

Major comments: The title of the manuscript is "SRF-deficient astrocytes provide neuroprotection in mouse models of excitotoxicity and neurodegeneration". It would be more accurate to say that SRF is involved in neurotoxicity in these models. To make a comment on the role of SRF in neuroprotection, experiments should be performed in spinal cord injury or ischaemia, where deficiency of SRF would be hypothesised to worsen recovery.

The authors claim that SRF KO astrocytes undergo hypertrophy. However, the quantification of the number of intersections gives information about morphology rather than hypertrophy. Quantification of cell size (area of S100B staining) should be provided.

In Figure S1 the authors provide evidence showing lack of B-gal in cell types other than astrocytes (neurons/OPCs). However, microglia are missing, which could be important as later they show that microglia undergo changes in the SRF knockout model. This staining should be provided.

Can the authors explain the large amount of variability in number of synapses in 15 mpi in Figure 3E?

The authors claim in the text that microglia have thicker processes and an amoeboid shape however no evidence of this is provided in Figure S5.

For the RNAseq of isolated astrocytes did the authors confirm that other cell types (e.g microglia) did not contaminate their samples?

In the text "Enrichment analysis of Gene Ontology terms for Biological Process (GO BP) revealed that Srf deficient astrocytes showed enrichment of pathways related to cellular response to betaamyloid and beta-amyloid clearance." This is not shown in fig 5. It would be more accurate to say that there is a downregulation of genes involved in B-amyloid metabolic process.

OPTIONAL: Figure 6 would be greatly strengthened by functional in vivo experiments showing reversal of motor/ cognitive phenotypes.

OPTIONAL: The study would be improved by isolating astrocytes from the models used in figure 6 and performing RNAseq to provide information about how SRF knockout affects astrocyte reactivity in these models.

Minor comments: The authors say that in Figure 1B many astrocytes did not show any SRF expression. However, overall averages of SRF intensity are plotted in Figure 1C. It would support their claim to instead to calculate the percentage of SRF expressing cells above a certain threshold in each condition, rather than plotting the mean intensity. As a control for their method of quantifying SRF intensity in Figure 1B, demonstrating no change in SRF in neurons would provide confidence for the specificity of the knockout.

The authors use the term "reactivation" throughout the manuscript. This could be misconstrued as re-activation and so I would suggest using the terms "reactivity" or "reactive transformation".

Furthermore, only one region is quantified in Figure 1C while in later figures multiple regions are quantified. The authors should justify this decision or update the figures with data from missing regions.

In Figure S2 the authors should provide a positive control for their staining.

Figure 1E is missing body weight data noted in the figure legend.

Images in Figure 2C are poorly visible and should be improved in terms of either quality or magnification.

In Figure 2B figure labels are missing.

Details of houskeeping gene normalisation are missing from qPCR data.

The authors should provide a list of differentially expressed genes from RNAseq of SRF KO mice. No information is currently given in the text about the number of differentially expressed genes in the conditional knockout. In figure 5A data would be better illustrated as a volcano plot (similar to Fig. S7C).

Significance

The strength of the manuscript is that the authors demonstrate in more than one model that astrocyte specific knockout of SRF rescues neuronal death, implicating SRF in astrocyte mediated neurotoxicity. The limitations of the study are that the mechanism by which SRF deletion reduces excitotoxicity is not addressed and there is no supporting data beyond neuronal survival in the excitotoxicity/OHDA models or plaque density in the APP/PS1 model.

This study adds SRF to an expanding understanding of the neurotoxic capacity of astrocytes in certain reactive states. It will be of broad interest to the astrocyte reactivity field.

My field of expertise is in astrocyte and microglia interactions in neurodegenerative diseases.

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Referee #2

Evidence, reproducibility and clarity

The manuscript, "SRF-deficient astrocytes provide neuroprotection in mouse models of excitotoxicity and neurodegeneration" by Thumu et al., describes the observation astrocyte specfic SRF deficient mice exhibit neuroprotection against a broad range of brain pathologies. The current ms follows up on previous work done by the corresponding author Ramanan and colleagues in which they showed that astrocyte-specific deletion of SRF early during mouse development resulted in persistent reactive-like astrocytes throughout the postnatal mouse brain. In the current ms the authors present data that adult astrocyte specific conditional deletion of serum response factor results in reactive-like hypertrophic astrocytes that localize throughout the mouse brain. They further show that SRF deficient astrocytes do not affect neuron survival, synapse numbers, synaptic plasticity or learning and memory. Strikingly, they further show that brains of Srf knockout mice exhibit protection against neurodegenerative disease related pathologies including induced excitotoxic cell death and that SRF-deficient astrocytes abrogate dopaminergic neuron death and reduce beta-amyloid plaques in mouse models of Parkinson's and Alzheimer's disease. Based on their results, the authors proposes that SRF is a key molecular switch for the generation of reactive astrocytes with neuroprotective functions can attenuate neuronal injury in the setting of neurodegenerative diseases.

Referees cross-commenting

Reviewer #1 raises an important concern regarding the quality of the behavioral studies. I would also agree that the ms is still strong and the findings are significant without them, although they do extend the functional dimensions of the overall study.

Significance

The manuscript addresses the important area of the cellular mechanisms that underlie neuroprotection. The ms adds to our understanding of genetic control of neuroprotection and should be of significant interest to others in the field. The experimental approach systematic and the data presented are generally of high quality and believable. While the ms presents quite a bit of overall cellular data that underlies various areas of neuronal and brain function that may be affected by loss of SRF, it is still somewhat descriptive. It is unclear what aspect of astrocyte reactivity is determinative, how mechanistically in normal cells SRF suppresses reactivity, and how SRF -negative reactive astrocytes confer such broad neuroprotection. While the latter is well beyond the scope of this study, the authors do propose SRF may be involved in regulating oxidative stress and amyloid plaque clearance as a potential pathway to account for SRF's role, however a more systematic discussion based on the gene expression data and known pathways would be welcome. Overall, this is a high quality ms that should be of interest to the field that identifies a SRF as a novel player in neuroprotection.

Additional considerations:

1. Quantification of the extent of SRF loss in astrocytes in conditional tamoxifen knockout would strengthen the quality of the data.
2. While the authos did use a Sholl analysis to show hypertophic changes in SRF negative astrocytes, given that SRF is an important regulator of actin and other cytoskeletal related proteins in other cell types, and that cytoskeletal components can play an important role in cell signaling, it is somewhat surprising that the gene array analysis did not include actin and other cytoskeletal proteins, nor did the authors consider a more careful analysis of intracellular cytoskeletal changes and the potential mechanistic implications of this for observed reactivity and neuroprotection.

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Referee #1

Evidence, reproducibility and clarity

Summary: The authors used a conditional transgenic mouse model to demonstrate that deletion of serum response factor (SRF) from adult astrocytes provides neuroprotection in various insult/diseases contexts without promoting any obvious phenotypic deficiencies. The work builds on the group's previous study where SRF was embryonically deleted from astrocytes and their precursor cells. Given the role of SRF in promoting glial cell differentiation, the adult conditional KO used in the current study was designed to circumvent the limitations of the previous approach. The authors used a variety of complementary approaches (including immunohistochemistry, electrophysiology, transcriptomics, and behavior) to demonstrate the therapeutic potential of their approach. However, I have questions regarding the validity of the behavioral analyses as well as some of the imaging results that dampen my overall enthusiasm.

Major Comments:

1. The synaptogenic factors probed in Figure 3C (e.g. glypicans, thrombospondins, etc.) are not likely to play major roles in the adult brain in a non-injury context, so I do not know that these analyses provide any significant insight into potential functional changes in the mutant mice. Along the same lines, the analysis of synapse count (Figure 3D-E) seems inconsequential given that SRF was knocked out well after the period of developmental synaptogenesis. It would have been much more interesting to have performed these analyses following insult (such as the kainate injury model used by the authors) or in one of the disease models presented later in the manuscript. As it stands, I don't think they add very much to the study.
2. There is considerable variability in the behavioral results, particularly the fear conditioning and Barnes maze tasks (Figures 4F-G). Given the extremely low sample size for mouse behavior (n=5 in on group, n=7 in the other), it is highly likely that the behavioral tests were done with a single cohort of animals (which would be far from ideal) and that these experiments are significantly underpowered. Furthermore, it does not appear that the fear conditioning task was properly optimized. For example, in the control mice in context A, there were two animals that were at or very close to 0 percent freezing; these were likely outliers, or even an indication that the foot shock conditioning protocol was not working as it should. The highest percent freezing of either group was ~70%, which would have been an ideal starting place as an average for the control group. In addition, sex of the animals was not reported for these experiments. If the authors combined sexes as they did in other analyses in this paper, it is possible that they missed reaching the appropriate reaction threshold for the foot shock for some of the animals, as sex differences have previously been demonstrated in mice (DOI: 10.1037/bne0000248). Given the age at which the animals are assessed with these tasks, these specific revisions would require greater than 6 months to complete. However, as currently presented, there simply are not enough data points to make any conclusions regarding behavior.

Minor Comments:

1. The representative GFAP images (Figure 1 E/G) do not appear to have been taken at the same magnification. This was particularly apparent in the comparison between the control and CKO hippocampus at 12mpi. It is difficult to say with certainty, due to the lack of fiducial markers in many of the images. Inclusion of a nuclear stain (DAPI) would be highly beneficial to allow the reader to make a more informed comparison.
2. The authors should note that the use of GluA1 as a postsynaptic marker will not identify silent synapses (i.e. structurally "normal" but functionally inert).

Referees cross-commenting

After reading the comments of the other reviewer, I think we're in agreement that the cellular and molecular data, while descriptive, is of mostly excellent quality. Moreover, the significance of the study is high, and the potential readership broad. However, I stand by my initial assessment of the behavioral data and find the manuscript quite lacking in this regard. Proper revisions would take at least half a year or more, so the authors may be disinclined to go this route. That being said, if the behavioral data were to be excised, I would be happy to sign off on the rest of the manuscript provided that the other major criticisms are addressed.

In response cross-comment of Rev 2:

Agreed that if properly conducted and presented, the behavioral data would indeed provide a nice functional correlate to the cellular work. In its current state, I'm afraid that it is instead a hindrance to the study and I would recommend that they just remove it if they choose not to address my concerns with the quality (particularly the extreme variability and the complete lack of freezing by several of the animals, especially in the controls).

Additional cross-comments:

I agree with the added criticisms raised by Reviewer #3, and I think that the manuscript would be greatly improved by revisions that address those and the original criticisms from myself and Reviewer #2. I still think that the behavioral data should be omitted, provided that the authors are not capable or willing to appropriately address those concerns within a reasonable time frame.

Significance

General assessment: Overall strengths of this study are the implications of SRF as a broad spectrum anti-neurodegeneration agent and the variety of techniques used. Limitations of this study include a lack of meaningful synaptic comparisons and underpowered behavioral assays.

Advance: Provided the above limitations are addressed, this study would provide a meaningful advance in our understanding of controlled reactive astrogliosis as a potential therapeutic strategy for neuroprotection.

Audience: This study would be of interest to a wide audience, particularly neuro- and gliobiologists as well as clinicians who deal with brain disorders and injury.

Expertise: imaging; behavior; synaptic development

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Reply to the reviewers

We appreciate the valuable suggestions and the overall highly positive review of our manuscript. We have now included many suggestions provided by the reviewers, which have made our manuscript much stronger and more rigorous. One reviewer acknowledged, “This study uncovers sex-dependent mechanisms underlying cold sensitivity between male and female mice. The detailed IHC analysis of MHCII expression in DRG neurons is a clear strength of this study and supports flow cytometry results as well as existing literature. The specificity of MHCII expression on small diameter is well characterized and supported by conditional knockout mouse models of MHCII in TRVPV1-lineage neurons.”

R1: It is not, yet, possible to conclude that all experiments are adequately powered as N's for some studies are not provided.

All experiments include N’s both in the text and in the figure legend.

R1: It is unclear what is meant by "novel" expression, used throughout the manuscript.

MHCII is traditionally thought to be constitutively expressed on antigen-presenting cells (APCs) and induced by inflammation on some non-APCs, including endothelial, epithelial, and glial cells (van Velzen et al., 2009). RNA seq data sets (Nguyen et al., 2021, Tavares- Ferreira et al., 2022, Usoskin et al., 2015, Lopes et al., 2017) demonstrate that mouse and human DRG neurons express transcripts for MHCII and MHCII-associated genes. However, there are no reports to date that demonstrate MHCII protein expression in terminally differentiated neurons. To the best of our knowledge, we are the first group to show that MHCII protein is expressed in DRG neurons.

R1: The statement at the end of the abstract, "and that neuronal MHCII may also contribute to many other neurological disorders" seems premature, beyond the scope of the present study.

We agree with the reviewer’s comment and have changed the sentence to the following: “Collectively, our results demonstrate expression of MHCII on DRG neurons and a functional role during homeostasis and inflammation” (pg. 1).

R1: While cold allodynia (hypersensitivity) is a clinically important feature of CIPN, especially in CIPN associated with the platinum based chemotherapeutic agents, it is less so taxane CIPN. Do 60% of patients with PTX CIPN express cold allodynia or does that number refer to CIPN in general?

This statistic is based on a study that conducted a meta-analysis of CIPN incidence and prevalence with paclitaxel, bortezomib, cisplatin, oxaliplatin, vincristine or thalidomide. However, we now include another reference (PMID: 15082135) that demonstrates patients receiving PTX experience cold hypersensitivity (pg.3).

R1: Again, the future direction of expanding studies of the role of MHCII in other aspects of the CIPN phenotype might bear mention.

We have included future directions regarding other aspects of CIPN phenotype in the discussion. We state, “Reducing the expression of MHCII in TRPV1-lineage neurons exacerbated PTXinduced cold hypersensitivity in both male and female mice. Future studies will evaluate the role of MHCII in PTX-induced mechanical hypersensitivity, another prominent feature of CIPN” (pg. 29).

R1: Is there any evidence that IL-4 and/or IL-10 influence cold sensitivity?

IL-10 and IL-4 have been shown to suppress spontaneous activity from sensitized nociceptors (Krukowski et al., 2016; Laumet et al., 2020; Chen et al., 2020) and to reduce neuronal hyperexcitability (Li et al., 2018), respectively. In addition, IL-10 has been shown to reduce mechanical hypersensitivity (Krukowski et al., 2016); however, cold sensitivity has not been evaluated. IL-4 KO mice do not have an increase in tactile allodynia or cold sensitivity after CCI; however, there is an increase in anti-inflammatory cytokines, specifically IL-10, and opioid receptors, which may be a compensatory mechanism that protects against enhanced pain after injury (Nurcan Üçeyler et al. 2011).

R1: Are these experiments run blinded?

Yes, this is discussed in the materials and methods section (pg. 31).

R1: The term "directly contacts" is unclear. No synaptic structure is identified. It might be more accurate to estimate the actual proximity between the two cells, especially as direct contact would not be necessary for the type of intercellular communication they are studying. This is not an EM study.

We agree with the reviewer’s comment and have changed the wording to “in close proximity” (pgs. 1,5, 7, 27).

R1: Two abbreviations are used for immunohistochemistry, ICC and IHC.

IHC refers to immunohistochemistry, and ICC refers to immunocytochemistry. We accidently wrote ICC in the immunohistochemistry section in the materials and methods section. We have now corrected it to say IHC (pg. 32).

R1: In some figure, group sizes are not indicated (e.g., Fig. 4D).

All group sizes are indicated in the text and figure legends.

R1: "small non-nociceptive neurons" - seems to refer to TRPV1+ neurons. There are, however, TRPV1-nociceptors. "Therefore, the majority of MHCII+ neurons in the DRG of naïve female mice were not TRPV1- lineage neurons but non-nociceptive C-LTMRs." Could use some clarification here. Are the authors suggesting that being TRPV1- defines a neuron a non-nociceptive?

We never said small non-nociceptive neurons are TRPV1+ neurons. We crossed TRPV1 lineage mice with td-tomato to label TRPV1 lineage neurons, which include TRPV1 neurons, IB4, and a subset of Aẟ neurons. We found that TRPV1 lineage neurons comprise about 65% of small diameter neurons, so 35% of small diameter neurons are not TRPV1 lineage cells. These non- TRPV1 lineage small diameter neurons are non-nociceptive LTMRs, most likely TH and MrgB4 neurons.

R2: The most pressing concern regarding this study is a lack of a vehicle control group. It is not appropriate to be comparing paclitaxel treated mice to naïve mice. Please include a vehicle treatment (cremophor:ethanol 1:1 diluted 1:3 in PBS) group for all experiments involving paclitaxel.

We believe the most appropriate control to paclitaxel treatment is the naïve control because clinically, paclitaxel is always administered to the patient in a formulation of 50% Cremophor and 50% ethanol. In clinical studies, the controls are healthy no-pain individuals and patients receiving paclitaxel without pain. However, the percentage of patients receiving paclitaxel that do not develop CIPN is low, emphasizing the need for healthy individuals not taking paclitaxel.

R2: Figure 1A only includes representative images of a small number of T cells in presumable contact with DRG neurons in female Day 14 paclitaxel mice but does not include images from other groups. Similarly, B-D show a single CD4+ T cell in contact with DRG neurons in Day 14 paclitaxel and naïve female mice. Please include quantification of the frequency of CD4+ T cells interacting with DRG neurons in the different experimental groups utilized in this study.

We have now quantified the number of CD4+ T cells per mm2 of DRG tissue, which is found in the text (pg. 5) and figures (Fig. S1 and Fig. 1A). We plan to add the quantification of CD4+ T cells per mm2 of DRG tissue for naïve and day 14 PTX-treated male mice. This data will be included in the text (pg. 5) and in Fig. S1.

R2: Please include entire blot for Figure 2A (or at least more of the blot). There is plenty of space in the figure and as it currently appears is not free from apparent manipulation.

We included a larger area of the western blot in Fig 2A (pg. 9).

R2: The authors conclude that MHCII helps to suppress chemotherapy-induced peripheral neuropathy, resolving cold allodynia following paclitaxel treatment. To support this conclusion, I think it is necessary to include a time-course experiment highlighting whether cKO of MHCII in TRPV1 neurons indeed increases the duration for cold hypersensitivity to resolve following paclitaxel treatment.

We conclude that neuronal MHCII suppresses cold hypersensitivity in naïve male mice and reduces the severity of PTX-induced cold hypersensitivity at the peak of the response (day 6) (pg. 1-2). In addition, knocking out one copy of MHCII in male TRPV1-lineage mice reduced total neuronal MHCII in naïve and PTX-treated mice (day 7 and 14) (pgs. 21-22; Fig.7). Moreover, knocking out one copy of MHCII in female TRPV1-lineage mice reduced surface- MHCII in female 7 days post-PTX (pgs. 19-20; Fig.6). Future studies will investigate the distinct roles of surface and intracellular neuronal MHCII and the contribution of MHCII to the resolution of CIPN.

R2: The graphical abstract is misleading. The authors suggest paclitaxel is acting exclusively via TLR4 and that signaling is resolved at Day 14 which their data does not support. Please adjust to reflect findings from the experiments included in this study.

We have removed TLR4 from our graphical abstract as we do not investigate the role of TLR4 in this manuscript. However, we do not suggest paclitaxel is acting exclusively through TLR4. We modified our wording to indicate both pro-inflammatory cytokines and PTX act on neurons to induce hyperexcitability and neurotoxicity: “Pro-inflammatory cytokines and PTX act on DRG neurons inducing hyperexcitability (Li et al., 2018, Boehmerle et al., 2006, Li et al., 2017) and neurotoxicity (Goshima et al., 2010, Flatters and Bennett, 2006), which manifests as pain, tingling, and numbness in a stocking and glove distribution (Rowinsky et al., 1993)” (pg. 9).

R2: Figure 4 and 6 MHCII labelling is oversaturated in most of the images, creating a blurry hue in the representative images. This should be fixed.

The signal intensity of immune cell MHCII is >5 times greater than neuronal MHCII; therefore, in order to visualize neuronal MHCII, the immune cell MHCII is oversaturated. We reference this in the discussion (pg. 26).

R2: The effects of the PTX cHET group are very mild in both the male and female cohorts, and specific to 1 trial. R3: Furthermore, the behavioral effect is seemingly variable, with only one of the three trials being significantly different between groups. This variable response needs to be discussed further.

This behavioral assay was developed by the UNE COBRE Behavior Core, under the guidance of Dr. Tamara King, who has extensive experience in using learning and memory measures to determine changes in pain such as development of thermal hypersensitivity (1-3, King et al, Nat Neuro 2009). Methodologically, the process is as follows: In the temperature placed preference assay, mice are placed on the reference plate (25 °C) to begin each 3-minute trial. For the habituation trial, both the test and reference plates are set to 25 °C, and the mice are allowed to explore for 3 minutes. The following 3 trials are the acquisition trials where the reference plate is set to 25 °C and the test plate to 20 °C. If the animals have cold hypersensitivity, modeling cold allodynia, then they will demonstrate faster acquisition of a learned avoidance response compared to the WT controls. For the results, we will clarify our findings, which are outlined below: 1) We will change the axis labels to better distinguish BL/habituation trial from reference trials in the graphs. 2) We will add graphs comparing naïve versus PTX for male and female WT mice. 3) The changes in the graphs will now reflect 3 key findings: First, we note that PTX-treated mice learn to avoid the cold test plate faster than the naive controls in the WT mice reflecting PTX-induced cold hypersensitivity. Of interest, both males and females demonstrate learned avoidance by trial 2 and that the percent of time on the cold plate continued to decline only in the PTX-treated mice. We had not graphed this in the original figure and plan to add graphs for both male and female WT mice. These graphs are important to include as it validates that this TPP can capture the expected PTX-induced cold hypersensitivity in WT mice. Second, in terms of the naïve cHET mice, these data show that both female and male cHET mice demonstrate faster learning to avoid the cold (20 °C) plate compared to the WT mice (Fig. 8A, B. We note that the males demonstrate a more robust effect, (faster learned avoidance of the cold plate) with significant avoidance to the cold plate emerging in the cHET mice by trial 3 compared to trial 4 in the females (sig diff compared to BL trial). Third, we observed that cHET mice treated with PTX demonstrate even more accelerated learning to avoid the cold plate compared to WT mice treated with PTX. This observation suggests that PTX-treated cHET mice have heightened cold allodynia compared to the WT mice.

R2: The statistical analysis (for the behavior) should also have been a mixed-effects repeated measures between groups ANOVA.

We agree and re-analyzed our behavior data using repeated measures mixed-effects model (REML) with Dunnett’s multiple comparison test comparing trials 2-4 to trial 1 within same group, and Sidak’s multiple tests for significance between groups at the same trial (pgs. 23-25; Fig. 8)

R3: Presented in Figure 3, the authors present data to show surface expression of MHCII, along with the ability of MHCII to present OVA peptide, on naïve and PTX-treated DRG neurons. These data are probably the most relevant in terms of expression as they look at the surface expression of MHCII along with the potential of MHCII to function; therefore, it is unclear why the authors only conducted this analysis on female neurons, and not both male and female neurons. Given the claims of the paper in terms of sex differences for MHC expression, I strongly suggest this is done in order to put the other observations into context.

We completely agree and have added male mice data in Figs. 2 and 3. By western blot, we show that PTX increased the amount of MHCII protein 14 days post-PTX in DRG neurons from female mice, but there’s no change in MHCII protein after PTX in male mice (Fig. 2). In agreement with the western blot, surface-MHCII determined by flow cytometry did not increase after PTX on DRG neurons from male mice (Fig. 3B). Moreover, the frequency of DRG neurons from male mice with surface-MHCII (determined by ICC) and OVA peptide did not change after PTX treatment (Fig. 3D, E). However, the percent area with polarized MHCII on DRG neurons from male mice increased 14 days post-PTX, indicating a modest PTX-induced response in males (Fig. 3F). We have now included the frequency of surface-MHCII on DRG neurons from male and female mice after PTX treatment, and again there was no change in surface-MHCII in male mice (Fig. 6). Collectively, our data demonstrates that neuronal MHCII in male mice is not strongly regulated by PTX treatment.

R3: Given the data presented in Figure 3, it is not clear what the relevance of investigating the subcellular puncta expression of MHCII neurons is, particularly when considering the sex differences observed, and how this was not been performed for surface expression.

We now include surface and total MHCII quantification for male and female WT and cHET mice (Figs. 6,7). In the text, we describe the significance of surface versus endosomal MHCII. “While endosomal MHCII can promote TLR signaling events(Liu et al., 2011), expression of MHCII on the cell surface is required to activate CD4+ T cells.” (pg. 10). “Although the major role for surface MHCII is to activate CD4+ T cells, cAMP/PKC signaling occurs in the MHCII-expressing cell(Harton, 2019). In addition, it has recently been shown that endosomal MHCII plays an important role in promoting TLR responses(Liu et al., 2011), and since DRG neurons are known to express TLRs (Lopes et al., 2017, Wang et al., 2020, Cameron et al., 2007, Barajon et al., 2009, Xu et al., 2015, Zhang et al., 2018), this suggests the potential for T-independent responses in MHCII+ neurons. Knocking out one copy of MHCII in TRPV1- lineage neurons (cHET) from female mice did not change total MHCII 7 days post-PTX but reduced surface-MHCII. Accordingly, PTX-treated cHET female mice were more hypersensitive to cold than PTX-treated WT female mice, suggesting a role for neuronal MHCII in CD4+ T cell activation and/or neuronal cAMP/PKC signaling. In contrast, knocking out one copy of MHCII in TRPV1-lineage neurons (cHET) from male mice did not change surface-MHCII in naïve or PTX-treated mice but reduced total MHCII, indicating endosomal MHCII and potentially a role in TLR signaling. Future studies are required to delineate MHCII surface and endosomal signaling mechanisms in naïve and PTX-treated female and male mice.” (pg. 28).

R3: Furthermore, the authors should provide details of what the abundant non-neuronal structures are within the DRG images that appear positive for MHCII staining.

We now include an image of the high MHCII+ cells in mouse DRG co-stained with macrophage and dendritic cell markers (CD11b/c), indicating the presence of immune cells (Fig. S6).

R3: The behavioral data presented in Figure 7 is somewhat confusing. Can the authors confirm how many alleles of MHCII were knocked out from the Trpv1-lineage neurons for these experiments? In Figure 7, it states cKO Het, which suggests that only one allele was deleted within the Trpv1 population. If this is the case, this needs to be clearly outlined within the results section and not simply referred to as "knocking out MHCII in Trpv1-lineage neurons". In addition, an explanation as to why heterozygous cKO were used rather than homozygous cKO needs to be provided. This is particularly relevant when discussing potential sex differences.

The mouse behavior is performed in wild type and TRPV1lin MHCII+/- heterozygote mice (Fig 8). Instead of saying we knocked out MHCII, we changed the text to “knocking out one copy of MHCII in TRPV1-lineage neurons” (pgs. 23, 29). In the methods section, we state that “cHET×MHCIIfl/fl crosses only yielded 8% cKO mice (4% per sex) instead of the predicted 25% (12.5% per sex) based on normal Mendelian genetics. Thus, cKO mice were only used to validate MHCII protein in small nociceptive neurons” (pg. 30) (Fig 7).

R3: A significant gap in the current manuscript is the functional assessment of MHCII protein expressed on DRG neurons in terms of T cell activity. I would suggest the authors consider performing a co-culture DRG-T cell (i.e. Treg) assay where anti-inflammatory cytokine release can be measured in the presence and absence of MHCII on DRG neurons.

The functional implication of MHCII protein on DRG neurons in terms of T cell activity is out of the scope of this manuscript. We currently have another manuscript in progress investigating CD4+ T cell signaling and cytokine production when co-cultured with DRG neurons. R3: Within the first paragraph of the results section, the authors reference Goode et al, 2022, stating that they have previously shown that CD4+ T cells in the DRG secrete anti-inflammatory cytokines. I have read this paper and could not find any data that showed increased secretion of cytokines, only that there is an increase in T-cell populations that contain anti-inflammatory markers. Please consider rewording to reflect the observations made in the original paper. We have changed “secrete” to “produce” (pg. 5) because we detected anti-inflammatory cytokines (IL-10 and IL-4) within CD4+ T cells using intracellular staining and multi-color flow cytometry.

R3: Figure 1A states that it is "day 14 PTX", however, there is no reference to this in the corresponding text - please state what Figure 1A is showing in the main text and legend regarding PTX treatment.

We have now included text and Fig. 1. legend that states that the images in Fig1A are of DRG tissue collected from female mice 14 days after PTX treatment (pg. 5).

R3: Throughout the results section (Figure 3-Figure 6), the authors provide percentage changes in observed difference in expression, however, in addition to this, it would be valuable to have the actual number of neurons analysed for each group and sex.

We now report in the materials and methods section the number of neurons that were analyzed (pg. 33).

R3: For Figure 5, can the authors confirm whether this was performed on tissue sections or dissociated cell culture?

This analysis was performed in DRG tissue sections. The legend now states, “Gaussian distribution of the diameter of MHCII+ DRG neurons in DRG tissue from naïve (pink), day 7 (orange) and day 14 PTX-treated (blue) (A) female and (E) male mice (n=8/sex, pooled neurons).”

R3: Can the authors comment on why surface expression for MHCII was not performed on the these reporter neurons?

In the future, we plan to delineate which subsets of neurons express MHCII by co-staining for MHCII and specific neuronal markers. However, these studies are beyond the scope of the current manuscript.

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Referee #3

Evidence, reproducibility and clarity

This manuscript sets out to investigate the mechanism by which the previously reported infiltration CD4+ T cells into the DRG parenchyma can mediate analgesia in the paclitaxel (PTX) model of chemotherapy-induced neuropathic pain (CIPN). The authors provide good rationale for the purpose of the study and make a number of interesting observations, including the expression of MHCII on DRG neurons, the effect of PTX on MHCII expression on DRG neurons, and the effect of targeted deletion of MHCII on Trpv1-expressing putative nociceptive neurons in exacerbating the effect of PTX-induced cold hypersensitivity. These data culminate to a hypothesis that MHCII expression on DRG neurons may drive T-cell mediated anti-inflammatory effects (and analgesia) in models where their recruitment is notable. Overall I enjoyed reading the manuscript, however, I believe there are a number of points that need to be considered further.

Major comments.

• Presented in Figure 3, the authors present data to show surface expression of MHCII, along with the ability of MHCII to present OVA peptide, on naïve and PTX-treated DRG neurons. These data are probably the most relevant in terms of expression as they look at the surface expression of MHCII along with the potential of MHCII to function; therefore, it is unclear why the authors only conducted this analysis on female neurons, and not both male and female neurons. Given the claims of the paper in terms of sex differences for MHC expression, I strongly suggest this is done in order to put the other observations into context.
• Given the data presented in Figure 3, it is not clear what the relevance of investigating the subcellular puncta expression of MHCII neurons is, particularly when considering the sex differences observed, and how this was not been performed for surface expression. Furthermore, the authors should provide details of what the abundant non-neuronal structures are within the DRG images that appear positive for MHCII staining.
• The behavioural data presented in Figure 7 is somewhat confusing. Can the authors confirm how many alleles of MHCII were knocked out from the Trpv1-lineage neurons for these experiments? In Figure 7, it states cKO Het, which suggests that only one allele was deleted within the Trpv1 population. If this is the case, this needs to be clearly outlined within the results section and not simply referred to as "knocking out MHCII in Trpv1-lineage neurons". In addition, an explanation as to why heterozygous cKO were used rather than homozygous cKO needs to be provided. This is particularly relevant when discussing potential sex differences. Furthermore, the behavioural effect is seemingly variable, with only one of the three trials being significantly different between groups. This variable response needs to be discussed further.
• A significant gap in the current manuscript is the functional assessment of MHCII protein expressed on DRG neurons in terms of T cell activity. I would suggest the authors consider performing a co-culture DRG-T cell (i.e. Treg) assay where anti-inflammatory cytokine release can be measured in the presence and absence of MHCII on DRG neurons.

Minor comments.

• Within the first paragraph of the results section, the authors reference Goode et al, 2022, stating that they have previously shown that CD4+ T cells in the DRG secrete anti-inflammatory cytokines. I have read this paper and could not find any data that showed increased secretion of cytokines, only that there is an increase in T-cell populations that contain anti-inflammatory markers. Please consider rewording to reflect the observations made in the original paper.
• Figure 1A states that it is "day 14 PTX", however, there is no reference to this in the corresponding text - please state what Figure 1A is showing in the main text and legend regarding PTX treatment.
• Throughout the results section (Figure 3-Figure 6), the authors provide percentage changes in observed difference in expression, however, in addition to this, it would be valuable to have the actual number of neurons analysed for each group and sex.
• For Figure 5, can the authors confirm whether this was performed on tissue sections or dissociated cell culture? In addition, can the authors comment on whey surface expression for MHCII was not performed on the these reporter neurons?

Significance

This paper presents interesting data on the expression of MHCII on DRG neurons, which corroborates existing and published RNA expression data from the literature. In addition, this paper builds on our current understanding of how T-cells may be able to interact with DRG neurons in order to modulate their responses in instances of nerve injury. However, there are significant gaps in the data presented which prevent a more informative conclusion being drawn regarding the role of MHCII in modulating neuronal responses following PTX-induced CIPN.

Audience: I would suggest basic scientists working within the field of pain and neuroimmunology would be interested in this work.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Whitaker EE and co-authors implicate MHCII expression in DRG neurons in the resolution of pain following paclitaxel treatment. The authors demonstrate that CD4 T cells closely interact with DRG neurons, which also express MHCII proteins. They further characterize neuronal MHCII expression in naïve and paclitaxel treated mice in small diameter TRPV1+ neurons. Utilizing genetic animal models with MHCII knockout in TRPV1-lineage neurons, the authors highlight that loss of MHCII in TRPV1 neurons exaggerates cold sensitivity in naïve male mice, and in both sexes following paclitaxel treatment.

Major concerns:

The most pressing concern regarding this study is a lack of a vehicle control group. It is not appropriate to be comparing paclitaxel treated mice to naïve mice. Please include a vehicle treatment (cremophor:ethanol 1:1 diluted 1:3 in PBS) group for all experiments involving paclitaxel. This would also improve statistics as unpaired T tests comparing naïve vs paclitaxel is not convincing.

Figure 1A only includes representative images of a small number of T cells in presumable contact with DRG neurons in female Day 14 paclitaxel mice, but does not include images from other groups. Similarly, B-D show a single CD4+ T cell in contact with DRG neurons in Day 14 paclitaxel and naïve female mice. Please include quantification of the frequency of CD4+ T cells interacting with DRG neurons in the different experimental groups utilized in this study.

Please include entire blot for Figure 2A (or at least more of the blot). There is plenty of space in the figure and as it currently appears is not free from apparent manipulation.

The authors conclude that MHCII helps to suppress chemotherapy-induced peripheral neuropathy, resolving cold allodynia following paclitaxel treatment. To support this conclusion, I think it is necessary to include a time-course experiment highlighting whether cKO of MHCII in TRPV1 neurons indeed increases the duration for cold hypersensitivity to resolve following paclitaxel treatment.

Minor concerns:

The graphical abstract is misleading. The authors suggest paclitaxel is acting exclusively via TLR4 and that signaling is resolved at Day 14 which their data does not support. Please adjust to reflect findings from the experiments included in this study.

Figure 4 and 6 MHCII labelling is oversaturated in most of the images, creating a blurry hue in the representative images. This should be fixed

The effects of the PTX cHET group are very mild in both the male and female cohorts, and specific to 1 trial. I believe these assessments were conducted at Day 6 post injection. Why was this timepoint chosen considering differences in MHCII expression in small neurons was only present at Day 14 relative to naïve? The statistical analysis should also have been a mixed-effects repeated measures between groups ANOVA.

Significance

This study uncovers sex-dependent mechanisms underlying cold sensitivity between male and female mice. The detailed IHC analysis of MHCII expression in DRG neurons is a clear strength of this study, and supports flow cytometry results as well as existing literature. The specificity of MHCII expression on small diameter is well characterized and supported by conditional knockout mouse models of MHCII in TRVPV1-lineage neurons. The clear limitations of this study is the lack of a vehicle control group and limited behavioral analysis. They undermine the conclusions made by the author, and in extension, the significance of this study.

This study adds to the understanding of neuro-immune signaling in peripheral neuropathic pain. As far as I am aware, this is the first study to investigate MHCII expression in DRGs in relation to development of chemotherapy-induced peripheral neuropathy. Thus this study provides an incremental advance in neuroimmune mechanisms contributing to the development of chemotherapy-induced peripheral neuropathy in mice.

This study would be of interest to basic researchers interested in neuropathic pain, with particularly researchers with a focus on neuroimmunology and chemotherapy-induced peripheral neuropathy models. The sex differences observed in naïve mice would also be of interest to basic researchers within the wider pain field. Given the preliminary nature of the findings, I do not think this would be of interest to broader neuroimmunology or clinical audiences.

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Referee #1

Evidence, reproducibility and clarity

Section A:

The key conclusions of this study are quite robust and compelling.

While no claims need qualification clarification of some conclusions could improve the impact of this study.

Additional experiments are not essential to support the claims of this study.

Sufficient details are provided to allow reproduction of the key findings of this study.

It is not, yet, possible to conclude that all experiments are adequately powered as N's for some studies are not provided.

Significance

Section B:

• State what audience might be interested in and influenced by the reported findings.

This study should be of broad interest not only in the field of the neurobiology of pain but in broader issues related to neuroimmunology.<br /> - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am a clinician-scientist with clinical responsibilities in immunologic disorders and a basic scientist with expertise in the area of pain, including chemotherapy-induced painful peripheral neuropathies and neuroimmune mechanisms.<br /> - Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.<br /> - Place the work in the context of the existing literature (provide references, where appropriate).

The authors provide compelling evidence that MHCII expression of MHCII in primary sensory neurons, is regulated in painful chemotherapy-induced peripheral neuropathy (CIPN) induced by the commonly used taxane class of chemotherapy drugs, paclitaxel (PTX).

The present studies build on recent literature demonstrating that PTX CD4+ T cells in DRG. This is key to their hypothesis as T cells and anti-inflammatory cytokines protect against CIPN. In the present study these investigators studied how CD4+ T cells are activated role of cytokines released from these cells on CIPN. To key findings of the present study: the expression of functional MHCII protein in DRG neurons and the proximity of the DRG neurons and CD4+ T cells. While the MHCII protein was expressed in small-diameter, nociceptive, DRG neurons, in male mice, in females it was induced by PTX. Compatible with the hypothesis that the anti-inflammatory CD4+ T cells attenuate CIPN. Finally, in support of the contribution of this mechanism to CIPN pain, they demonstrated that attenuation of MHCII protein from nociceptors produced the predicted increase in cold hypersensitivity. Taken together their findings support suppression of CIPN by MHCII

While the experiments are well designed and executed and the results clearly presented, I have some relatively minor concerns that, if addressed, might improve the ability of a general scientific audience to appreciate the impact of the findings presented (possibly a penultimate paragraph covering caveats and limitations of the present study).

It is unclear what is meant by "novel" expression, used throughout the manuscript.

The statement at the end of the abstract, "and that neuronal MHCII may also contribute to many other neurological disorders" seems premature, beyond the scope of the present study.

While cold allodynia (hypersensitivity) is a clinically important feature of CIPN, especially in CIPN associated with the platinum based chemotherapeutic agents, it is less so taxane CIPN. Do 60% of patients with PTX CIPN express cold allodynia or does that number refer to CIPN in general? Again, the future direction of expanding studies of the role of MHCII in other aspects of the CIPN phenotype might bear mention. Is there any evidence that IL-4 and/or IL-10 influence cold sensitivity? Are these experiments run blinded?

The term "directly contacts" is unclear. No synaptic structure is identified. It might be more accurate to estimate the actual proximity between the two cells, especially as direct contact would not be necessary for the type of intercellular communication they are studying. This is not an EM study.

Two abbreviations are used for immunohistochemistry, ICC and IHC.

In some figure, group sizes are not indicated (e.g., Fig. 4D).

"small non-nociceptive neurons" - seems to refer to TRPV1+ neurons. There are, however, TRPV1-nociceptors.

"Therefore, the majority of MHCII+ neurons in the DRG of naïve female mice were not TRPV1-lineage neurons but non-nociceptive C-LTMRs." Could use some clarification here. Are the authors suggesting that being TRPV1- defines a neuron a non-nociceptive?

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Reply to the reviewers

We would like to thank all reviewers for their highly valuable comments, reviewing the article, and suggesting changes to improve its overall structure, clarity, and comprehension. Please find below our point-by-point responses to each reviewer’s comments. Lines, figures, and tables we refer to in the responses correspond to the clean copy of the revised manuscript.

Reviewer #1:

1) In the introduction the authors list 4 databases of ultra-conserved non-coding elements, and choose to work with the UCNEbase that detects UCNE regions by comparing human and chicken, as they state that it is one of the most comprehensive resources. Can the authors comment on the extent of overlap of UCNE regions identified in this database compared to other databases. It would also be helpful to add an explanation in the Introduction on the advantage of comparing the human genome to the chicken genome, e.g., is chicken the most distant vertebrate with a high quality genome, or another reason? And can the authors comment on the extent of conservation of the UCNEs compared to other species - in the UCNEbase paper, orthologues for the UCNEs are identified in 18 vertebrate species including reptiles, amphibians and fish.

We have addressed these comments and incorporated them in the introduction (lines 46-47; 49-52). As stated, it is not straightforward to evaluate to which extent UCNE regions overlap with those collected in other databases due to the different scopes and methods of these resources. We clarified why we selected this database, which was precisely based on the comments mentioned by the reviewer, i.e., sufficient evolutionary distance to identify functional regions confidently and high quality genome assemblies. Regarding the extent to which UCNEs are conserved in other species, the UCNEdatabase indeed provides additional information with respect to UCNE orthologues in other vertebrate species, including reptiles, amphibians, and fish. As we consider that this comparison is beyond the scope of the present study, it was not included in the main manuscript. However, to address this interesting point raised by the reviewer, we evaluated the proportion of UCNEs found in different species with respect to those annotated for human-chicken. As show in the figure below, UCNEs are conserved to a larger extent up to Xenopus tropicalis, for which most of the UCNEs annotated for human-chicken have corresponding orthologues in this species. Although to a minor extent, UCNEs are also conserved across more distant species (e.g., fish), for which approximately half of the UCNEs annotated for human-chicken have orthologues.

2) The authors briefly describe how potential target genes were assigned to UCNEs in the Method section (section begins on page 21, line 407 and on lines 379-381). They note that they used the Genomic Regions Enrichment of Annotations Tool (GREAT). Can the authors provide additional details on what this method does and also provide a high level sentence in the Results section on page 8, lines 144-146, on how target genes were assigned to UCNEs, as well as in the Discussion on page 16, line 289. Based on the Methods description on lines 409-414, a UCNE was associated with any gene within 1Mb of the UNCE that was expressed in retina and whose curated regulatory domains overlapped the UNCE. Is this correct? How were the regulatory domains curated (line 411-412)? Can the authors please clarify this important point.

Additional details about the GREAT algorithm have been included in the Methods section (lines 410-424) as well as a high-level sentences in the Results (lines 140-141) and Discussion (lines 276-280). It is correct that a UCNE was associated with any gene within 1Mb of the UCNE that was expressed in retina and whose curated regulatory domains overlapped the UCNE. As stated now (lines 420-424), these regulatory domains are supported by experimental evidence demonstrating that a gene is directly regulated by an element located beyond of its putative regulatory domain. We specified these domains for the utilized version of GREAT as well.

3) There are other approaches for linking putative transcriptionally active genomic regions with target genes in specific tissues or cell types through correlation analysis of ATAC-seq peaks (chromatin accessibility) and gene expression in RNA-seq data. A commonly used peak-to-gene linkage method is implemented in ArchR (Granja et al, 2021, PMID: 33633365). The authors note that they used scATAC-seq gene scores and scRNA-seq gene expression to further characterize the proposed target genes of UCNEs. It is not clear what the authors mean by "scATAC-seq gene scores". Please define "scATAC-seq gene score" and add a reference. Can the authors compare the target gene mapping to UCNEs using GREAT and gene expression filtering to that using peak-to-gene linkage based on retina tissue or single cell ATAC-seq and RNA-seq data?

We have defined explicitly what scATAC-seq gene scores are in the Methods section (lines 436-437) along with its reference. We have also addressed this important point and compared the overlap between the set of target genes predicted by GREAT and those assigned by the peak-to-gene linkage method implemented by ArchR. Details of this analysis, its results, interpretation are included in the Methods (lines 441-446), Results (lines 158-163; Supplementary Table 4), and Discussion (lines 280-282) sections.

4) For gene expression filtering (line 419) the authors quantify transcript expression of retina from FASTQ samples using the Kallisto method, and then note that they did the filtering on gene expression levels (TPM<0.5). Please add details on how you went from transcript expression levels to gene expression levels for the filtering, or was the filtering performed at the transcript level?

We have added details on how transcript-level quantification estimates were summarized at gene level, for which the filtering was performed (lines 429-430).

5) The authors use the words "active UCNE", first mentioned in the Results on line 144. Can the authors define what they mean by "active UCNE". What information/evidence is used to ascertain that a UCNE is indeed active. Overlap of a UCNE with a chromatin accessibility region from ATAC-seq or DNAase-Seq would only suggest that the UCNE may be active. Intersection with enhancer activity measured with in vivo enhancer reporter assays in transgenic mice from the VISTA enhancer browser provides stronger evidence of transcriptional activity. The authors might want to distinguish between putatively actively and active based on the functional support.

We thank the reviewer for this relevant comment to address the nuances of defining active UCNEs. The reviewer’s assumptions are correct and hence these terms were clarified throughout the entire text. The term functional is now only used when referring to UCNEs for which there is functional support (e.g., PAX6-associated UCNE in line 193) .

6) The authors assessed the significance of depletion of common variation (MAF>1%) in the UCNE regions compared to a background of randomly selected genomic regions. In generating the random distribution of regions, did the authors match on the distribution of distances of the UNCEs to the TSS of genes in the randomly selected regions? This may be a confounder. Also, in the legend of Figure 3, lines 191-192, it is stated: "Variant population frequencies within putative retinal UCNEs normalized to a background composed of randomly selected sequences (see Methods).", but we did not find a description of this analysis in the Methods section.

Evaluating the potential confounding effect of the genomic background was indeed a very important point. We have now incorporated the details showing the suitability of such background well as a detail description of how such background was generated (lines 479-481; Figure S1). Additionally, to further support our analysis demonstrating the depletion of common variation within UCNEs, we have included an evaluation of the distribution of genome-wide residual variation intolerance score (gwRVIS) values (PMID: 33686085) compared to this background of randomly selected genomic regions in a human reference cohort (lines 173-178; 487-495; Fig. 3C).

7) In regards to intersecting UCNEs with epigenetic marks that detect active or repressed enhancers in retina, the authors used data from Aldiri et al 2017 that measured epigenetic changes during retinal development. Did this dataset contain epigenetic measurements in adult retina? The authors might want to consider using the epigenetic marks/ChIP-seq data from adult human retina in Cherry et al. PNAS 2020 (PMID: 32265282)

We have incorporated the adult-stage data suggested by the reviewer to provide a more comprehensive characterization. Details about the integration of this dataset as well as the results and their corresponding interpretation have been incorporated in the Methods (lines 372-374), Results (lines 115-117; Supplementary Table 2), and Discussion (lines 271-273) sections accordingly.

8) With respect to the examination of rare variants that may be associated with rare eye disease in retina active UCNEs, for the interpretation of the results, it would be helpful to get more information on the distribution of rare variants found in UCNEs associated in this study to known IRD genes in all affected individuals in families, if this information is available in the 100,000 Genomes Project.

Although it is indeed a relevant point, this information cannot be retrieved in the 100,000 Genomes Project. As it is a restricted research environment, we are only allowed to query sequencing data corresponding to participants enrolled within the framework of our specific sub-domain, namely “Hearing and Sight”, and therefore evaluating the distribution of rare variants in all affected individuals is not feasible.

9) In the Methods section on lines 450-451, the authors mention that they performed variant screening of retinal disease genes, referencing the Genomics England Retinal Disorder panel and Martin et al., 2019. Can the authors add to the Methods and Results sections how many retinal disease genes were initially tested. Also, to get a sense of the specificity of the overlap of rare variants in the 100k Genome Project cohort with UNCE regions, it would be informative to show a distribution of the number of rare variants <0.5% that passed the filtering in gnomAD per eye disease gene before the overlap with UNCEs.

We specified the number of retinal genes that were tested in the Method section (line 471). In addition, as suggested by the reviewer, we generated allele frequency distributions for all variants retrieved within a selection of 25 disease-gene associated loci and their corresponding UCNEs in order to assess the specificity of the overlap between rare variants and UCNE regions (lines 181-182, 496-501; Figure S2).

10) The authors found "an ultrarare SNV (chr11:31968001T>C) within a candidate cis-regulatory UCNE located ~150kb upstream of PAX6. This variant was found in four individuals of a family segregating autosomal dominant foveal abnormalities". They tested the functional effect of this element with a reporter assay in zebrafish and found that the UNCE affects expression in the eye, forebrain, and neural tube. It would add further value if the authors were to test the effect of this SNV in the UCNE on the reporter expression pattern, using CRISPR/cas9?

That is a very relevant point. We have tested the effect of this SNV in the UCNE on the reported expression pattern using the same experimental setup that we used for testing the wild-type construct, namely transgenic enhancer zebrafish assays. However, we could not obtain conclusive results, most likely due to the limitations posed by testing these regions outside their native genomic context. Therefore, additional experimental work (e.g., CRISPR-based) should be performed to address this question. This is, however, beyond the scope of the present study, for which the main focus was the identification and functional annotation of ultraconserved cCREs. We have incorporated the details, results, and interpretation of the assays performed mutant construct in the Methods (lines 525-527; Supplementary Table 12), Results (lines 235-238; Supplementary Table 10), and Discussion (lines 350-353) sections.

11) The authors found rare variants in UCNEs linked to 45 IRD genes. Can the authors provide additional information on the functional genomic annotations of these UCNEs and distance to the target genes. The UCNEs were characterized with respect to their genic features in the original paper (UCNEbase, Dimitrieva et al., NAR, 2013), e.g., intergenic, intronic and 3'/5' UTR. Also, it would be useful for clinical applications to provide the start and end positions of the UCNEs that contain the rare variants associated with their 45 IRD genes in Supplementary Table 6.

Additional functional genomic annotations, genic features following those of the original UCNE paper, and the distance to the TSS of these 45 target disease-associated genes have been incorporated in (new) Supplementary Table 5. The start and end positions of the UCNEs that contain the rare variants have also been indicated in new Supplementary Table 7.

12) A total of 724 target genes were assigned to 1,487 UCNEs that displayed candidate cis-regulatory activity. Given the interest in using UCNEs to help identify potential pathogenic mutations that lead to IRDs, can the authors note in the Results section how many of the 724 target genes are IRDs.

We thank the reviewer for this important point. From the total of 724, a total of 27 genes are annotated as IRD genes, of which (interestingly) 23 were kept as found to be expressed in the retina. This has been clarified in the Results section (line 166-168).

13) In the Discussion on page 15 line 259, can the authors clarify if variation found in UCNEs were only associated with rare disease or also with common diseases.

We have clarified that variation found in UCNEs has only been associated with rare diseases (line 247).

Minor edits:

1) In abstract, the authors might consider changing the words "rare eye diseases" on lines 20 and 22 to "rare retina degeneration diseases", and on lines 88-89.

We thank the reviewer for this comment. However, we consider that rare eye diseases is a more suitable term for our purpose as it includes diseases primarily characterized by stationary and non-progressive phenotypes such as North Carolina Macular Dystrophy and fovea hypoplasia.

2) In the Introduction on line 49, there seems to be a typo in the number of UCNE regions reported. 4,135 UCNE regions is supposed to be 4,351, based on the original paper (https://academic.oup.com/nar/article/41/D1/D101/1057253).

We have corrected this typo accordingly.

3) In the introduction on lines 75-76, these references: Lyu et al., Cell Reports 2021, PMID: 34788628, and Zhang et al., Trends in Genetics 2023, PMID: 37423870, could be added to the following sentence to provide additional: "This cellular complexity is the result of spatiotemporally controlled gene expression programs during retinal development”.

We have now included these relevant references.

4) On lines 77 and 84, I would write IRD as plural: IRDs.

This has been amended in the new version.

5) In introduction on lines 89-90, it can be further added that you provide experimental support for an ultra rare SNV in a cis regulatory UCNE affecting PAX6.

We have explicitly stated that we provided functional evidence for this UCNE.

6) On line 98, the authors refer to Figure 1A when noting that the integration of UCNEs with multi-omics data in human retina allows to evaluate the regulatory capacity of UCNEs across the major developmental stages of human retina. However panel A in figure 1 does not seem to show this point. It shows the comparison of elements across species. Please make appropriate changes to the main text and figure legend.

We have made the appropriate changes and located the reference to this figure in a more relevant part of the text (line 87).

7) Please explain what the names appended to the gene symbols in the first column "UCNE ID" in Supplementary Tables 1 and 2 refer to.

We have clarified what these refer to.

8) On line 145, can the authors clarify what they mean by "active gene expression in the retina". Is this just another way of referring to genes found to be expressed in retina? If so, it might be clearer just to write: "We annotated the identified active UCNEs to assign them potential target genes and thus assess their association with genes expressed in the retina"

We indeed meant genes found to be expressed in retina. As this phrasing might not be completely clear, we have now changed to the wording suggested by the reviewer.

9) One line 156, I would write "regulation of transcription" as listed in the gene ontology terms in Figure 2C, instead of "regulation of gene expression". The authors might want to add this to the Discussion. Can the authors include the full gene set enrichment results from Enrichr in a supplementary table at Padj<0.05 since only the top gene sets are shown in Fig. 2C (at P<1E-13)?

We changed the term to “regulation of transcription” to keep the nomenclature consistent to that of Figure 2C. We have also provided a full gene set enrichment from Enrichr as well (Supplementary Table 3).

10) On page 12, line 214, what does "EH38E1530321" Stand for? It seems to specify a distal enhancer-like signatures in bipolar neurons, but I couldn't find this ID in any database.

This refers to the identifier of ENCODE:

https://screen-v2.wenglab.org/search/?q=EH38E1530321&assembly=GRCh38

Additionally, when mentioning a specific UCNE, VISTA enhancer, or ENCODE cCRE (as in this case), we have explicitly included its corresponding identifier.

11) In the Methods section on lines 391-392, can the authors give some high-level explanation of the unconstrained integration method: "Single-nucleus RNA-seq of the same tissue and timepoints (GSE183684) were integrated using the unconstrained integration method". Also, can they comment on how retinal cell class identities were assigned (line 393). Was it based on known markers or on previous identification of cell classes and highly variable genes between clusters?

We have included a high-level explanation of the unconstrained method in the Methods section (lines 387-392). We also clarified that the assignment of cell class identities was based on known markers (line 394).

12) In the integration of UCNEs with bulk and single cell ATAC-seq and Dnase hypersentitivity regions, can the authors note in the Methods section (lines 400-404) what peak width was used to test for overlap with the UCNEs.

We have specified the peak widths that were used for the overlap with UCNEs (lines 397 and 403).

13) On line 436, the word 'and' is missing between "(SNVs, and indels < 50bp)" and "large structural variants".

This has been corrected.

14) On lines 443-444, please provide references to the computational tools listed. Please note if default settings/parameters were used.

We have specified that default parameters were used in the analysis (line 464).

15) In the following sentence in the Methods section on lines 447-449, it is not clear in the Results section how this was used in the flow of the analysis, and how many cases showed such a similarity in phenotype: "For each candidate variant, we compared the similarities between the participant phenotype (HPO terms) and the ones known for its target gene through literature search and clinical assessment by the recruiting clinician when possible." Can the authors add more detail to the Results section.

As the evaluation of the candidate variants was essentially performed on a case-by-case basis, we opted to include a rather general description of the workflow, which indeed included a comparison of the reported phenotypes with those associated with the putative target gene. An example of such comparison has been included in the Results (lines 186-187) section regarding the cases for which a NCMD-like phenotype was suspected.

16) It would be helpful to have a table that describes the different omics datasets used in the paper, with some basic annotations (tissue type, sample size, reference).

This has now been incorporated in Supplementary Table 11.

17) Can the authors add references to their sentence in the Discussion on page 17 lines 299-301: "As has been shown before, the phenotype caused by a coding mutation of a developmental gene can be different from the phenotype caused by a mutation in a CRE controlling spatiotemporal expression of this gene."

We clarified that this phrase referred to the case of PRDM13, for which bi-allelic coding pathogenic variants are linked to hypogonadotropic hypogonadism and perinatal brainstem dysfunction in combination with cerebellar hypoplasia (Whittaker et al., 2021), while non-coding variants within its regulatory regions are associated with NCMD.

Reviewer #2:

Minor discretionary suggestions for improving the presentation:

1) Wherever a specific UCNE, Vista enhancer or ENCODE cCRE is mentioned, the element should be identified by name or accession code: For instance (Iine 212): "this variant is located within a UCNE (PAX6_Veronica) that is catalogued as a cCRE in ENCODE (EH38E1530321)". UCNE names are particularly important, because they are systematically used as identifiers in the supplemental Tables and thus would enable the reader to easily find additional information about the element mentioned in the main text.

We have now explicitly included all corresponding identifiers throughout the text.

2) I also recommend inclusion of the UCNE, Vista and ENCODE cCRE tracks in all genome browser screen shots. The UCNE track is currently included only in Figure 1. Vista and ENCODE cCRE tracks are missing in all browser views.

We have now included UCNE, VISTA, and ENCODE cCREs tracks in the main genome browser figures (Figures 1 and 4).

3) Supplementary Table 6: It would be useful to indicate for each variant, the type of ophthalmological disorder (Table S5, column C) it is associated with.

We agree this is a relevant point. However, due to limitations in the (bulk) export of clinical information from the protected Research Environment of Genomics England, inclusion of this type of information is not feasible.

4) Fig S2 and supplementary Table 3 are not referred to in the main Text.

We have corrected this and updated the figure and table accordingly.

5) Supplementary Table 8: The Table caption should be expanded.

The contents of each column should be explained. For instance, column F: what means Homo_sapiens|M01298_1.94d|Zoo_01|2337? Where does this information come from, what data and software resources were used?

We have expanded the caption of this table to clarify this output, which is derived from the QBiC-Pred tool, a software used for predicting quantitative TF binding changes due to nucleotide variants.

6) Line 401 probable typo: 103-105 days (103-125?)

Indeed, this typo has now been corrected.

Reviewer #3:

1) Given that UCNE only accounts for a small fraction of gene regulatory elements, this study is likely with low sensitivity in terms of identifying potential regulatory mutations. Although one would expect that variants in UCNE are more likely to be pathogenic, it is hard to extrapolate from the results to assess the contribution of gene regulatory variant to the disease.

We agree that restricting our analysis to these particular regions is one of the limitations of the study, as stated in the Discussion section (line 304-311). However, one of our main aims was to provide a strategy to reduce the search space for pathogenic variants with a potential regulatory effect. Given the substantial body of literature supporting a regulatory role for these regions and, particularly, the availability of already-existing functional data, we considered that this set of regions could represent a suitable target for such analysis. Indeed, the features evaluated, and the methods presented in this study could be extrapolated and applied in other settings involving other candidate regulatory regions and/or tissues of interest, and their associated disease-phenotypes, for which, in any case, the overall contribution of regulatory pathogenic variation to disease might vary greatly.

2) I am wondering how many UCNE overlaps with open chromatin regions specific to the fetal retina and how many UCNE overlaps with adult only. Are UCNEs enriched for developmental genes? If so, how many patients are due to developmental defect?

We have now integrated into our analysis epigenetic measurements in adult retina, in particular the candidate cis-regulatory elements nominated by Cherry et al. PNAS 2020 (PMID: 32265282) based on accessible chromatin and enrichment for active enhancer-related histone modifications in adult human retina. Details about the integration of this dataset as well as the results and their corresponding interpretation have been incorporated in the Methods (lines 372-374), Results (115-117; Supplementary Table 2), and Discussion (lines 271-273) sections accordingly. In particular, out of the 111 UCNEs identified to display the active enhancer mark H3K27ac, 33 were found to maintain this signature at adult stage. Regarding the specific question from the reviewer, the majority of UCNEs overlapping with open chromatin regions are specific to the fetal retina (1,346), with only 7 UCNEs overlapping with open chromatin regions exclusively in adult state. This indeed further supports the major role of the identified candidate cis-regulatory UCNEs in the regulation of developmental gene expression programs, which was already suggested by the Gene Ontology enrichment analysis performed using the set of UCNE target genes as input (Figure 2C; new Supplementary Table 3). As far as the number of patients with development defects that were included in this study, these included: corneal abnormalities (n=62), Leber congenital amaurosis (n=142), ocular coloboma (n=111), developmental foveal and macular dystrophy (n=230), developmental glaucoma (n=94), anophthalmia or microphthalmia (n=120).

3) I am wondering if the 431 ultrarare variants found in the UCNEs is higher than expected. This can be tested by comparing patients without visual disorders.

Although it is indeed a relevant point, retrieving sequencing data from patients without visual disorders is not feasible for us. As it is a restricted research environment, we are only allowed to query sequencing data corresponding to participants enrolled within the framework of our specific sub-domain, namely “Hearing and Sight”, and therefore evaluating additional patients from other sub-domains is not doable. Based on previous studies and our observations, common variants are precisely the ones depleted within UCNEs, while ultrarare variation seems to occur at levels comparable to those observed elsewhere in the genome. Therefore, it is reasonable to speculate that this amount of ultrarare variants is not higher than expected as compared to patients without visual disorders. To further demonstrate the high intolerance of UCNEs to common variation, we have included an evaluation of the distribution of genome-wide residual variation intolerance score (gwRVIS) values compared to a set of randomly selected genomic regions in a human reference cohort (lines 173-178; 487-495; Fig. 3C). Additionally, to address this question further, we have also generated allele frequency distributions for all variants retrieved within a selection of 25 disease-gene associated loci and their corresponding UCNEs in order to assess the specificity of the overlap between rare variants and UCNE regions (lines 181-182, 496-501; Figure S2).

4) It seems that the ultrarare variants listed in sup table 6 are more abundant in a small number of genes. Is this due to the number/size of UCNEs is larger in these genes?

Indeed, the clustering of UCNEs in genomic regions containing genes coding for transcription factors and developmental regulators (e.g., OTX2, PAX6, ZEB2) seems to be one of their intrinsic properties, hence the observed enrichment for a small number of genes. One reason can be that these neighboring UCNEs cooperate to achieve higher degrees of tissue-specific regulatory accuracy needed for these genes.

5) The variant in the putative Pax6 gene regulatory element is intriguing. It would be much more informative if the enhancer with and without the variant is tested in parallel in fish.

That is a very relevant point. We have now tested the effect of this SNV in the UCNE on the reported expression pattern using the same experimental setup that we used for testing the wild-type construct, namely transgenic enhancer zebrafish assays. However, we could not obtain conclusive results, most likely due to the limitations posed by testing these regions outside their native genomic context. We have incorporated the details, results, and interpretation of the assays performed mutant construct in the Methods (lines 525-527; Supplementary Table 12), Results (lines 235-238; Supplementary Table 10), and Discussion (lines 350-353) sections.

6) (optional) it would be quite interesting to check the phenotype in fish or mice with the element repressed via technique such as CRISPRi.

Indeed, we fully agree that CRISPR-based techniques would be the ideal experimental approaches to further validate the functionality of the PAX6-associated UCNE and the identified variant in their native genomic context. Conducting these detailed and focused mechanistic studies is, however, beyond the scope of the present work, for which the main focus was the identification and functional annotation of ultraconserved cCREs.

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Referee #3

Evidence, reproducibility and clarity

In the report, the authors combined bulk and single cell multi-omics data from the retina to identify ultraconserved noncoding elements (UCNE) that might function as regulatory elements based on chromatin openness, DNAse sensitive regions, and histone marks. The candidate UCNEs are intersected with whole genome sequencing data from 3.220 patients with rare eye disease to identify potential rare variants that might affect the activity of UNCE. The goal of the project is intriguing.

My comments are listed below:

1. Given that UCNE only accounts for a small fraction of gene regulatory elements, this study is likely with low sensitivity in terms of identifying potential regulatory mutations. Although one would expect that variants in UCNE are more likely to be pathogenic, it is hard to extrapolate from the results to assess the contribution of gene regulatory variant to the disease.
2. I am wondering how many UCNE overlaps with open chromatin regions specific to the fetal retina and how many UCNE overlaps with adult only. Are UCNEs enriched for developmental genes? If so, how many patients are due to developmental defect?
3. I am wondering if the 431 ultrarare variants found in the UCNEs is higher than expected. This can be tested by comparing patients without visual disorders.
4. It seems that the ultrarare variants listed in sup table 6 are more abundant in a small number of genes. Is this due to the number/size of UCNEs is larger in these genes?
5. The variant in the putative Pax6 gene regulatory element is intriguing. It would be much more informative if the enhancer with and without the variant is tested in parallel in fish.
6. (optional) it would be quite interesting to check the phenotype in fish or mice with the element repressed via technique such as CRISPRi.

Significance

Given that UCNE only accounts for a small fraction of gene regulatory elements, this study is likely with low sensitivity in terms of identifying potential regulatory mutations. Although one would expect that variants in UCNE are more likely to be pathogenic, it is hard to extrapolate from the results to assess the contribution of gene regulatory variant to the disease.

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Referee #2

Evidence, reproducibility and clarity

Starting with a comprehensive analysis of multi-omics data, the authors identify a subset of ultra-conserved non-coding elements (UCNEs) likely to play a role in retinal development. Restricting subsequent analyses to these genomic regions, they identify ultra-rare mutations associated with eye disease, using data from the 100k genome project. They then follow-up on one newly discovered, disease associated UCNE and a presumably causal mutation within this UCNE. The follow-up experiments involve fine mapping of the spatiotemporal expression pattern of a UCNE-driven reporter gene in zebra fish, as well as a re-examination of the disease phenotype in carriers of the mutation.

The computational pipeline used for prioritization of UCNEs is sound. The evidence supporting the claim that the identified ultra-rare SNV is causal is highly convincing. This study also constitutes proof of concept for a novel methodology to search for causal disease associated mutations in the nowadays still under-investigated non-coding part of the genome.

The paper is clearly written. Methods are described in enough detail to allow for reproduction of the results. Overall, this study is of high scientific quality, self-contained, and complete. Publication in a peer-reviewed journal should not be delayed by additional, perhaps interesting but non-essential experiments.

However, if the authors intend to undertake similar studies in the future, I would recommend to carry out the reporter-gene assays in zebrafish with both the wild-type and the mutant version of the UCNE. Comparison of the spatiotemporal expression patterns of the two alleles could provide valuable insights into the mechanism of action of the deleterious mutation under investigation.

Minor discretionary suggestions for improving the presentation:

Wherever a specific UCNE, Vista enhancer or ENCODE cCRE is mentioned, the element should be identified by name or accession code: For instance (Iine 212):

"this variant is located within a UCNE (PAX6_Veronica) that is catalogued as a cCRE in ENCODE (EH38E1530321)"

UCNE names are particularly important, because they are systematically used as identifiers in the supplemental Tables and thus would enable the reader to easily find additional information about the element mentioned in the main text.

I also recommend inclusion of the UCNE, Vista and ENCODE cCRE tracks in all genome browser screen shots. The UCNE track is currently included only in Figure 1. Vista and ENCODE cCRE tracks are missing in all browser views.

Supplementary Table 6: It would be useful to indicate for each variant, the type of ophthalmological disorder (Table S5, column C) it is associated with.

Fig S2 and supplementary Table 3 are not referred to in the main Text.

Supplementary Table 8: The Table caption should be expanded. The contents of each column should be explained. For instance, column F: what means Homo_sapiens|M01298_1.94d|Zoo_01|2337? Where does this information come from, what data and software resources were used?

Line 401 probable typo: 103-105 days (103-125?)

Significance

This work is of interest to different research communities: Biomedical researchers working on neural disorders, human geneticists engaged in GWAS studies, computational biologists trying to make sense out of omics data, molecular biologists exploring the "dark matter" of the genome, and finally the small community tackling the enigma of UCNEs. As with many omics papers, the most valuable parts of this study are in the supplemental tables, in particular tables 1,4, and 6. It can be hoped that some prospective readers will follow up on the leads presented in these tables.

The detailed computational and experimental characterization of a likely causal ultra-rare disease associated mutation may serve as a guiding and motivating example for medical geneticists working on other syndromes.

Back to UCNEs: They are enigmatic entities, which so far have largely resisted molecular and physiological characterization. It took 10 years to finally uncover a phenotype in ko mice missing one or several UCNEs, after the surprising initial observation that such mice were viable and fertile. The difficulties in studying the function of UCNEs may be due to their conjectured pleiotropic activity in different cell types at different developmental stages, their apparent cooperative interactions with many other control elements (limiting the power of reporter gene assays with single elements), and their putative involvement in morphogenetic processes (minimizing the relevance of epigenetic data collected from cell lines). In view of these considerations, I consider UCNE research starting from human disease phenotypes more promising, than ab initio approaches using reverse genetics in model organisms.

The impact of this paper is potentially very high. Note the following statement in the paper:

"For each instance for which only the UCNE variant remained as candidate, we placed a clinical collaboration request with Genomics England."

We thus can expect more exiting stories from the same team. The strategy and computational pipeline introduced here are of course applicable to other congenital diseases, and it can reasonably be hoped that researchers inspired by this study will apply components of the methodology in other contexts. The prioritization of UCNEs in studying the "dark matter" of the genome and the "missing heredity" would likely lead to new insights into the function of these enigmatic elements and the reasons for their extreme conservation.

My background: I'm a bioinformatician with first training in molecular genetics. My research focus is on gene regulation: promoters, enhancers, transcription factor binding sites. I also made some contributions to the UCNE field, having co-developed UNCEbase with Slavica Dimitrieva. On the other hand, I don't claim to be an expert in medical genetics, and more specifically, I know very little about eye diseases and retinal development.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript entitled "Multi-omics analysis in human retina uncovers ultraconserved cis-regulatory elements at rare eye disease loci", Soriano et al. explore the role of ultraconserved noncoding elements (UCNEs) as candidate cis-regulators (cCREs) in developing and adult human retina by integrating UCNEs with multi-omic data from fetal and adult human retina. They further examine the potential contribution of UCNEs to rare eye diseases by testing for rare variants that fall in UCNEs that are potentially active in retina in patients with inherited retina degeneration diseases (IRDs), using whole genome sequencing (WGS) data from Genomics England. This work is based on the assumption that genomic regions under strong evolutionary constrain are good predictors of important functionality. The authors use 4,135 UCNEs identified in Dimitrieva and Bucher, 2013, defined as sequences with more than 95% identity between human and chicken with >200bp in length. By integrating bulk tissue RNA-Seq, single cell (sc)RNA-Seq, DNAase-Seq, scATAC-Seq and ChIP-Seq from retinal tissues from different developmental stages and adulthood with the 4,135 UCNEs, they identified one third of UCNEs (1,487) that may be associated with various retinal development stages. Using bioinformatic approaches they identify potential target genes for 724 UCNEs that may be regulated in cis. Based on ATAC-Seq, the authors show that 834 UCNEs fall in open chromatin regions, and of these 111 have active histone markers, supporting an active functional role for the identified UCNEs. The authors demonstrate an application of this approach in identifying potential pathogenic noncoding variants for rare eye diseases. Using WGS from 100,000 Genomes project the authors identify 45 UCNEs that were bioinformatically associated with mendelian IRD genes that contain rare variants, proposing potential solutions for unsolved cases. They demonstrate the utility of their analysis by highlighting an ultra-rare SNP they identified in a UCNE candidate CRE located upstream of PAX6 that belongs to a family of genes with foveal abnormalities. They confirm the effect of the UCNE 150k upstream of PAX6 on gene expression in the eye, forebrain and neuronal tube using an enhancer reporter assay in Zebrafish.

The authors demonstrate a strategy for narrowing down the genomic space to putative functional noncoding regions involved in development and that may contribute to rare disease. This work that integrates various genomic modalities is of broad interest and can be applied to other diseases and tissues. There are several points that should be addressed to assess the robustness of the results and strengthen the conclusions of the paper, and in some places to better clarify the analyses conducted.

Major edits:

1. In the introduction the authors list 4 databases of ultra-conserved non-coding elements, and choose to work with the UCNEbase that detects UCNE regions by comparing human and chicken, as they state that it is one of the most comprehensive resources. Can the authors comment on the extent of overlap of UCNE regions identified in this database compared to other databases. It would also be helpful to add an explanation in the Introduction on the advantage of comparing the human genome to the chicken genome, e.g., is chicken the most distant vertebrate with a high quality genome, or another reason? And can the authors comment on the extent of conservation of the UCNEs compared to other species - in the UCNEbase paper, orthologues for the UCNEs are identified in 18 vertebrate species including reptiles, amphibians and fish.
2. The authors briefly describe how potential target genes were assigned to UCNEs in the Method section (section begins on page 21, line 407 and on lines 379-381). They note that they used the Genomic Regions Enrichment of Annotations Tool (GREAT). Can the authors provide additional details on what this method does and also provide a high level sentence in the Results section on page 8, lines 144-146, on how target genes were assigned to UCNEs, as well as in the Discussion on page 16, line 289. Based on the Methods description on lines 409-414, a UCNE was associated with any gene within 1Mb of the UNCE that was expressed in retina and whose curated regulatory domains overlapped the UNCE. Is this correct? How were the regulatory domains curated (line 411-412)? Can the authors please clarify this important point.

There are other approaches for linking putative transcriptionally active genomic regions with target genes in specific tissues or cell types through correlation analysis of ATAC-seq peaks (chromatin accessibility) and gene expression in RNA-seq data. A commonly used peak-to-gene linkage method is implemented in ArchR (Granja et al, 2021, PMID: 33633365). The authors note that they used scATAC-seq gene scores and scRNA-seq gene expression to further characterize the proposed target genes of UCNEs. It is not clear what the authors mean by "scATAC-seq gene scores". Please define "scATAC-seq gene score" and add a reference. Can the authors compare the target gene mapping to UCNEs using GREAT and gene expression filtering to that using peak-to-gene linkage based on retina tissue or single cell ATAC-seq and RNA-seq data?

For gene expression filtering (line 419) the authors quantify transcript expression of retina from FASTQ samples using the Kallisto method, and then note that they did the filtering on gene expression levels (TPM<0.5). Please add details on how you went from transcript expression levels to gene expression levels for the filtering, or was the filtering performed at the transcript level?<br /> 3. The authors use the words "active UCNE", first mentioned in the Results on line 144. Can the authors define what they mean by "active UCNE". What information/evidence is used to ascertain that a UCNE is indeed active. Overlap of a UCNE with a chromatin accessibility region from ATAC-seq or DNAase-Seq would only suggest that the UCNE may be active. Intersection with enhancer activity measured with in vivo enhancer reporter assays in transgenic mice from the VISTA enhancer browser provides stronger evidence of transcriptional activity. The authors might want to distinguish between putatively actively and active based on the functional support.<br /> 4. The authors assessed the significance of depletion of common variation (MAF>1%) in the UCNE regions compared to a background of randomly selected genomic regions. In generating the random distribution of regions, did the authors match on the distribution of distances of the UNCEs to the TSS of genes in the randomly selected regions? This may be a confounder.

Also, in the legend of Figure 3, lines 191-192, it is stated: "Variant population frequencies within putative retinal UCNEs normalized to a background composed of randomly selected sequences (see Methods).", but we did not find a description of this analysis in the Methods section.<br /> 5. In regards to intersecting UCNEs with epigenetic marks that detect active or repressed enhancers in retina, the authors used data from Aldiri et al 217 that measured epigenetic changes during retinal development. Did this dataset contain epigenetic measurements in adult retina? The authors might want to consider using the epigenetic marks/ChIP-seq data from adult human retina in Cherry et al. PNAS 2020 (PMID: 32265282)<br /> 6. With respect to the examination of rare variants that may be associated with rare eye disease in retina active UCNEs, for the interpretation of the results, it would be helpful to get more information on the distribution of rare variants found in UCNEs associated in this study to known IRD genes in all affected individuals in families, if this information is available in the 100,000 Genomes Project.<br /> 7. In the Methods section on lines 450-451, the authors mention that they performed variant screening of retinal disease genes, referencing the Genomics England Retinal Disorder panel and Martin et al., 2019. Can the authors add to the Methods and Results sections how many retinal disease genes were initially tested. Also, to get a sense of the specificity of the overlap of rare variants in the 100k Genome Project cohort with UNCE regions, it would be informative to show a distribution of the number of rare variants <0.5% that passed the filtering in gnomAD per eye disease gene before the overlap with UNCEs.<br /> 8. The authors found "an ultrarare SNV (chr11:31968001T>C) within a candidate cis-regulatory UCNE located ~150kb upstream of PAX6. This variant was found in four individuals of a family segregating autosomal dominant foveal abnormalities". They tested the functional effect of this element with a reporter assay in zebrafish and found that the UNCE affects expression in the eye, forebrain, and neural tube. It would add further value if the authors were to test the effect of this SNV in the UCNE on the reporter expression pattern, using CRISPR/cas9?<br /> 9. The authors found rare variants in UCNEs linked to 45 IRD genes. Can the authors provide additional information on the functional genomic annotations of these UCNEs and distance to the target genes. The UCNEs were characterized with respect to their genic features in the original paper (UCNEbase, Dimitrieva et al., NAR, 2013), e.g., intergenic, intronic and 3'/5' UTR. Also, it would be useful for clinical applications to provide the start and end positions of the UCNEs that contain the rare variants associated with their 45 IRD genes in Supplementary Table 6.<br /> 10. A total of 724 target genes were assigned to 1,487 UCNEs that displayed candidate cis-regulatory activity. Given the interest in using UNCEs to help identify potential pathogenic mutations that lead to IRDs, can the authors note in the Results section how many of the 724 target genes are IRDs.<br /> 11. In the Discussion on page 15 line 259, can the authors clarify if variation found in UNCEs were only associated with rare disease or also with common diseases.

Minor edits:

1. In abstract, the authors might consider changing the words "rare eye diseases" on lines 20 and 22 to "rare retina degeneration diseases", and on lines 88-89.
2. In the Introduction on line 49, there seems to be a typo in the number of UCNE regions reported. 4,135 UCNE regions is supposed to be 4,351, based on the original paper (https://academic.oup.com/nar/article/41/D1/D101/1057253).
3. In the introduction on lines 75-76, these references: Lyu et al., Cell Reports 2021, PMID: 34788628, and Zhang et al., Trends in Genetics 2023, PMID: 37423870, could be added to the following sentence to provide additional: "This cellular complexity is the result of spatiotemporally controlled gene expression programs during retinal development,"
4. On lines 77 and 84, I would write IRD as plural: IRDs.
5. In introduction on lines 89-90, it can be further added that you provide experimental support for an ultra rare SNV in a cis regulatory UCNE affecting PAX6.
6. On line 98, the authors refer to Figure 1A when noting that the integration of UCNEs with multi-omics data in human retina allows to evaluate the regulatory capacity of UCNEs across the major developmental stages of human retina. However panel A in figure 1 does not seem to show this point. It shows the comparison of elements across species. Please make appropriate changes to the main text and figure legend.
7. Please explain what the names appended to the gene symbols in the first column "UCNE ID" in Supplementary Tables 1 and 2 refer to.
8. On line 145, can the authors clarify what they mean by "active gene expression in the retina". Is this just another way of referring to genes found to be expressed in retina? If so, it might be clearer just to write: "We annotated the identified active UCNEs to assign them potential target genes and thus assess their association with genes expressed in the retina"
9. One line 156, I would write "regulation of transcription" as listed in the gene ontology terms in Figure 2C, instead of "regulation of gene expression". The authors might want to add this to the Discussion. Can the authors include the full gene set enrichment results from Enrichr in a supplementary table at Padj<0.05 since only the top gene sets are shown in Fig. 2C (at P<1E-13)?
10. On page 12, line 214, what does "EH38E1530321" Stand for? It seems to specify a distal enhancer-like signatures in bipolar neurons, but I couldn't find this ID in any database.
11. In the Methods section on lines 391-392, can the authors give some high-level explanation of the unconstrained integration method: "Single-nucleus RNA-seq of the same tissue and timepoints (GSE183684) were integrated using the unconstrained integration method". Also, can they comment on how retinal cell class identities were assigned (line 393). Was it based on known markers or on previous identification of cell classes and highly variable genes between clusters?
12. In the integration of UCNEs with bulk and single cell ATAC-seq and DNase hypersentitivity regions, can the authors note in the Methods section (lines 400-404) what peak width was used to test for overlap with the UCNEs.
13. On line 436, the word 'and' is missing between "(SNVs, and indels < 50bp)" and "large structural variants".
14. On lines 443-444, please provide references to the computational tools listed. Please note if default settings/parameters were used.
15. In the following sentence in the Methods section on lines 447-449, it is not clear in the Results section how this was used in the flow of the analysis, and how many cases showed such a similarity in phenotype: "For each candidate variant, we compared the similarities between the participant phenotype (HPO terms) and the ones known for its target gene through literature search and clinical assessment by the recruiting clinician when possible." Can the authors add more detail to the Results section.
16. It would be helpful to have a table that describes the different omics datasets used in the paper, with some basic annotations (tissue type, sample size, reference)
17. Can the authors add references to their sentence in the Discussion on page 17 lines 299-301: "As has been shown before, the phenotype caused by a coding mutation of a developmental gene can be different from the phenotype caused by a mutation in a CRE controlling spatiotemporal expression of this gene."

Significance

General assessment: This is the first study to our knowledge to integrate ultraconserved noncoding elements (UNCEs) with a range of multi-omic data to identify UNCEs that may be active and their target genes in a specific tissue, in this case human retina. They also experimentally test one of the UNCE predicted to affect the expression of a given gene in retina (and potentially other tissues) in Zebrafish and confirm its transcriptional activity in the eye, to provide some functional support to their strategy. This study also demonstrates the potential value of inspecting UCNEs in prioritizing pathogenic mutations for rare disease. One limitation is the lack of statistical significance assessment of the potential causal effect of a rare variant found in a UCNE on the expression of its predicted target gene, which is a rare eye disease gene, since the linkage of the UCNE to the disease gene was performed based on bioinformatic analysis of multi-omic data. Experimental testing of the effect of some of these mutations on their target gene expression could provide additional support.

Advance: This study addresses an important unsolved problem in the field of human genetics and rare diseases, namely the challenge of identifying pathogenic mutations that lead to rare Mendelian diseases, in particular, in noncoding regions in unsolved cases. This is the first study to consider UCNEs together with tissue or cell type specific expression, epigenetics and chromatin accessibility in detecting pathogenic mutations for retina degeneration diseases. See for example Ellingford et al., Genome Medicine 2023 (PMID: 35850704). Their demonstration of rare variants in UCNE associated with inherited retinal degeneration diseases in patients with IRD in the 100k Genomics Project suggests that the role of UCNEs in disease should be further investigated and functionally tested. This work could have important clinical implications, and also proposes a strategy for integrating UCNEs with multi-omic and genomic data.

Audience: This work will be of interest to the human genetics and genomics community, in particular to researchers interested in uncovering the genetic basis and causal mechanisms of rare diseases, and to scientists interested in clinical applications of genetic variation. This work will also be of interest to scientists interested more broadly in understanding the regulatory effects of the noncoding regions in the genome.

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Reply to the reviewers

Reviewer #1:

1. If doable, image dynein and dynactin simultaneously in the Halo-DYNC1H1/DCTN4-SNAP iNeurons. Co-movement of dynein and dynactin towards the somatodendritic compartment and their separate movement in the anterograde direction along the axon would provide the most convincing evidence for the key claims of the manuscript.

Please see the planned revision section for our response

Reviewer #2:

Major comment (requires additional experimentation)

1. While the data presented do certainly suggest that dynein and Lis1 are transported anterogradely on separate vesicular cargoes from dynactin and Ndel1, the study would be much stronger if supported by dual imaging of dynein and dynactin to prove that these proteins do indeed move in association with separate vesicular populations. I would like to see dual-color kymograph traces showing that the proteins move independently. The authors should be able to accomplish this using their dual Halo-DYNC1H1/DCTN4-SNAP hESC line. To acquire and analyze this data might take several months, but it would greatly strengthen this paper. If the authors do this experiment, they may also be able to address the mechanism of reversal of anterograde cargoes which they speculate about in the Discussion, which would add even more interest and insight.

Please see the planned revision section for our response

Minor comments (addressable without additional experimentation)

1. The authors deduce that 1-4 Halo fluorochromes corresponds to 1-2 dynein molecules. This implies that the cells are homozygous for the Halo tag, but I do not see this addressed explicitly. The authors should state explicitly whether the lines generated for their study are heterozygous or homozygous for the tag. If the cells are heterozygous, which would seem most likely, then they may be underestimating the number of dyneins per spot and should take this into account.

We have added whether lines are homozygous or heterozygous to the manuscript. We also include a new Supplementary Figure panel (Fig S6) showing the genotyping data. In summary, all lines are homozygous except for PAFAH1B1-Halo (hESCs) which is heterozygous.

1. Why are the moving spots lower in intensity than the NEM-treated static spots. It appears to suggest that they may be associated with different structures. This should be clarified and discussed.

Our data suggest that the fast-moving spots have fewer dyneins than NEM treated static spots. We suggest this is because the fast-moving cargos are smaller than the average cargo and therefore have fewer dyneins on them. This is also supported by the smaller number of dyneins reported previously on endosomes as compared to the large lysosomes. We have clarified this in the discussion (page 7-8).

1. The authors state in the Results that most of the dynein spots were diffusing, often along microtubules, but they do not visualize microtubules so how do they know this? They may need to remove the phrase "often along microtubules".

This has been removed.

1. At the end of the Introduction the authors state that their data "allow us to understand how the dynein machinery drives long-range transport in the axon". This is an overstatement. The "how" in this sentence is not addressed in this study.

We have softened the sentence by adding the phrase “better understand”.

1. The conclusion that dynein binds to cargos stably throughout their transport along the axon is based on measurements of the fastest moving cargoes but the authors do not provide data on the distribution of velocities for the entire population of retrograde cargoes. It is not valid to extrapolate the behavior of a small number of cargoes to the entire population. The average may be much slower than the fastest cargoes. Moreover, even for the fastest organelles the authors cannot say that the dynein is stably bound because they did not track single cargoes and thus do not know that the cargoes moved continuously in one single bout of movement for 500 µm; it is possible that the cargoes moved in multiple consecutive bouts interrupted by brief pauses and dynein motors may have exchanged between bouts.

We have added a section to the discussion to highlight that other cargos may behave differently from the fastest ones (page 7). We have also clarified the assumptions that lead us to expect a slower arrival time of the first signal (page 5).

1. The authors say that "it is clear that at least some dyneins remain on cargoes throughout their transport along the axon". As explained above, the data do not prove this so this statement should be removed.

We have softened this sentence from “it is clear” to “our results suggest” and explained in more detail why we make this conclusion

1. The authors note that most of the dynein spots were not moving processively and state that this is consistent with prior studies showing that only a subset of dynein is actively involved in transport. However, as they note elsewhere, dynein is both motor and cargo and most axonal dynein is transported at slow average velocities so maybe they should be more explicit about what they mean by "involved in transport".

We have clarified we mean fast axonal transport and thank the reviewer for highlighting this point.

1. When the authors note that most of the dynein in axons is transported in the slow component of axonal transport, they should also cite the work of Pfister and colleagues who were the first to show this (PMID 8824315 and 8552592).

This was an omission on our part. The references have now been added.

1. The authors propose that dynein and Lis1 are transported together but there were significantly fewer anterogradely transported Lis1 particles than dynein particles. This should be discussed.

We have added more information to the discussion. Although we cannot rule out this effect being due to the heterozygous tagging of our LIS1 cell line, we do not witness the same decrease in events in the retrograde direction. Therefore, we believe there is a subset of anterogradely moving dynein lacking LIS1. As discussed in the manuscript, this subset may already be bound to dynactin and therefore not require LIS1.

1. For the statistical analysis, the authors should provide p values in the legends for the comparisons that are judged to be "not significant". The authors should also be consistent in how they label differences that are not significant - they mark them as "ns" in Fig. 1, but in the other figures they do not, leaving some ambiguity about whether particular comparisons were not tested or were found to be not significant. For example, in Fig. 4C the average speed of the dynactin is about 0.5 µm/s greater than for the other proteins and the spread in the data suggest that this could be significant, but no significance is indicated on the plot, implying p>0.05. It is not clear how confident we can be that there is no difference.

We have now included all p values in the figure legends and have removed the “ns” in Fig 1D. In our revised manuscript, only significant differences are highlighted in the figures.

Reviewer #3:

• if I look at the kymographs, trajectories appear rather complex, pausing, standing still, moving and everything mixed. The explanation of how actual trajectories are extracted and on what basis is very short, too short for me. I think the authors should expand this. Furthermore, I think it would be good if the authors would present, in their kymographs examples of the tracked (and also the not included) tracks. Maybe in supplementary info.

The analysis of this data used the Trackmate Fiji plugin. This tracks spots frame to frame in a movie and then outputs the data of the tracks. No data was extracted from kymographs but they were used as a graphical illustration of the moving spots. To better explain our analysis pipeline, we have expanded our methods section and have added an example of a tracked movie (Video 15) as well as highlighted the tracked spots in one kymograph example (Figure 7S).

• I found 'velocity' ill defined. I get the impression, judging from the number of points (compared to the other parameters) that the authors determine the average velocity of each individual trajectory. That is an important parameter (but should indeed be called 'trajectory averaged' velocity), but might not be the only one useful to learn from the data, where trajectories do not always appear to have constant speeds (pausing, etc.). Why do the authors not determine point-to-point velocities and plot histograms of those for all the trajectories (simply plot histograms of all the displacements between subsequent data points in trajectories)? This might provide great insight into the actual maximum velocity and the fraction of pausing or moving in opposite direction etc., providing much more molecular detail than currently extracted from the data.

The reviewer is correct. We have measured the average velocity of the spots from the beginning of the track to the end. We have clarified this in the text. Furthermore, as stated above in the revision plan, we are currently doing the additional analysis and will include it in the final revision

• I was a bit surprised to read that the authors have gone to the effort to create a dual-color labeled cell line, but did not do actual correlative two-color measurements (or at least show them). It would be so insightful to see dynein and dynactin move separately in the anterograde direction.

Please see the planned revision section for our response.

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Referee #3

Evidence, reproducibility and clarity

Fellows and coauthors present a signle-molecule study toward dynein regulation in axons. They observe that dynein in vivo makes very long runs and that regulators LIS1 and NDEL1 cotransport with dynein all the (retrograde way). Remarkably, different components of the dynein complex appear to be transported in different ways/velocities in the antorograde direction. Overall experiments are well conducted, I only have a couple of important questions regarding data analysis. Some aspects should be explained better, more steps should be shown and here and there I think the authors could, with minimal effort, obtain much more out of their data (see below). Nevertheless, I think this is an important study, on of the first single-molecule efforts to understand axonal transport in the cell (see below). Key findings are important for our understanding of dynein regulation.

My concerns:

• if I look at the kymographs, trajectories appear rather complex, pausing, standing still, moving and everything mixed. The explanation of how actual trajectories are extracted and on what basis is very short, too short for me. I think the authors should expand this. Furthermore, I think it would be good if the authors would present, in their kymographs examples of the tracked (and also the not included) tracks. Maybe in supplementary info.
• I found 'velocity' ill defined. I get the impression, judging from the number of points (compared to the other parameters) that the authors determine the average velocity of each individual trajectory. That is an important parameter (but should indeed be called 'trajectory averaged' velocity), but might not be the only one useful to learn from the data, where trajectories do not always appear to have constant speeds (pausing, etc.). Why do the authors not determine point-to-point velocities and plot histograms of those for all the trajectories (simply plot histograms of all the displacements between subsequent data points in trajectories)? This might provide great insight into the actual maximum velocity and the fraction of pausing or moving in opposite direction etc., providing much more molecular detail than currently extracted from the data.
• I was a bit surprised to read that the authors have gone to the effort to create a dual-color labeled cell line, but did not do actual correlative two-color measurements (or at least show them). It would be so insightful to see dynein and dynactin move separately in the anterograde direction.

Referee Cross-Commenting

I think we agree on the key points:<br /> - in principle, great study<br /> - quantification / tracking could go a bit further and should be explained better<br /> - manuscript / conclusions would be strengthened substantially if the authors could do some 2-color experiments to correlated dynein / dynactin movements in anterograde vs retrograde direction.

Significance

I think this is an important and exciting manuscript. As an in vivo single-molecule biophysicist with great interest in intracellular transport, I have been astonished in the lack of people trying to take single-molecule data on the motor involved, in particular neurons. I believe this is the only way to find out how transport actually works and what role motors play. Mutants is not enough, bulk data is not enough, in vitro is not enough. This is what the field needs (and many in the field do not seem to be aware of this...). Great that Fellows and coauthors took on this task and show some really exciting data. I am not an expert on their stem-cell labeling approach so cannot judge on that. The imaging seems to be done well. As discussed above, I think there might be much more in the data than the authors now get out, so I would encourage them to do some additional analysis. But overall, this effort is important and I think the conclusions will stand and provide important new insights in dynein regulation in the cell.

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Referee #2

Evidence, reproducibility and clarity

Summary - The authors use a CRISPR knock-in gene editing strategy to label endogenous dynein, dynactin (p62 or Arp11) and dynein regulators (Ndel1 and Lis1) with Halo or SNAP tags. They do this in human iPSC and ESC cell lines engineered to express doxycycline-inducible NGN2 cloned into a "safe harbor" site of the genome. They induce the cells to differentiate into iNeurons using doxycycline and image the tagged proteins in axons with single molecule sensitivity using HILO illumination. The paper is clearly written, the description of the methods is thorough, and the data and figures (including the videos) are of good quality. The use of gene editing to knock the tags into the endogenous gene loci is a superior strategy to classic overexpression strategies. The authors also make effective use of microfluidic chambers to ensure the axons are uniformly orientated and coaligned over a distance of 500µm.

Major comment (requires additional experimentation)

1. While the data presented do certainly suggest that dynein and Lis1 are transported anterogradely on separate vesicular cargoes from dynactin and Ndel1, the study would be much stronger if supported by dual imaging of dynein and dynactin to prove that these proteins do indeed move in association with separate vesicular populations. I would like to see dual-color kymograph traces showing that the proteins move independently. The authors should be able to accomplish this using their dual Halo-DYNC1H1/DCTN4-SNAP hESC line. To acquire and analyze this data might take several months, but it would greatly strengthen this paper. If the authors do this experiment, they may also be able to address the mechanism of reversal of anterograde cargoes which they speculate about in the Discussion, which would add even more interest and insight.

Minor comments (addressable without additional experimentation)

1. The authors deduce that 1-4 Halo fluorochromes corresponds to 1-2 dynein molecules. This implies that the cells are homozygous for the Halo tag, but I do not see this addressed explicitly. The authors should state explicitly whether the lines generated for their study are heterozygous or homozygous for the tag. If the cells are heterozygous, which would seem most likely, then they may be underestimating the number of dyneins per spot and should take this into account.
2. Why are the moving spots lower in intensity than the NEM-treated static spots. It appears to suggest that they may be associated with different structures. This should be clarified and discussed.
3. The authors state in the Results that most of the dynein spots were diffusing, often along microtubules, but they do not visualize microtubules so how do they know this? They may need to remove the phrase "often along microtubules".
4. At the end of the Introduction the authors state that their data "allow us to understand how the dynein machinery drives long-range transport in the axon". This is an overstatement. The "how" in this sentence is not addressed in this study.
5. The conclusion that dynein binds to cargos stably throughout their transport along the axon is based on measurements of the fastest moving cargoes but the authors do not provide data on the distribution of velocities for the entire population of retrograde cargoes. It is not valid to extrapolate the behavior of a small number of cargoes to the entire population. The average may be much slower than the fastest cargoes. Moreover, even for the fastest organelles the authors cannot say that the dynein is stably bound because they did not track single cargoes and thus do not know that the cargoes moved continuously in one single bout of movement for 500 µm; it is possible that the cargoes moved in multiple consecutive bouts interrupted by brief pauses and dynein motors may have exchanged between bouts.
6. The authors say that "it is clear that at least some dyneins remain on cargoes throughout their transport along the axon". As explained above, the data do not prove this so this statement should be removed.
7. The authors note that most of the dynein spots were not moving processively and state that this is consistent with prior studies showing that only a subset of dynein is actively involved in transport. However, as they note elsewhere, dynein is both motor and cargo and most axonal dynein is transported at slow average velocities so maybe they should be more explicit about what they mean by "involved in transport".
8. When the authors note that most of the dynein in axons is transported in the slow component of axonal transport, they should also cite the work of Pfister and colleagues who were the first to show this (PMID 8824315 and 8552592).
9. The authors propose that dynein and Lis1 are transported together but there were significantly fewer anterogradely transported Lis1 particles than dynein particles. This should be discussed.
10. For the statistical analysis, the authors should provide p values in the legends for the comparisons that are judged to be "not significant". The authors should also be consistent in how they label differences that are not significant - they mark them as "ns" in Fig. 1, but in the other figures they do not, leaving some ambiguity about whether particular comparisons were not tested or were found to be not significant. For example, in Fig. 4C the average speed of the dynactin is about 0.5 µm/s greater than for the other proteins and the spread in the data suggest that this could be significant, but no significance is indicated on the plot, implying p>0.05. It is not clear how confident we can be that there is no difference.

Referee Cross-Commenting

There seems to be agreement among all three reviewers that the authors should perform dual imaging of dynein and dynactin to prove that these proteins do indeed move together in the retrograde direction but separately in the anterograde direction. This would strengthen the study greatly.

Significance

General assessment - There are now multiple papers that have analyzed axonal transport of cargoes in iPSC-derived neurons, but this one appears to be the first to do it by tagging dynein motors and with single-molecule sensitivity. The principal conclusions are (1) that dynein is capable of long-range movement in axons and (2) that dynein moves dynein/Lis1 complexes are transported anterogradely in association with distinct cargoes from dynactin/Ndel1 complexes. The former is a modest conclusion and is entirely expected so not very impactful, but the latter is interesting and novel. The difference between the average velocities for the four proteins in the anterograde and retrograde directions is striking. All four move at similar velocities in the retrograde direction but in the anterograde direction, dynein and Lis1 move significantly faster than dynactin and Ndel1. Given these data, it is reasonable to infer that these proteins are being transported in two separate sets of cargoes. As the authors note in their Discussion, this is important because it could provide a mechanism for transporting dynein components anterogradely in a less active form that could then be activated when the components come together in the distal axon. However, I feel that one critical experiment is missing, which is to perform dual labeling of anterogradely transported dynein and dynactin in the same cells (see major comment). Without this experiment, the evidence is indirect.

Audience - If confirmed by the dual labeling experiment, the authors' conclusions would represent a conceptual and mechanistic insight into the mechanism of bidirectional transport in axons that would be of broad interest to neuronal cell biologists studying neuronal trafficking.

Expertise - This reviewer has expertise in the neuronal cytoskeleton, live imaging and axonal transport and has some experience working with iPSC-derived neurons.

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Referee #1

Evidence, reproducibility and clarity

To image dynein in the axon at a single-molecule level, Fellows et al. used neuron-inducible human stem cell lines to Halo/SNAP tag endogenous dynein components by gene editing, and visualized fluorescently labeled protein molecules in differentiated neurons in microfluidic chambers by HILO microscopy-based live imaging. Using those cutting edge technologies, the authors demonstrate that in the axon, not only dynein and dynactin but also the dynein regulators LIS1 and NDEL1 can move long distance retrogradely towards the somatodendritic compartment. They also show that dynein /LIS1 move faster than dynactin/NDEL1 in the anterograde direction, suggesting that they are delivered separately to the distal end of the axon. The approach to study subcellular motility of endogenous dynein/dynactin is creative, the data are solid. I would like to suggest one experiment to support more strongly the authors' conclusions:<br /> If doable, image dynein and dynactin simultaneously in the Halo-DYNC1H1/DCTN4-SNAP iNeurons. Comovement of dynein and dynactin towards the somatodendritic compartment and their separate movement in the anterograde direction along the axon would provide the most convincing evidence for the key claims of the manuscript.

Referee Cross-Commenting

I agree with Reviewer 2 that the authors should clarify whether the knockin lines for dynein are homozygous. I also agree with both Reviewers 2 and 3 that the authors should do more analysis of the kymographs to obtain more information.

Significance

This is an elegant study on dynein motility and transport in vivo. The experimental approaches and findings presented in this manuscript are very valuable contributions to the field of dynein/dynactin and axonal transport. The results showing that dynein/dynactin can move long-range retrogradely in the axon are in good agreement with previous findings that dynein-driven cargo transport is highly processive, and the data suggesting that dynein and dynactin/NDEL1 are trafficked separately to the distal tip of the axon provide new insights into the regulatory mechanisms for the subcellular distribution and activity of molecular motors. Together these findings provide conceptual advances for understanding axonal transport. They will be of great interest to not only scientists in the field of intracellular transport but also those in cellular neurobiology.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

REVIEW COMMENT

The article titled "The tRNA thiolation-mediated translational control is essential for plant immunity" by Zheng et al. highlights the critical role of tRNA thiolation in Arabidopsis plant immunity through comprehensive analysis, including genetics, transcriptional, translational, and proteomic approaches. Through their investigation, the authors identified a cbp mutant, resulting in the knockout of ROL5, and discovered that ROL5 and CTU2 form a complex responsible for catalyzing the mcm5s2U modification, which plays a pivotal role in immune regulation. The findings from this study unveil a novel regulatory mechanism for plant defense. Undoubtedly, this discovery is innovative and holds significant potential impact. However, before considering publication, it is necessary for the authors to address the various questions raised in the manuscript concerning the experiments and analysis to ensure the reliability of the study's conclusions.

Response: Thank you very much for your support and suggestions!

Here is Comments:

Line 64-65:

The author mentioned that 'While NPR1 is a positive regulator of SA signaling, NPR3 and NPR4 are negative regulators.' However, several recent discoveries are suggesting that it may not be a definitive fact that NPR3 and NPR4 are negative regulators. Therefore, I recommend the authors to review this section in light of the findings from recent papers and make necessary edits to reflect the most current understanding.

Response: Thank you for your feedback. Since we mainly focused on NPR1 in this study, we removed this sentence to avoid confusion. We provided additional information about NPR1 in the Introduction section to emphasize the importance of NPR1 (Line 64-68).

Line 182- & Figure 4:

The author conducted RNA-seq, Ribo-seq, and proteome analysis. Describing the analysis as "transcriptional and translational" using RNA-seq and proteome data seems not entirely accurate. Proteome data compared with RNA-seq not only reflects translational changes but may also encompass post-translational regulations that contribute to the observed differences. To maintain precision, the title of this section should either be modified to "transcriptional and protein analysis" or, alternatively, compare RNA-seq and Ribo-seq data to demonstrate the transcriptional and translational changes more explicitly.

Responses: Thank you for your suggestions. We agree with you and thus change the description accordingly throughout the manuscript.

Line 229-235 and Figure 5C:

The interpretation of Figure 5C's polysome profiling results is inconclusive. There does not seem to be a noticeable difference in polysomal fractions between the cab mutant and CAM. The observed differences in the overlay of multiple polysome fractions between cab and COM could be primarily influenced by baseline variations rather than a significant decrease in the polynomial fractions in cpg. Therefore, it is necessary to carefully review other relevant papers that discuss polysome fraction data and their analysis. By doing so, the authors can make the appropriate corrections to ensure accurate interpretations.

Responses: Thank you for your comments. We agree that the difference between cgb and COM was not dramatic visually. This is a common feature of polysome profiling assay (e.g. Extended Data Fig. 1f in Nature 545: 487–490; Fig. 1c in Nature Plants, 9: 289–301). In our case, the difference between polysome fractions was unlikely due to the baseline variation for two reasons. First, baseline variation affects monosome and polysome fractions in the same way. However, our results showed the monosome fraction of cgb is higher than that of COM, whereas the polysome fraction of cgb is lower than that of COM. Second, this result was repeatedly detected. For better visualization, we adjusted the scale of Y axis in the revised manuscript (Figure 5D).

Line 482 Ion Leakage assay:

I could not find the ion leakage assay in this manuscript, so I wonder why it is mentioned.

Response: We are sorry for the mistake. The Ion leakage data were included in previous visions of the manuscript. We removed the data but forgot to remove the corresponding method in the present version.

Materials and Methods:

To enhance the reproducibility of the study, the authors should provide a more detailed description of the materials and methods, especially for critical experiments like the Yeast-two-hybrid assays. Clear documentation of specific reagents, strains, and protocols used, along with information on controls, will bolster the validity of the results and facilitate future research in this area.

Response: Thank you for your suggestions. We provided more details in the methods. For yeast two-hybrid assays, the vector information was included in “Vector constructions” section.

Minor Point:

Line 61: There is a space between ')' and '.', which needs to be edited.

Response: The space was deleted.

Reviewer #1 (Significance): This study holds significant importance within the field of plant immunity research. The authors have made valuable contributions through their comprehensive analysis, encompassing genetics, transcriptional, translational, and proteomic approaches, to elucidate the critical role of tRNA thiolation in plant immunity. One of the major strengths of this study lies in its ability to shed light on a previously unknown regulatory mechanism for plant defense. By identifying the cbp mutant and investigating the role of ROL5 and CTU2 in catalyzing the mcm5s2U modification, the authors have unveiled a novel aspect of plant immune regulation. This innovative discovery provides a deeper understanding of the intricate molecular processes governing immunity in plants.

Moreover, the study's findings are not limited to the immediate field of plant immunity but also have broader implications for the scientific community. By employing diverse methodologies, the authors have demonstrated how tRNA thiolation exerts control over both transcriptional and translational reprogramming, revealing intricate links between these processes. This integrative approach sets a precedent for future research in the field of plant molecular biology and opens up new avenues for investigating other aspects of immune regulation.

In terms of its relevance, the study's findings have the potential to captivate researchers across various disciplines, such as plant biology, molecular genetics, and translational research. The insights gained from this study may inspire researchers to explore further the role of tRNA in other regulation.

Response: Thank you very much for your positive comments and support!

Reviewer #2 (Evidence, reproducibility and clarity): The authors presented an intriguing and previously unknown mechanism that the tRNA mcm5s2U modification regulates plant immunity through the SA signaling pathway, specifically by controlling NPR1 translation. The manuscript was well-written and logically structured, allowing for a clear understanding of the research. The authors provided strong and persuasive data to support their key claims. However, further improvement is required to strengthen the conclusion that mcm5s2U regulates plant immunity by controlling NPR1 translation.

Response: Thank you very much for your positive comments and support!

Major comments:

1. NPR1 translation should be examined to verify the Mass Spec (Figure 5B) and polysome profiling data (Figure 5D) by checking the NPR1 protein and mRNA level using antibodies and qPCR, respectively, in the cgb mutant background to establish a concrete confirmation of CGB regulation in NPR1 translation.

Response: This is a very constructive suggestion. We performed these experiments and found that the transcription levels of NPR1 were similar between COM and cgb both before and after PsmES4326 infection (Figure S2), which is consistent with RNA-Seq data. Consistent with the Mass Spec and polysome profiling data, the NPR1 protein level was much higher in COM than that in cgb(Figure 5C) after Psm ES4326 infection. Together, these data further supported our conclusion that translation of NPR1 is impaired in cgb.

1. Analyzing the genetic epistasis of CGB and NPR1 to check if CGB regulates plant immunity through the NPR1-dependent SA signal pathway. If the authors' claim is valid, I would expect no addictive effect on bacterial growth in the cgb/npr1 double mutant compared to the single mutants. Due to the broad impact of CGB on plant signaling (Figures 4E and 4F), the SA protection assay, which concentrates on the SA signal pathway, needs to be tested in WT, cgb and npr1 plants as an alternative assay to the genetic epistasis analysis. I expect that the SA-mediated protection is also compromised in cgb mutant background.

Response: Thank you for your suggestions. We did examine the growth of Psm ES4326 in the cgb npr1_double mutant and found that _cgb npr1 was significantly more susceptible than npr1 and cgb (Figure below). Although the additive effects were observed, this result was not against our conclusion for the following reasons. First, the translation of NPR1 was reduced rather than completely blocked in cgb. In other words, NPR1 still has some function in cgb. But in the cgb npr1 double mutant, the function of NPR1 is completely abolished, which explains why cgb npr1 was more susceptible than cgb. Second, in addition to NPR1, some other immune regulators (such as PAD4, EDS5, and SAG101) were also compromised in cgb(Figure 5B), which explained why cgb npr1 was more susceptible than npr1. Since the result of the genetic analysis was not intuitive, we decided not to include it in the manuscript.

SA signaling is known to regulate both basal resistance and systemic acquired resistance (SA-mediated protection). We have shown that cgb is defective in the defect of basal resistance, which cgb is sufficient to support our conclusion that the tRNA thiolation is essential for plant immunity. We agree that it is expected that the SA-mediated protection is also compromised in cgb. We will test this in the future study.

1. Could the authors comment on why using COM instead of WT as a control to perform the majority of the experiments?

Response: Thank you for your comments. In addition to ROL5, the cgb mutant may have other mutations compared with WT.COM is a complementation line in the cgb background. Therefore, the genetic background between COM and cgb may be more similar than that of WT and cgb.

1. In Figure 5E, why does ACTIN2 have an enhanced translation while NPR1 shows a compromised one in cgb mutant? How does the mcm5s2U distinguish NPR1 and ACTIN2 codons? Does mcm5s2U modification have both positive and negative roles in regulating protein translation?

Response: Thank you for raising this question. As previously reported, loss of the mcm5s2U modification causes ribosome pausing at AAA and CAA codons. Therefore, the translation of the mRNAs with more GAA/CAA/AAA codons (called s2 codon) is likely to be affected more dramatically in cgb. We have analyzed the percentage of s2 codon at whole-genome level (Figure below). The average percentage is 8.5%, while NPR1 contains 10.1% s2 codon and actin contains only 4.5% s2 codon. When fewer ribosomes are used for translation of the mRNAs with high s2 codon percentage, more ribosomes are available for translation of the mRNAs with low s2 codon percentage, which may account for the enhanced translation efficiency. To focus on NPR1 and to avoid confusion, we removed the ACTIN data in the revised manuscript.

1. Specify the protein amount used for the in vitro pull-down assay and agrobacteria concentration used for the tobacco Co-IP assay in the protocol section.

Response: We added this information in Method section in the revised manuscript.

4. Delete the SA quantification and Ion leakage assay in the protocol, which are not used in the study.

Response: We are sorry for the mistake. The SA quantification and ion leakage data were included in previous visions of the manuscript. We removed the data but forgot to remove the corresponding method in the present version. We deleted them in the revised manuscript.

1. The strain Pst DC3000 avrRPT2 was not used in this study. Please remove it.

Response: We are sorry for the mistake. The strain Pst DC3000 avrRPT2 was used for ion leakage assay in previous visions of the manuscript. We deleted it in the revised manuscript.

1. In Figure 5F, did the 59 genes tested overlap with the 366 attenuated proteins in the cgb mutant? Were the 59 genes translationally regulated?

Response: Thank you for your suggestion. Venn diagram analysis revealed that 12 genes (about 20%) are also attenuated proteins, suggesting that the mcm5s2U modification regulates the translation of some SA-responsive genes.

Reviewer #2 (Significance): The authors' study is significant as it establishes the first connection between tRNA mcm5s2U modification and plant immunity, specifically by regulating NPR1 protein translation. This research expands our understanding of the biological role of tRNA mcm5s2U modification and highlights the importance of translational control in plant immunity. It is likely to captivate scientists working in this field.

Response: Thank you very much for your positive comments and support!

Reviewer #3 (Evidence, reproducibility and clarity):

In this manuscript, the authors identified a cgb mutant that carries a mutation in the ROL5 gene Both the cgb mutant and the newly created rol5-c mutant are susceptible to the bacterial pathogen Psm. The authors showed that ROL5 interacts with CTU2, the Arabidopsis homologous protein of the yeast tRNA thiolation enzyme NCS2. A ctu2-1 mutant is also susceptible to Psm, suggesting the tRNA thiolation may play a role in plant immunity. Indeed, tRNA mcm5S2U levels are undetectable in rol5-c and ctu2-1 mutants. The authors found that the cgb mutation significantly attenuated basal and Psm-induced transcriptome and proteome changes. Furthermore, it was found that the translation efficiency of a group of SA signaling-related proteins including NPR1 is compromised.

The manuscript provides solid evidence for the involvement of ROL5 and CTU2 in plant immunity using the rol5 and ctu2 mutants. The authors may consider the following suggestions and comments to improve the manuscript.

Response: Thank you very much for your support and suggestions!

1. The function of the Elongator complex in tRNA modification/thiolation has been extensively studied. In Arabidopsis Elongator mutants, mcm5S2U levels are very low, similar to the levels in the rol5 and ctu2 mutants (Mehlgarten et al., 2010, Mol Microbiology, 76, 1082-1094; Leitner et al., 2015 Cell Rep). In elp mutants, the PIN protein levels are reduced without reduced mRNA levels (Leitner et al., 2015), indicating that Elongator-mediated tRNA modification is involved in translation regulation. The Elongator complex plays an important role in plant immunity, though the reduced mcm5S2U levels in elp mutants were not proposed as the exclusive cause of the immune phenotypes. In fact, it would be difficult to establish a cause-effect relationship between tRNA modification and immunity. These results should be discussed in the manuscript.

Response: Thank you very much for your insightful comment on the role of the ELP complex in tRNA modification and plant immunity. We added a paragraph discussing the ELP complex in the revised manuscript (Line 280-295).

In addition to tRNA modification, the ELP complex has several other distinct activities including histone acetylation, α-tubulin acetylation, and DNA demethylation. Therefore, it is difficult to dissect which activity of the ELP complex contributes to plant immunity. However, the only known activity of ROL5 and CTU2 is to catalyze tRNA thiolation. Considering that the elp, rol5, and ctu2 mutants are all defective in tRNA thiolation, it is likely the tRNA modification activity of the ELP complex underlies its function in plant immunity.

1. The interaction between CTU2 and ROL5 in Y2H has previously been reported (Philipp et al., 2014). The same report also showed reduced tRNA thiolation in the ctu2-2 mutant using polyacrylamide gel. These results should be mentioned/discussed in the manuscript.

Response: Thank you for pointing them out. We added this information in the revised version (Line 146-147).

1. tRNA modification unlikely plays a unique role in plant immunity. It can be inferred that mutations affecting tRNA modification (rol5, ctu2, elp, etc.) would delay both internal and external stimulus-induced signaling including immune signaling.

Response: We agree with you that tRNA modification has other roles in addition to plant immunity. In the Discussion section, we have mentioned that “it was found that tRNA thiolation is required for heat stress tolerance (Xu et al., 2020). ……It will also be interesting to test whether tRNA thiolation is required for responses to other stresses such as drought, salinity, and cold.” (Line276-279).

1. It would be interesting to conduct statistical analyses on the genetic codons used in the CDSs whose translation was attenuated as described in the manuscript. Do these genes including NPR1 use more than average levels of AAA, CAA, and GAA codons? If not, why their translation is impaired?

Response: Thank you for your suggestion. We called GAA/CAA/AAA codons s2 codon. We have analyzed the percentage of s2 codon at whole-genome level (Figure below). NPR1 does contain more s2 codon (10.1%) than the average level (8.5%). We are preparing another manuscript, which will report the relationship between s2 codon and translation.

Referees cross-commenting

It is important to put current research in the context of available knowledge in the field. The digram in Figure 3C shows that the Elongator complex functions upstream of ROL5 & CTU2 in modifying tRNA. The function of Elongator in plant immunity has been well established. The similarities and differences should be discussed. Additionally, it may no be a good idea to claim that the results are novel.

Response: Thank you for your comments. We added a paragraph discussing the ELP complex in the revised manuscript (Line 280-295). The ELP complex catalyzes the cm5U modification, which is the precursor of mcm5s2U catalyzed by ROL5 and CTU2. In addition to tRNA modification, the ELP complex has several other distinct activities including histone acetylation, α-tubulin acetylation, and DNA demethylation. Therefore, it is difficult to dissect which activity of the ELP complex contributes to plant immunity. However, the only known activity of ROL5 and CTU2 is to catalyze tRNA thiolation. Considering that the elp, rol5, and ctu2 mutants are all defective in tRNA thiolation, it is likely the tRNA modification activity of the ELP complex underlies its function in plant immunity. Therefore, our study improved our understanding of the ELP complex in plant immunity. We have deleted the words “new” and “novel” throughout the manuscript.

Reviewer #3 (Significance): The manuscript provides solid evidence for the involvement of ROL5 and CTU2 in plant immunity. However, the authors did not acknowledge the existing results about the Elongator complex that functions in the same pathway in modifying tRNA. The involvement of Elongator in plant immunity has been well established. The cause-effect relationship between tRNA modification and plant immunity is difficult to demonstrate.

Response: We think that the cause-effect relationship between the activities of the ELP complex and plant immunity is difficult to demonstrate because the ELP complex has several distinct activities other than tRNA modification. However, since the only known activity of ROL5 and CTU2 is to catalyze tRNA thiolation, the cause-effect relationship between tRNA thiolation and plant immunity is clear, which indicated that the tRNA modification activity of the ELP complex contributes to plant immunity.

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 manuscript, the authors identified a cgb mutant that carries a mutation in the ROL5 gene Both the cgb mutant and the newly created rol5-c mutant are susceptible to the bacterial pathogen Psm. The authors showed that ROL5 interacts with CTU2, the Arabidopsis homologous protein of the yeast tRNA thiolation enzyme NCS2. A ctu2-1 mutant is also susceptible to Psm, suggesting the tRNA thiolation may play a role in plant immunity. Indeed, tRNA mcm5S2U levels are undetectable in rol5-c and ctu2-1 mutants. The authors found that the cgb mutation significantly attenuated basal and Psm-induced transcriptome and proteome changes. Furthermore, it was found that the translation efficiency of a group of SA signaling-related proteins including NPR1 is compromised.

The manuscript provides solid evidence for the involvement of ROL5 and CTU2 in plant immunity using the rol5 and ctu2 mutants. The authors may consider the following suggestions and comments to improve the manuscript.

1. The function of the Elongator complex in tRNA modification/thiolation has been extensively studied. In Arabidopsis Elongator mutants, mcm5S2U levels are very low, similar to the levels in the rol5 and ctu2 mutants (Mehlgarten et al., 2010, Mol Microbiology, 76, 1082-1094; Leitner et al., 2015 Cell Rep). In elp mutants, the PIN protein levels are reduced without reduced mRNA levels (Leitner et al., 2015), indicating that Elongator-mediated tRNA modification is involved in translation regulation. The Elongator complex plays an important role in plant immunity, though the reduced mcm5S2U levels in elp mutants were not proposed as the exclusive cause of the immune phenotypes. In fact, it would be difficult to establish a cause-effect relationship between tRNA modification and immunity. These results should be discussed in the manuscript.
2. The interaction between CTU2 and ROL5 in Y2H has previously been reported (Philipp et al., 2014). The same report also showed reduced tRNA thiolation in the ctu2-2 mutant using polyacrylamide gel. These results should be mentioned/discussed in the manuscript.
3. tRNA modification unlikely plays a unique role in plant immunity. It can be inferred that mutations affecting tRNA modification (rol5, ctu2, elp, etc.) would delay both internal and external stimulus-induced signaling including immune signaling.
4. It would be interesting to conduct statistical analyses on the genetic codons used in the CDSs whose translation was attenuated as described in the manuscript. Do these genes including NPR1 use more than average levels of AAA, CAA, and GAA codons? If not, why their translation is impaired?

Referees cross-commenting

It is important to put current research in the context of available knowledge in the field. The digram in Figure 3C shows that the Elongator complex functions upstream of ROL5 & CTU2 in modifying tRNA. The function of Elongator in plant immunity has been well established. The similarities and differences should be discussed. Additionally, it may no be a good idea to claim that the results are novel.

Significance

The manuscript provides solid evidence for the involvement of ROL5 and CTU2 in plant immunity. However, the authors did not acknowledge the existing results about the Elongator complex that functions in the same pathway in modifying tRNA. The involvement of Elongator in plant immunity has been well established. The cause-effect relationship between tRNA modification and plant immunity is difficult to demonstrate.

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

The authors presented an intriguing and previously unknown mechanism that the tRNA mcm5s2U modification regulates plant immunity through the SA signaling pathway, specifically by controlling NPR1 translation. The manuscript was well-written and logically structured, allowing for a clear understanding of the research. The authors provided strong and persuasive data to support their key claims. However, further improvement is required to strengthen the conclusion that mcm5s2U regulates plant immunity by controlling NPR1 translation.

Major comments:

1. NPR1 translation should be examined to verify the Mass Spec (Figure 5B) and polysome profiling data (Figure 5D) by checking the NPR1 protein and mRNA level using antibodies and qPCR, respectively, in the cgb mutant background to establish a concrete confirmation of CGB regulation in NPR1 translation.
2. Analyzing the genetic epistasis of CGB and NPR1 to check if CGB regulates plant immunity through the NPR1-dependent SA signal pathway. If the authors' claim is valid, I would expect no addictive effect on bacterial growth in the cgb/npr1 double mutant compared to the single mutants. Due to the broad impact of CGB on plant signaling (Figures 4E and 4F), the SA protection assay, which concentrates on the SA signal pathway, needs to be tested in WT, cgb and npr1 plants as an alternative assay to the genetic epistasis analysis. I expect that the SA-mediated protection is also compromised in cgb mutant background.

Minor comments:

1. Could the authors comment on why using COM instead of WT as a control to perform the majority of the experiments?
2. In Figure 5E, why does ACTIN2 have an enhanced translation while NPR1 shows a compromised one in cgb mutant? How does the mcm5s2U distinguish NPR1 and ACTIN2 codons? Does mcm5s2U modification have both positive and negative roles in regulating protein translation?
3. Specify the protein amount used for the in vitro pull-down assay and agobacterial concentration used for the tobacco Co-IP assay in the protocol section.
4. Delete the SA quantification and Ion leakage assay in the protocol, which are not used in the study.
5. The strain Pst DC3000 avrRPT2 was not used in this study. Please remove it.
6. In Figure 5F, did the 59 genes tested overlap with the 366 attenuated proteins in the cgb mutant? Were the 59 genes translationally regulated?

Significance

The authors' study is significant as it establishes the first connection between tRNA mcm5s2U modification and plant immunity, specifically by regulating NPR1 protein translation. This research expands our understanding of the biological role of tRNA mcm5s2U modification and highlights the importance of translational control in plant immunity. It is likely to captivate scientists working in this 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 #1

Evidence, reproducibility and clarity

The article titled "The tRNA thiolation-mediated translational control is essential for plant immunity" by Zheng et al. highlights the critical role of tRNA thiolation in Arabidopsis plant immunity through comprehensive analysis, including genetics, transcriptional, translational, and proteomic approaches. Through their investigation, the authors identified a cbp mutant, resulting in the knockout of ROL5, and discovered that ROL5 and CTU2 form a complex responsible for catalyzing the mcm5s2U modification, which plays a pivotal role in immune regulation. The findings from this study unveil a novel regulatory mechanism for plant defense. Undoubtedly, this discovery is innovative and holds significant potential impact. However, before considering publication, it is necessary for the authors to address the various questions raised in the manuscript concerning the experiments and analysis to ensure the reliability of the study's conclusions.

Here is Comments:

Line 64-65:<br /> The author mentioned that 'While NPR1 is a positive regulator of SA signaling, NPR3 and NPR4 are negative regulators.' However, several recent discoveries are suggesting that it may not be a definitive fact that NPR3 and NPR4 are negative regulators. Therefore, I recommend the authors to review this section in light of the findings from recent papers and make necessary edits to reflect the most current understanding.

Line 182- & Figure 4:<br /> The author conducted RNA-seq, Ribo-seq, and proteome analysis. Describing the analysis as "transcriptional and translational" using RNA-seq and proteome data seems not entirely accurate. Proteome data compared with RNA-seq not only reflects translational changes but may also encompass post-translational regulations that contribute to the observed differences. To maintain precision, the title of this section should either be modified to "transcriptional and protein analysis" or, alternatively, compare RNA-seq and Ribo-seq data to demonstrate the transcriptional and translational changes more explicitly.

Line 229-235 and Figure 5C:<br /> The interpretation of Figure 5C's polysome profiling results is inconclusive. There does not seem to be a noticeable difference in polysomal fractions between the cab mutant and CAM. The observed differences in the overlay of multiple polysome fractions between cab and COM could be primarily influenced by baseline variations rather than a significant decrease in the polynomial fractions in cpg. Therefore, it is necessary to carefully review other relevant papers that discuss polysome fraction data and their analysis. By doing so, the authors can make the appropriate corrections to ensure accurate interpretations.

Line 482 Ion Leakage assay:

I could not find the ion leakage assay in this manuscript, so I wonder why it is mentioned.

Materials and Methods:

To enhance the reproducibility of the study, the authors should provide a more detailed description of the materials and methods, especially for critical experiments like the Yeast-two-hybrid assays. Clear documentation of specific reagents, strains, and protocols used, along with information on controls, will bolster the validity of the results and facilitate future research in this area.

Minor Point:

Line 61: There is a space between ')' and '.', which needs to be edited.

Significance

This study holds significant importance within the field of plant immunity research. The authors have made valuable contributions through their comprehensive analysis, encompassing genetics, transcriptional, translational, and proteomic approaches, to elucidate the critical role of tRNA thiolation in plant immunity. One of the major strengths of this study lies in its ability to shed light on a previously unknown regulatory mechanism for plant defense. By identifying the cbp mutant and investigating the role of ROL5 and CTU2 in catalyzing the mcm5s2U modification, the authors have unveiled a novel aspect of plant immune regulation. This innovative discovery provides a deeper understanding of the intricate molecular processes governing immunity in plants.

Moreover, the study's findings are not limited to the immediate field of plant immunity but also have broader implications for the scientific community. By employing diverse methodologies, the authors have demonstrated how tRNA thiolation exerts control over both transcriptional and translational reprogramming, revealing intricate links between these processes. This integrative approach sets a precedent for future research in the field of plant molecular biology and opens up new avenues for investigating other aspects of immune regulation.

In terms of its relevance, the study's findings have the potential to captivate researchers across various disciplines, such as plant biology, molecular genetics, and translational research. The insights gained from this study may inspire researchers to explore further the role of tRNA in other regulation.

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Reply to the reviewers

General Statements

In this manuscript, we describe a LINC complex-dependent centrosome positioning mechanism that takes place during the early stages of mitotic spindle assembly. We are grateful to the reviewers for their comments and suggestions and hope the proposed revision plan addresses all concerns raised. We are pleased that reviewers recognize the excellent technical quality of the experiments and the significance of the work presented in this manuscript.

Description of the planned revisions

Reviewer 1

• “Moreover, we demonstrate this mechanism is altered in cancer cells, leading to increased chromosome segregation errors. » Here the authors infer that the identified mechanism is absent in cancer cells and that its absence contributes to chromosome segregation errors. Both conclusions are not supported by the presented data. First, the authors did not test whether any members of the LINC complex or dynactin is present at lower levels on the nuclear membranes of the cancer cells. Such a direct validation would be essential to make such a strong statement. Second, the authors conclude that this mechanism prevents chromosome segregation errors, based on the fact that depletion or impairment of the LINC complex (shSUN1, shSUN2, DN-KASH) results in chromosome segregation errors. These perturbations lead, however, as noted by the authors themselves to pleiotropic effects, including insufficient retraction of nuclear membrane, which can all contribute to chromosome segregation errors. It is therefore impossible to estimate the contribution of the centrosome positioning mechanism to these segregation errors using this type of perturbations. One could even argue that this mechanism might not be that important, since depletion of SUN2, which also impairs centrosome positioning has no significant effect on chromosome segregation.

We agree with the reviewer that an analysis of the levels of LINC complex components and dynactin in cancer cells is lacking. For this reason, we propose to analyze the levels of SUN1, SUN2, dynactin and Nesprins by immunofluorescence in all cell lines. In addition, we have now re-written the manuscript regarding the chromosome segregation phenotype, to clarify that the observed phenotypes are not necessarily due to centrosome positioning defects.

Reviewer 2

“The authors need some other NE protein as a control to show that the reduction of dynein by DN-KASH is a specific defect and not a broad impact on the NE. The dynein data in Figs. 5J-L need to be extended to SUN1/2”.

We thank the reviewer for these suggestions. To clarify this point, we will analyze the levels of lamin B following expression of DN-KASH or DPPPL-KASH. This will allow us to determine whether expression of the DN-KASH construct only affects dynein and not other NE proteins. In addition, we will analyze dynactin levels following SUN1 and SUN2 depletion.

Reviewer 3:

“Fig. 3: I suggest to quantify the lamin B1 and LBR overexpression levels”.

According to the reviewer´s suggestion, we will perform a WB analysis of the cells overexpressing lamin B1 and LBR and quantify its levels.

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

Reviewer 1

• “The authors conclude based on three cell lines that the centrosome positioning mechanisms is present in non-transformed cells and not in cancerous cells. The authors have, however, only analysed 1 non-cancerous cell line, and they compare cells originating from vastly different tissues (retina, bones and breast) and origins (epithelial vs. mesenchymal cartilage cells). Such a general statement is not possible, without a systematic comparison of several healthy cells vs cancerous cells from the same tissue”.

We agree with this reviewer´s comment, which is also shared by the other reviewers. Accordingly, we have now extensively rewritten the manuscript to tone down this statement and focus on the role of the LINC complex in determining centrosome positioning.

• “While the data showing that centrosome positioning depends on the LINC complex is solid and robust, some of the "negative" examples identified by the authors are less convincing. One the process the authors study is cell rounding. Based on the fact that Rap1 transfection or treatment with Calyculin A does not lead to differences that are statistically different, the authors conclude that cell rounding is not involved. However, absence of statistical difference does not mean that there is no difference. Indeed, when comparing the raw data in Figure 2L and 2Q to the positive hit shSun2 in Figure 4J, one could conclude that cell rounding does make a difference, and that this statistical difference would emerge if the authors would count a high number of cells. Therefore the authors should interpret these results in a more differentiated manner, and also instead of just stating nonsignificant, state also the real p-values for the different experiment”.

According to the reviewer´s suggestion, we have now added all p values to the respective graphs and interpreted these results in a more step-by-step manner. Moreover, while we understand the reviewer`s comment regarding our sample size, it should be noted that this is a single-cell, high-resolution imaging approach which, in combination with certain treatments makes it very challenging to obtain data for a high number of cells. In this regard, we point out that interfering with cell rounding was extremely difficult to achieve. When highly overexpressed, Rap1* completely impairs mitotic cell de-adhesion, and this blocks mitotic entry (Marchesi et al., 2014). Furthermore, CalA treatment induces a fast and drastic rounding, which makes it very challenging to accurately track centrosome and nuclear positions. Nevertheless, we filmed additional cells treated with CalA and added the data to the figures. Our results still confirm that interfering with cell rounding does not significantly change centrosome positioning during this stage. It should be noted that the sample size in all conditions is within the range normally used when performing single-cell high resolution imaging.

• The second major concerns emerges when looking at the data in Figure 5, when the authors test for the abundance of the dynein complex on the nuclear envelope in cells treated with DPPPL-KASH or DN-KASH. Yes, there is a statistical difference, but the absolute difference is tiny (I estimated a normalized intensity of 1.44 vs 1.35). This is a difference of less than 10%. How do the authors think that such a small change in dynein could have such a strong effect on centrosome positioning? Would a partial dynactin depletion by 10% give an equivalent result? Does the depletion of other proteins involved in the late recruitment of dynein at the NE also affect centrosome positioning?

We thank the reviewer for this important point. Originally, we quantified dynactin intensity by selecting three unbiased random regions of the NE. However, this approach might underestimate the overall fluorescence intensity across the entire structure. For this reason, we have now measured dynactin fluorescence intensity over the entire NE using the same dataset. We have replaced Fig. 5K and L with this data and a description of the method has been added to the Materials and Methods section. As can be seen from the new graph, there is a reduction of approximately 50% in dynactin NE fluorescence intensity.

The reviewer also asks whether depletion of other proteins involved in the late recruitment of dynein at the NE would also affect centrosome positioning. However, extensive previous work done by us and others, has shown that depletion of either BicD2 or NudE/NudEL, which are the main adaptors for dynein loading during the G2/M transition, significantly affect prophase centrosome positioning, since they detach centrosomes from the NE (Splinter et al., 2010; Bolhy et al., 2011; Hu et al., 2013; Baffet et al., 2015; Nunes et al., 2020). Once detached, centrosomes are no longer able to orient according to nuclear cues. Therefore, we do not believe such an approach would provide additional information regarding the role of the LINC complex in this process.

Reviewer 2:

• “Figure 1 is insufficiently explained. The authors have to describe in an understandable way how they measured centrosome-centrosome angle and centrosome-nucleus angle. They should show a cartoon in which these angles are clearly shown. The small cartoons in Fig. 1C are not helpful at all; they are also not explained. The authors should explain the meaning of the black dots (are these centrosomes?) and the even smaller dots. The short nuclear axis should be indicated, e.g., by a red line”.

We apologize for the lack of sufficient explanation in Figure 1. We have now re-written the text. We have also added a scheme explaining how centrosome-nucleus and centrosome-centrosome angles are quantified, according to the reviewer´s suggestion. We have added this to Fig. S1. We believe this makes our data more understandable and easier to follow.

“On the first page of the manuscript: "Consequently, at the NEP, centrosomes are positioned on the shortest nuclear axis (Fig. 1C) as can be seen in Fig. 1A. This means that the centrosome-nucleus angle relative to the shortest nuclear axis should be 0. However, in Fig. 1C, this angle is between 45 and 90 degrees. This is also the case for Fig. 1D. Please clarify”.

We thank the reviewer for noticing this error. In fact, the graphs reflect positioning of centrosomes relative to the longest nuclear axis. Therefore, when the values are close to 90º, this means they are oriented on the shortest nuclear axis. We understand this could be confusing to the readers. We have now clarified this information throughout the text.

• “I find it confusing that in Fig. 1, depending on the subfigure, the short or longest nuclear axis is used as a reference point: Fig. 1C: shortest; D: shortest; F: shortest; G: longest; I: shortest; J: longest. Thus, even within the same cell line, the reference point is changing. What is the rational for this variation”?

Again, we refer to the point above. The reference point is always the shortest nuclear axis. However, we apologize for the lack of clarity. This has all been changed, according to the explanation provided in the previous point.

• Fig. 4K, L, M: in figure, y-axis: "shortest nuclear axis". In legend: "relative to the longest nuclear axis". I guess the longest nuclear axis is correct. Same in Fig. 5D and E. Fig. 5C lacks the WT control.

This information has been clarified in the text and panels have been corrected accordingly. Regarding Fig. 5C, we believe the correct control is the expression of PPPL-KASH, since it has been shown extensively that Nesprins localize to the NE in control, unmanipulated cells. Nevertheless, we have added a WT control to Supplementary Figure 5, showing localization of Nesprins in unmanipulated prophase cells.

“The cells in Fig. 5J are not comparable: one has a monopolar spindle, the other a bipolar. The authors need some other NE protein as a control to show that the reduction of dynein by DN-KASH is a specific defect and not a broad impact on the NE. The dynein data in Figs. 5J-L need to be extended to SUN1/2”.

We agree with the reviewer´s comment that the cell in the top panel might appear as a monopolar. However, it is not. In fact, this cell has centrosomes on the top and bottom of the nucleus, in a vertical configuration (check Magidson et al., Cell, 2011). To clarify this, we have now added lateral projections of all cells, highlighting the centrosomes to clearly show they are positioned on opposite sides of the nucleus. The other points related to the effects of DN-KASH on other NE proteins and dynactin levels following shSUN1 and shSUN2 are being addressed (please see comments above in the section “description of planned reviews”).

“The title of the paper is misleading: the authors do not provide any indication for a nuclear signal in prophase that determines centrosome positioning”.

We have changed the title of the manuscript according to the reviewer´s suggestion.

“It would make sense to use the same time scale in Figs. 1A and B (either min.sec. or sec.) to allow direct comparison”.

We have now changed the time scale to seconds in all figures to allow direct comparison.

“2nd section: Mitotic cell rounding "The authors state: Given that cancer cells failed... I would be careful with this generalization; only one cancer cell was used in this study”.

Given the limited number of cells that we used, and following the concern raised by all reviewers, we have now re-written the text to avoid generalizations. Instead, we now focus on the role of the LINC complex in determining centrosome positioning.

“The authors say: "However, they did not place the centrosomes at the shortest nuclear axis (Figure 4K-M)." Centrosomes are still on the shortest nuclear axis but not as frequent as in control”.

This has been corrected.

“The white color in Fig. 6B cannot be seen and needs to be changed to something else”.

We apologize for this oversight. During the upload and pdf conversion process, we did not realize the color of this bar, corresponding to the DN-KASH group had changed to white. This has now been corrected.

The paper has neither line nor page numbers.

This has been added.

Reviewer 3

“it would make sense to indicate the test used for each p-value in all the figure legends”.

We have now added the statistical test used and the p-value in the figure legends.

“Figure legends are quite repetitive and could be shortened. E.g. in Fig. 1 the description for E, F, H and I repeats what has been explained for B and C. Same applies between figure legends. The authors might refer to previous legends if the analysis was done in a similar way”.

The legends have been simplified.

“How is nuclear solidity defined and analyzed in Fig S3D”?

Nuclear solidity was analyzed using Fiji. In short, nuclei are outlined using the polygon tool and nuclear area is measured. To calculate nuclear solidity, the nuclear area is then divided by the corresponding nuclear convex hull area. Irregular nuclei will typically show a lower nuclear solidity value. This information was added to the text.

“The references to Fig S3 in figure legend 3 ("see Fig S3") do not enlighten the message and could be removed. The same applies to Fig5 - here it is not clear why the author refer to Fig S4”.

We agree with this reviewer´s comment. We have now removed these references from the legends.

“Fig. 5: Consider reordering the panel: Start with the current panel C (as in the text) as it is the necessary control prior to the experimental data”.

We have now changed the order of the panel according to the reviewer´s suggestion.

“Fig 5 I: what means "before"? Can the authors give a time window they use for analysis”.

We have now replaced the term “before” with a defined time.

“Page 20: "... shortest nuclear axis (Fig. 1C, 5D-G; n.s. - not significant). However, DN-KASH-expressing cells showed compromised separation and positioning of centrosome (Fig. 5D-G, * p=0.0155 and * p=0.0237, respectively). - rather point to the specific panels, i.e. Fig. 1C, 5D and F as well as and Fig. 5E and G”.

We have now clarified these points in the text.

“Fig 6B. The DN- KASH bars are on my pdf not visible - use a darker grey”.

As mentioned above, we apologize for this oversight. We did not realize that during the pdf conversion process the bar corresponding to the DN-KASH group had changed to white. We have now corrected this.

“Fig S6, albeit mentioned in the text, is not included in the supplementary info”.

We apologize for this error. In fact, where it reads Fig. S6, should be Fig. S5. We have now corrected this.

“a. GlutaMAX instead of GlutaMAXE (page 29)

b. What means "as described previously"? No reference is given. Do you refer to the upper part of the method section? (page 30)

c. 20 nM HEPES should most probably read 20 mM (page 32)

d. "1:50 protease inhibitor; 1:100 Phenylmethylsulfonul fluoride" - which protease inhibitor (mixture)? Rather phenylmethylsulfonyl fluoride.

e. exact composition of the cytoskeleton buffer used to prepare 4% paraformaldehyde could be given”.

All these suggestions/corrections have been introduced in the text.

Description of analyses that authors prefer not to carry out.

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Referee #3

Evidence, reproducibility and clarity

Summary: Centrosomes separate early in mitosis to allow faithful spindle assembly and chromatin segregation. In the current study the author show that in RPE-1 cells the separated centrosomes typically position each other along the shorter axis of the nucleus while in cancer derived U2OS and MDA-MB-486 this is rather random. Mitotic cell rounding is not causal for this effect. Rather, the LINC (linker of nucleoskeleton and cytoskeleton) complex, a protein complex spanning both membranes of the nuclear envelope, is required for this. The data indicate that this is dynactin1 recruitment to the nuclear envelope. The work suggest that proper arrangement of the centrosomes along the short nuclear axis via the LINC complex contributes to chromatin segregation fidelity in RPE-1 cells.

Major comments: The data, derived mostly by life cell imaging of cell culture lines, are of very high quality, carefully controlled and analyzed. They fully support the claims of the study and are well presented, both in text and figures. Statistical analysis seems adequate, but since the authors show different kinds of data sets including time series and use several kinds of statistical tests, it would make sense to indicate the test used for each p-value in all the figure legends. I have no major criticism or experiments to suggest.

Minor comments:

1. Figure legends are quite repetitive and could be shortened. E.g. in Fig. 1 the description for E, F, H and I repeats what has been explained for B and C. Same applies between figure legends. The authors might refer to previous legends if the analysis was done in a similar way.
2. How is nuclear solidity defined and analyzed in Fig S3D?
3. The references to Fig S3 in figure legend 3 ("see Fig S3") do not enlighten the message and could be removed. The same applies to Fig5 - here it is not clear why the author refer to Fig S4.
4. Fig. 3: I suggest to quantify the lamin B1 and LBR overexpression levels.
5. Fig. 5: Consider reordering the panel: Start with the current panel C (as in the text) as it is the necessary control prior to the experimental data.
6. Fig 5 I: what means "before"? Can the authors give a time window they use for analysis.
7. Page 20: "... shortest nuclear axis (Fig. 1C, 5D-G; n.s. - not significant). However, DN-KASH-expressing cells showed compromised separation and positioning of centrosome (Fig. 5D-G, * p=0.0155 and * p=0.0237, respectively). - rather point to the specific panels, i.e. Fig. 1C, 5D and F as well as and Fig. 5E and G.
8. Fig 6B. The DN- KASH bars are on my pdf not visible - use a darker grey
9. Fig S6, albeit mentioned in the text, is not included in the supplementary info.
10. Material and Methods: in general very clear and carefully written
11. a. GlutaMAX instead of GlutaMAXE (page 29)
12. b. What means "as described previously"? No reference is given. Do you refer to the upper part of the method section? (page 30)
13. c. 20 nM HEPES should most probably read 20 mM (page 32)
14. d. "1:50 protease inhibitor; 1:100 Phenylmethylsulfonul fluoride" - which protease inhibitor (mixture)? Rather phenylmethylsulfonyl fluoride.
15. e. exact composition of the cytoskeleton buffer used to prepare 4% paraformaldehyde could be given

Referees cross-commenting

I also mentioned in teh significance section the two weak points (only one non-cancer cell line (RPE-1); the precise role of the LINC complex). I thus think all three reviewers come to a similar conclusion: technically well done albeit some improvements are possible (reviewer 2). Manuscript is interesting but whether the findings can be generalized remains open and the overall impact is limited. Personally, I think a good strategy for the authors might be to stay with the three cell lines and avoid too general statements.

Significance

General assessment: This is a very elaborate analysis of centrosome positioning at the entry of mitosis. The experiments are carefully controlled and the findings supported by multiplied experiments, e.g. the aspect of mitotic cell rounding by analysis of unperturbed cells but also by manipulation accelerating and inhibiting cell rounding. Contribution of the LINC complex is evaluated by shRNA against SUN1/2, i.e. main LINC components, but also by the KASH-DN fragment, which acts as dominant negative. On the downside the study is limited to one untransformed cell line. Given that the treatments interfering with LINC complex function most likely affect all aspects of LINC-centromere interplay, it remains open what precise function of the LINC-complex contributes to chromatin segregation fidelity

Advance: The work clearly shows that at least in RPE-1 cells the separated centrosomes arrange each other along the shorter axis of the nucleus and that the LINC complex is required for this.

Audience: The work is certainly interesting for researches interested in mitosis, most precisely in spindle assembly. It enlightens a very specific aspect of spindle assembly but this very convincing. The work is basic research.

Our experience is basic research of mitosis, nuclear structure and function both using biochemical assays and life cell imaging.

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Referee #2

Evidence, reproducibility and clarity

A nuclear signal in prophase determines centrosome positioning and ensures efficient mitotic spindle assembly.<br /> Lima and Ferreira investigate in this manuscript the regulation of centrosome positioning in early mitosis. The authors first analyze the position of the two centrosomes either relative to the cell length axis or the shortest or longest axis of the nucleus and describe differences between RPE1, U2OS, and MDA-MB cells. Next, they analyze whether mitotic cell rounding determines the position of centrosomes; however, delayed cortical retraction (Rho-kinase inhibition), adhesion disassembly inhibition (Rap1Q63E), and inducing premature rounding (CalA) did not impact centrosome positioning in RPE1, U2OS, and MDM-MB cells. In addition, the nuclear lamina and LBR were also not required for centrosome positioning on the shortest nuclear axis. In contrast, depletion of SUN1 or SUN2 and overexpression of a dominant-negative DN-KASH affected the nuclear positioning of centrosomes in RPE1 cells. Finally, the authors analyze whether the LINC complex impacts mitotic fidelity. This is indeed the case when SUN1 is depleted, but it is not the case for SUN2 depletion or DN-KASH overexpression. This difference between LINC complex components is not discussed in the manuscript. Since SUN1, SUN2, and DN-KASH affect centrosome positioning in a similar way (Figs. 4 and 5), the chromosome segregation defect in SUN1-depleted cells is most likely not caused by a centrosome position defect but probably by another defect caused by SUN1 depletion.

Major comments

1. Figure 1 is insufficiently explained. The authors have to describe in an understandable way how they measured centrosome-centrosome angle and centrosome-nucleus angle. They should show a cartoon in which these angles are clearly shown. The small cartoons in Fig. 1C are not helpful at all; they are also not explained. The authors should explain the meaning of the black dots (are these centrosomes?) and the even smaller dots. The short nuclear axis should be indicated, e.g., by a red line.
2. On the first page of the manuscript: "Consequently, at the NEP, centrosomes are positioned on the shortest nuclear axis (Fig. 1C) as can be seen in Fig. 1A. This means that the centrosome-nucleus angle relative to the shortest nuclear axis should be 0. However, in Fig. 1C, this angle is between 45 and 90 degrees. This is also the case for Fig. 1D. Please clarify.
3. I find it confusing that in Fig. 1, depending on the subfigure, the short or longest nuclear axis is used as a reference point: Fig. 1C: shortest; D: shortest; F: shortest; G: longest; I: shortest; J: longest. Thus, even within the same cell line, the reference point is changing. What is the rational for this variation?
4. Fig. 4K, L, M: in figure, y-axis: "shortest nuclear axis". In legend: "relative to the longest nuclear axis". I guess the longest nuclear axis is correct. Same in Fig. 5D and E. Fig. 5C lacks the WT control.
5. The cells in Fig. 5J are not comparable: one has a monopolar spindle, the other a bipolar. The authors need some other NE protein as a control to show that the reduction of dynein by DN-KASH is a specific defect and not a broad impact on the NE. The dynein data in Figs. 5J-L need to be extended to SUN1/2.
6. The title of the paper is misleading: the authors do not provide any indication for a nuclear signal in prophase that determines centrosome positioning.

Minor comment

1. It would make sense to use the same time scale in Figs. 1A and B (either min.sec. or sec.) to allow direct comparison.
2. 2nd section: Mitotic cell rounding "The authors state: Given that cancer cells failed... I would be careful with this generalization; only one cancer cell was used in this study.
3. The authors say: "However, they did not place the centrosomes at the shortest nuclear axis (Figure 4K-M)." Centrosomes are still on the shortest nuclear axis but not as frequent as in control.
4. The white color in Fig. 6B cannot be seen and needs to be changed to something else.
5. The paper has neither line nor page numbers.

Referees cross-commenting

My comments are more or less reflected by the comments and concerns of reviewer 1 (only one cancer cell line; the role of the LINC complex). This reduced the impact of this manuscript that is certainly intresting and has novel aspects.

Significance

The manuscript analysis an early step in spindle assembly: the positioning of the two centrosomes on the NE. As such, the paper is interesting and important. They exclude cell rounding and lamin disassembly as mechanisms for centrosome positioning. The SUN1/2 and KASH data on centrosome positioning are convincing, and they provide a novel finding on the function of the LINC complex in centrosome positioning, probably via dynein recruitment to the NE. It remains unclear whether LINC recruits dynein directly or functions via one of the two known dynein/NE recruitment pathways. LINC-dynein at the NE binds centrosome microtubules and dynein pulls them towards the NE. However, how LINC-dynein spatially positions centrosomes relative to the short axis of the nucleus remains unclear (dynein uniformly decorates the NE (Fig. 5J)). The data on chromosome missegregation are not so clear because the defect only occurs in SUN1-depleted cells. Thus, this phenotype indicates most likly a function of SUN1 but not the LINC complex and is probably not related to centrosome positioning since all LINC components affect centrosome positioning. The paper falls short in explaining how parameters were measured and contains mistakes in the figures, as outlined above. The paper lacks a coherent story (a little bit on cancer, some negative data, LINC-dynein, but it stops on the surface).

It will be relatively easy to improve some aspects of the manuscript (explaining the angles, correcting the figures: one week). Measuring dynein at the NE in SUN1/2-depleted cells is also easy to do (1-2 months). To get more mechanistic insides into how LINC-dynein positions centrosomes probably will not be possible during revision time.

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Referee #1

Evidence, reproducibility and clarity

Summary: in this study, Lima and colleagues, investigate the mechanisms controlling the position of the two centrosomes at nuclear envelope breakdown. The authors show that in the non-cancerous human epithelial RPE1-cell line, the centrosomes are generally positioned in the short axis of the nucleus; in contrast in two cancer cell lines, they did not find an equivalent pattern. When the authors set out to identify potential molecular players required for this positioning, they find that the LINC complex is required , possibly by recruiting dynein to the nuclear membrane. Finally, the authors show that disruption of the LINC complex is associated with chromosome segregation errors.

Major Comments:

In general, the presented experiments are of excellent technical quality. The main conclusions of the manuscript, are however, not always well supported by the experimental data. They should be either interpreted more cautiously or supported by additional experimental evidence. I highlight these here, using the main conclusions of the abstract.

1. "We show that in untransformed cells, centrosome positioning is regulated by a nuclear signal, independently of external cues. »

The authors conclude based on three cell lines that the centrosome positioning mechanisms is present in non-transformed cells and not in cancerous cells. The authors have, however, only analysed 1 non-cancerous cell line, and they compare cells originating from vastly different tissues (retina, bones and breast) and origins (epithelial vs. mesenchymal cartilage cells). Such a general statement is not possible, without a systematic comparison of several healthy cells vs cancerous cells from the same tissue.<br /> 2. "This nuclear mechanism relies on the linker of nucleoskeleton and cytoskeleton (LINC) complex that controls the loading of dynein on the nuclear envelope (NE), providing spatial cues for robust centrosome positioning on the shortest nuclear axis, prior to nuclear envelope permeabilization (NEP). »

While the data showing that centrosome positioning depends on the LINC complex is solid and robust, some of the "negative" examples identified by the authors are less convincing. One the process the authors study is cell rounding. Based on the fact that Rap1 transfection or treatment with Calyculin A does not lead to differences that are statistically different, the authors conclude that cell rounding is not involved. However, absence of statistical difference does not mean that there is no difference. Indeed, when comparing the raw data in Figure 2L and 2Q to the positive hit shSun2 in Figure 4J, one could conclude that cell rounding does make a difference, and that this statistical difference would emerge if the authors would count a high number of cells. Therefore the authors should interpret these results in a more differentiated manner, and also instead of just stating non-significant, state also the real p-values for the different experiment.<br /> The second major concerns emerges when looking at the data in Figure 5, when the authors test for the abundance of the dynein complex on the nuclear envelope in cells treated with DPPPL-KASH or DN-KASH. Yes, there is a statistical difference, but the absolute difference is tiny (I estimated a normalized intensity of 1.44 vs 1.35). This is a difference of less than 10%. How do the authors think that such a small change in dynein could have such a strong effect on centrosome positioning? Would a partial dynactin depletion by 10% give an equivalent result? Does the depletion of other proteins involved in the late recruitment of dynein at the NE also affect centrosome positioning?<br /> 3. « Moreover, we demonstrate this mechanism is altered in cancer cells, leading to increased chromosome segregation errors. »

Here the authors infer that the identified mechanism is absent in cancer cells and that its absence contributes to chromosome segregation errors. Both conclusions are not supported by the presented data. First, the authors did not test whether any members of the LINC complex or dynactin is present at lower levels on the nuclear membranes of the cancer cells. Such a direct validation would be essential to make such a strong statement. Second, the authors conclude that this mechanism prevents chromosome segregation errors, based on the fact that depletion or impairment of the LINC complex (shSUN1, shSUN2, DN-KASH) results in chromosome segregation errors. These perturbations lead ,however, as noted by the authors themselves to pleiotropic effects, including insufficient retraction of nuclear membrane, which will can all contribute to chromosome segregation errors. It is therefore impossible to estimate the contribution of the centrosome positioning mechanism to these segregation errors using this type of pertubrations. One could even argue that this mechanism might not be that important, since depletion of SUN2, which also impairs centrosome positioning has no significant effect on chromosome segregation.

Minor comments:

The author state in the Material and methods that all the figure legends contain the number of replicates. This is, however, not the case, the authors only indicate the total number of analyzed cells.

Referees cross-commenting

I agree that all three reviewers come to similar conclusions - strong technical quality, novel results and concepts, but some limitations due to lack of precise tools or the limited number of model cell lines investigated.<br /> I recommend that the authors prioritize which are the suggested experiments that could be done within a few months, and otherwise rephrase their conclusions in less general terms.

Significance

This study establishes for the first time that some cell lines set up the mitotic spindle at predefined positions of the nucleus and they identify a first molecular complex controlling this complex.

The strength of this study is the high technical quality of the data - a limitation is the over-interpretation of the current data (see major comments), and the fact that the authors do not have a tool that specifically only disrupts centrosome positioning, which would allow them to probe the importance of this mechanism.

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Reply to the reviewers

Manuscript number: RC-2023-02111

Corresponding author(s): Moira O’Bryan

1. General Statements

We thank the Review Commons editor and the three reviewers for their overall positive responses in assessing this manuscript. Further, we appreciate and would like to reiterate the similarities across our three reviewers’ comments regarding the significance of this work, where our examination of epsilon tubulin (TUBE1) during mammalian spermatogenesis will be valuable for both microtubule/cytoskeletal and developmental/ reproductive fields. Below, we have made point-by-point responses to the reviewers’ comments, and outlined by the revisions we plan to make, or have made. All line numbers refer to the transferred manuscript file with tracked changes.

2. Description of the planned revisions

Reviewer 1:* The authors claim that because the TUBE1 knockout mouse have abnormal centrosome numbers during meiosis, there is a role for TUBE1 in suppressing supernumerary centriole formation. While this is one possibility, it's also possible that abnormal centrosome numbers arose as a result of cell division defects, especially because binucleate cells are present in mutants. The authors should edit the text to state that abnormal centrosome numbers may arise from either supernumerary centriole formation (by the templated or de novo pathways) or from failure to complete cell division. *

*OPTIONAL: to test these possibilities, the authors may choose to 1) count the number of centrioles in meiosis with two different centriole markers 2) stain for markers of mature centrioles, such as Cep164, to determine the number of parental centrioles. *

Response: This is a good point. Published data indicates that the Stra8-cre is active within a subset of undifferentiated spermatogonia, and in differentiated spermatogonia through to pre-leptotene spermatocytes (Sadate-Ngatchou et al., 2008). This raises the possibility that the increase in centriole numbers could be due to a failure to complete cell division if cre is active in mitotically active spermatogonia populations. The text has been appropriately modified in lines 207-209 and 352 to reflect these insights. We appreciate the Reviewer’s optional suggestion to perform additional immunolabeling experiments and intend to examine the number of parental centrioles in spermatocytes during meiotic division using a marker of the distal or subdistal appendages. This data will be included in the final revised document.

Reviewer 2:* Considering the suggested non-canonical function of Epsilon tubulin outside the centriole in mice sperm, it is critical to know the localization of the protein in spermatocytes during meiosis and spermatids during differentiation. *

Response: We agree with Reviewer 2 that determining the localization of TUBE1 in spermatocytes and spermatids would be desirable. However, we are yet to find an appropriate available antibody for this. We have previously assessed the specificity of a TUBE1 antibody (PA5-56917, Invitrogen), however, this antibody was not suitable for use in our mouse model. This aside, we have recently acquired a new TUBE1 antibody which we plan to evaluate its specificity during this revision period. If it appears to bind specifically to TUBE1, we will perform the requested localization experiments.

For clarification we have previously defined the location of TUBE1 in spermatids to the manchette and basal body in elongating spermatids (lines 72-74) (Dunleavy et al., 2017). Unfortunately, the antibody used in this study is now discontinued. The phenotypes observed as a consequence of TUBE1 loss of function in this study are, however, consistent with these patterns of localization.

Reviewer 2:* Localization of Epsilon tubulin is needed to distinguish between mutant sperm cells and those that are not Epsilon tubulin mutants in the Tube1GCKO/GCKO mice. E.g., are the 28.07% of Tube1GCKO/GCKO tubules that showed a Sertoli cell only (SCO) phenotype the one where all the cells are mutants? *

Response: As per our response to Reviewer 2’s comment above, we plan to test a new TUBE1 antibody to determine TUBE1 localization in this model. Outlined in our response to Reviewer 2 below, we also plan to sequence DNA from mature epididymal sperm from our mutant mice to further confirm the deletion of Tube1 exon 3.

Reviewer 2:* The generated conditional germ cell-specific mutants are demonstrated by mRNA expression spermatocytes. It would help if DNA sequencing, western, and Immunohistochemical staining were used to show the gene and protein are affected. *

Response: We thank Reviewer 2 for their suggestions. Should we successfully validate an appropriate TUBE1 antibody for use in our model, we will perform immunohistochemical staining during the revision process. Our qPCR results from purified spermatocytes however, strongly suggest that the Tube1 gene is deleted in our model, noting that such purifications are on average 81% pure with the major contaminants being Sertoli cells and spermatids (Dunleavy et al., 2019). To further confirm the deletion of Tube1 exon 3, we plan to sequence DNA from mature epididymal sperm from our mutant mice.

Reviewer 2:* "Suggesting a core TUBE1 function that can be supplemented by either z-tubulin or TUBD1." Can you test what happens to mice Z and D tubulin isoforms in the mutant? Did their level increase in the centrioles? This is informative since there is no clear centriolar phenotype (other than centriole number that may be due to cell division failure) in mice spermatogenesis and the paper's central hypothesis in the introduction. *

Response: We appreciate this question by Reviewer 2. Zeta tubulin is not present in the mouse genome as outlined in our introduction (lines 38-39). We do acknowledge that exploring Tubd1 will be informative in our mutant and thereby plan to examine its expression in round spermatids.

Reviewer 2: The authors looked at the Metaphase stage cells to assess meiosis. It would be more interesting to look at the meiosis prophase I. Since the Stra8 acts very early leptotene stage, it would be interesting to see if meiosis is defective from the very beginning. Also, some suggest that the manchette is nucleated at the pachytene stage. Is the manchette defective from the very early stage of nucleation?

Response: We thank Reviewer 2 for this suggestion. To this end, we plan to examine juvenile mouse testes at days 10 and 17 post-partum where leptotene and pachytene spermatocytes are the most mature germ cells respectively.

In regard to the Reviewer’s comment of the manchette being nucleated in pachytene stage spermatocytes, we acknowledge that the precise mechanism of manchette nucleation has not been confirmed. We are aware of the alternative hypothesis introduced by Moreno and Schatten (2000), which postulates manchette microtubules may be nucleated prior to pachytene period, through their examination of bovine male germ cells. This hasn’t, however, been supported by evidence and with more recent data, others have suggested that the manchette is nucleated at the centrosomal adjunct (Lehti and Sironen, 2016). Indeed, our unpublished data suggests this is the case (another study). Regardless, the origin of the microtubule seeds that ultimately extend to form the manchette is not relevant to the hypothesis we have proposed. As we note that in our manuscript and mouse model, manchettes appear to assemble normally in step 8 spermatids. Rather, their movement and disassembly is abnormal i.e. TUBE1 serves critical roles more manchette movement and disassembly rather than manchette formation.

Reviewer 2:* Is the acetylation of manchette microtubules affected in the absence of TUBE1? *

Response: Reviewer 2 raises an interesting question, which we plan to answer through immunolabeling of testis sections for acetylated tubulin in our control and mutant groups.

Reviewer 3: *Minor points, a substantial percentage of sperm produced had a normal head shape in the KO (Figure 1I), which undermine the function of tube1 in nuclear shaping, the author should address this point in their manuscript. It is also curious whether there are phenotype in other tissues, can the authors comment on that? *

Response: We thank Reviewer 3 for highlighting this point. As reported in Fig. 1I, 28.5% of sperm from Tube1GCKO/GCKO epididymides have abnormal nuclear shape. This is a 4.4-fold increase over that seen in wild type sperm. These data clearly highlight the role of TUBE1 in defining nuclear morphology. Variations between cells does not undermine this conclusion. It appears that prior to sperm release from the testis, the majority of TUBE1 null spermatids heads are abnormally shaped. However, in the epididymis there appears to be an increase in the proportion of normally shaped heads. We thus hypothesize that the high rates of spermiation failure in the TUBE1 null mice reflect the preferential removal of abnormally shaped sperm by Sertoli cells, thus enriching for normally shaped heads that are released. During the revision process, we will quantify the percentage of spermatids with normal versus abnormally shaped heads prior to spermiation in testis sections. All Tube1 null mice were sterile.

To Reviewer 3’s second point - we have not examined other tissues in this conditional male germ cell knockout mouse model, as the cre used in this manuscript is only expressed in the testis (Sadate-Ngatchou et al., 2008). Consistent with the specificity of the deletion, null male mice are overtly healthy, with the exception of male fertility, and exhibit normal body weight as detailed on line 123 and in Fig S1D.

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

Reviewer 1:* In figure 5, based on quantification of fluorescence intensity, the authors conclude that loss of epsilon-tubulin results in an increase in the levels of KATNAL1, KATNAL2, and KATNB1. Given the inherent variability in immunofluorescence staining, the authors should at a minimum normalize their intensity measurements to those of an unrelated control protein stained in the same cell (ex: alpha-tubulin). It would be more convincing to quantify the levels of these proteins by Western blot (again, normalized to a control protein or to total cellular protein), which should be feasible given that the authors can isolate elongating spermatids. *

Response: We thank Reviewer 1 for this suggestion to better account for any potential variability between immunofluorescence staining in cells. In this instance, alpha-tubulin would be a related protein in our model, making it unsuitable for normalization - the longer manchette phenotypes in our mutant spermatids indicate more tubulin present in mutant cells. We have therefore normalized the fluorescence intensity in our cells to DNA content (DAPI staining). This has provided comparable results to our initial analysis, and we have edited our text accordingly at lines 303, 307-310, 563-564, 845, 850 and Fig. 5. We respectfully disagree that western blotting would be informative, as the point is that katanin proteins are accumulating abnormally on the elongating sperm manchette. This does not necessarily mean that overall katanin levels will be increased. This aside, given the low numbers of elongating spermatids in the Tube1GCKO/GCKO mice, obtaining sufficient materials of western blotting is prohibitive. With the severity of germ cell loss indicated by our daily sperm production calculations, we predict the isolated spermatids of up to 5 Tube1GCKO/GCKO animals would be required to make up one biological replicate. It would not be feasible to collect the large number of animals required for at least three biological replicates in the revision timeframe.

Reviewer 1:* A major claim of the paper is that epsilon-tubulin plays a different role within mammalian germ cells (abstract, line 22; p9, lines 167-168; p15 lines 315-316), because the Tube1GCKO/GCKO mice can form some sperm with relatively normal ciliary ultrastructure, whereas ciliates lacking epsilon-tubulin fail to form cilia. However, it's unclear whether the centrioles that templated these normal cilia were formed before or after epsilon-tubulin loss. Given that centrioles are inherited from one generation to the next, it's possible that the few normal cilia may be templated by relatively normal parental centrioles. These parental centrioles would have been present in spermatogonia prior to Cre expression/epsilon-tubulin deletion, and inherited by a fraction of sperm after the mitotic and meiotic divisions, resulting in sperm with normal ciliary ultrastructure. Other spermatocytes may have inherited centrioles formed in the absence of epsilon-tubulin, resulting in aberrant centrioles similar to those reported in human somatic cells, but these would not form any sperm flagella due to a loss of cell viability, as has been reported for acentriolar cells in a p53+ background. Underscoring this point, Chlamydomonas and human somatic mutant cells constitutively lack epsilon-tubulin. In these systems, the parental centrioles were diluted from the population over many cell divisions, and phenotypic analysis would only include the centrioles that formed in the absence of epsilon-tubulin. To make their major claim, the authors need to demonstrate that the basal bodies of sperm flagella with normal ultrastructure were formed in the absence of epsilon-tubulin, and were not normal parental centrioles. Given the difficulty of this experiment, the authors may instead choose to remove their claim that epsilon-tubulin plays a different role within mammalian germ cells. *

Response: The authors thank Reviewer 1 for their detailed input regarding TUBE1’s centriolar importance across species. From their feedback, we recognize the need to modulate our interpretation of this result. We have also added a line to our manuscript highlighting that the normal axonemal structure observed may be due to the inheritance of normal centrioles (lines 328-329). We note however, that sperm produced within the null animals were immotile and that motility could not be recovered by the addition of exogenous ATP thus revealing that TUBE1 is required to form functional sperm tails.

Reviewer 2:* It will help if the introduction summarizes the knowledge on Epsilon tubulin in spermatogenesis with emesis on its localization and the method used to find the localization. *

Response: We have modified the introduction accordingly in lines 72-73.

Reviewer 2:* How many independent mutant animals were studied, and what was the elfishness of generating mutants with a complete mutant testis? From Fig s1c, it appears all mutants generated were total mutations in almost all cells - is this correct? *

Response: We have updated the number of animals studied as per the comment below. Regarding the mutant status of our mouse model, we used Stra8-Cre which is active between early (postnatal day 3) spermatogonia to pre-leptotene spermatocytes (Sadate-Ngatchou et al., 2008) thus all spermatocytes, spermatids, and sperm will carry the deletion. As shown in Fig. S1C we measured a 90.1% reduction in Tube1 mRNA expression from purified spermatocytes. As mentioned above, we note that the purified germ cells always contain a low percentage of contaminating cells. Using our optimized Staput method we obtain isolated germ cell populations of high purity, where in spermatocyte populations we calculate 19% contamination with other testicular cell types (e.g. somatic Sertoli/interstitial cells, spermatogonia, spermatids) (Dunleavy et al., 2019). We therefore believe the 9.9% Tube1 mRNA expression detected in our Tube1GCKO/GCKO group are the origin of that residual mRNA. We have included this information in the materials and methods section (lines 491-493).

Reviewer 2:* Add a definition to "ZED-tubulins." *

Response: A definition to the ZED-tubulins can be found on line 32.

Reviewer 2:* From the paper, it is unclear if Epsilon tubulin is dispensable for centriole function only in sperm cells or if the same is true in mice somatic cells in vivo. *

Response: In this study we have used a conditional male germ cell knockout mouse model to examine TUBE1’s function specifically in male germ cells. As mentioned in our introduction, the function of TUBE1 has not been examined in murine somatic cells in vivo (lines 68-70). To avoid confusion, we have reiterated this point in lines 356-358 of our discussion.

Reviewer 2:* Fig. S1 and other figures: "n {greater than or equal to} 3 samples/genotype" - this is unclear - please indicate the number of independent animals tested. *

Response: We have modified the figure legends accordingly in lines 11-13 and 33-35 of the transferred supplementary information file and lines 787-788 and 810-811 of the transferred manuscript file.

Reviewer 2:* "suppressing supernumerary centriole formation" is this due to access centriole formation or failed mitosis? *

Response: We acknowledge Reviewer 2’s comment is similar to the comment made by Reviewer 1 above and note we have modified the associated text in lines 207-209 in response to the above comment.

Reviewer 2:* The KATNAL1, KATNAL2, and KATNB1 staining in Fig 5 show multiple foci in the nucleus. Are these foci-specific staining or nonspecific? It is surprising to see such a large complex. *

Response: As outlined in the materials and methods and the Fig. 5 legend, Fig. 5 displays three-dimensional (3D) z-stack images of whole elongating spermatids presented as 2D maximum intensity projections. The katanin subunit staining is around the nucleus rather than inside of it, however the flattening of the image from 3D to 2D make the foci appear inside the nucleus. To clarify this, we have modified the Fig. 5 legend in lines 845 and 848.

Reviewer 2:* How the staging of spermatids was performed needs to be explained in the method. *

Response: We have included additional explanation the materials and methods section (lines 513-514).

Reviewer 3: The experimental part is of the highest quality and the manuscript is very well written. My only reservation with the manuscript is concerning the model proposed for manchette migration in the Discussion section (Figure 6). I find the proposed model highly speculative and pre-mature, not supported enough by data, as even admitted by the authors (lines 415-427). Having it as a figure and concluding remark gives it too match weight, my suggestion would be to remove figure 6 and tone down the discussion.

Response: The authors thank Reviewer 3 for their complimentary overview of our manuscript. We agree that some unanswered questions remain in our proposed model of manchette migration. This study has however, added several critical missing pieces. With respect, we prefer to keep Figure 6 in the manuscript as explaining manchette function to non-experts is very difficult without a visual aide. To ensure transparency with the audience that our model is indeed hypothetical, we have edited our discussion and Figure 6 legend to reflect this (lines 406, 417, 428, 435, 463, 860, 863, 869).

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

None

References

DUNLEAVY, J. E., GRAFFEO, M., WOZNIAK, K., O’CONNOR, A. E., MERRINER, D. J., NGUYEN, J., SCHITTENHELM, R. B., HOUSTON, B. J. & O’BRYAN, M. K. 2022. Male mammalian meiosis and spermiogenesis is critically dependent on the shared functions of the katanins KATNA1 and KATNAL1. bioRxiv, 2022.11.11.516072.

DUNLEAVY, J. E. M., O’CONNOR, A. E. & O’BRYAN, M. K. 2019. An optimised STAPUT method for the purification of mouse spermatocyte and spermatid populations. Molecular Human Reproduction.

DUNLEAVY, J. E. M., OKUDA, H., O’CONNOR, A. E., MERRINER, D. J., O’DONNELL, L., JAMSAI, D., BERGMANN, M. & O’BRYAN, M. K. 2017. Katanin-like 2 (KATNAL2) functions in multiple aspects of haploid male germ cell development in the mouse. PLOS Genetics, 13.

LEHTI, M. S. & SIRONEN, A. 2016. Formation and function of the manchette and flagellum during spermatogenesis. Reproduction, 151__,__ R43-54.

MORENO, R. D. & SCHATTEN, G. 2000. Microtubule configurations and post-translational alpha-tubulin modifications during mammalian spermatogenesis. Cell Motil Cytoskeleton, 46__,__ 235-46.

SADATE-NGATCHOU, P. I., PAYNE, C. J., DEARTH, A. T. & BRAUN, R. E. 2008. Cre recombinase activity specific to postnatal, premeiotic male germ cells in transgenic mice. Genesis, 46__,__ 738-42.

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Referee #3

Evidence, reproducibility and clarity

In this study Stathatos et al looked at the function of epsilon tubulin (tube1), specifically in male germ cells. Previous work showed that tube1 is an important member of the tubulin family but its function is more enigmatic compared to alpha, beta and gamma tubulin. The authors produced a mouse KO line of tube1 and the data presented in this manuscript concerns the effects on spermatogenesis. They found that tube1 is essential for multiple microtubule dependent functions, including meiosis, nuclear shaping and sperm motility.

The experimental part is of the highest quality and the manuscript is very well written. My only reservation with the manuscript is concerning the model proposed for manchette migration in the Discussion section (Figure 6). I find the proposed model highly speculative and pre-mature, not supported enough by data, as even admitted by the authors (lines 415-427). Having it as a figure and concluding remark gives it too match weight, my suggestion would be to remove figure 6 and tone down the discussion. Minor points, a substantial percentage of sperm produced had a normal head shape in the KO (Figure 1I), which undermine the function of tube1 in nuclear shaping, the author should address this point in their manuscript. It is also curious whether there are phenotype in other tissues, can the authors comment on that?

Significance

The observations reported are novel and will be highly valuable specifically for the sperm biology field but also very interesting to the microtubule field in general.

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Referee #2

Evidence, reproducibility and clarity

The paper "Epsilon tubulin is an essential determinant of microtubule-based structures in male germ cells" provides the first insight into the essential function of Epsilon tubulin. TUBE1 (epsilon tubulin) is a non-canonical tubulin localized at the pericentriolar material of somatic and germ cell centrosome. TUBE1 has been primarily studied in unicellular organisms and cell lines, and multiple studies have shown its role in ciliogenesis and flagellum formation. However, its role in mammals, specifically in fertility, is unknown. Here, Stathatos et al address the critical question of whether TUBE1 plays a role in mammalian spermatogenesis and fertility. The authors show by germline inactivation of TUBE1 that the mice lacking TUBE1 are sterile, defective in meiosis, form abnormal manchette, and sperms are nonmotile. The authors further correlate that the TUBE1 functions together with KATNAL-1, KATNAL-1, and KATNB1, the microtubule severing protein. As little is known about the role of non-canonical tubulin like TUBE1 in fertility, this manuscript addresses a significant knowledge gap and generates an exciting hypothesis that TUBE1 regulates the KATNAL1-KATNB1 and KATNAL2-KATNB1 dynamic at manchette microtubules and perinuclear ring to control the manchette microtubule severing and migration.

Overall, the paper suggests that Epsilon tubulin is essential for multiple complex microtubule arrays, including the meiotic spindle, axoneme, and manchette; however, in the absence of Epsilon tubulin localization data, it is unclear which microtubule array is affected directly and which indirectly (e.g., is the axoneme defect is due to Epsilon tubulin in the axoneme or centriole?). In particular, it is interesting that in mice sperm, Epsilon tubulin is dispensable for centriole-mediated axoneme formation, its primary function in single-cell organisms (can this be due to compensation by the other tubulin isoforms?). Once the concerns below are resolved, the paper will be significant for the cytoskeleton and reproductive research fields.

Major comment

• Considering the suggested non-canonical function of Epsilon tubulin outside the centriole in mice sperm, it is critical to know the localization of the protein in spermatocytes during meiosis and spermatids during differentiation.
• Localization of Epsilon tubulin is needed to distinguish between mutant sperm cells and those that are not Epsilon tubulin mutants in the Tube1GCKO/GCKO mice. E.g., are the 28.07% of Tube1GCKO/GCKO tubules that showed a Sertoli cell only (SCO) phenotype the one where all the cells are mutants?

Minor comment

• It will help if the introduction summarizes the knowledge on Epsilon tubulin in spermatogenesis with emesis on its localization and the method used to find the localization.
• The generated conditional germ cell-specific mutants are demonstrated by mRNA expression spermatocytes. It would help if DNA sequencing, western, and Immunohistochemical staining were used to show the gene and protein are affected.
• How many independent mutant animals were studied, and what was the elfishness of generating mutants with a complete mutant testis? From Fig s1c, it appears all mutants generated were total mutations in almost all cells - is this correct?
• Add a definition to "ZED-tubulins."
• "Suggesting a core TUBE1 function that can be supplemented by either z-tubulin or TUBD1." Can you test what happens to mice Z and D tubulin isoforms in the mutant? Did their level increase in the centrioles? This is informative since there is no clear centriolar phenotype (other than centriole number that may be due to cell division failure) in mice spermatogenesis and the paper's central hypothesis in the introduction.
• From the paper, it is unclear if Epsilon tubulin is dispensable for centriole function only in sperm cells or if the same is true in mice somatic cells in vivo.
• Fig. S1 and other figures: "n {greater than or equal to} 3 samples/genotype" - this is unclear - please indicate the number of independent animals tested.
• "suppressing supernumerary centriole formation" is this due to access centriole formation or failed mitosis?
• The KATNAL1, KATNAL2, and KATNB1 staining in Fig 5 show multiple foci in the nucleus. Are these foci-specific staining or nonspecific? It is surprising to see such a large complex.
• How the staging of spermatids was performed needs to be explained in the method.
• The authors looked at the Metaphase stage cells to assess meiosis. It would be more interesting to look at the meiosis prophase I. Since the Stra8 acts very early leptotene stage, it would be interesting to see if meiosis is defective from the very beginning. Also, some suggest that the manchette is nucleated at the pachytene stage. Is the manchette defective from the very early stage of nucleation?
• Is the acetylation of manchette microtubules affected in the absence of TUBE1?

Significance

Overall, the paper suggests that Epsilon tubulin is essential for multiple complex microtubule arrays, including the meiotic spindle, axoneme, and manchette; however, in the absence of Epsilon tubulin localization data, it is unclear which microtubule array is affected directly and which indirectly (e.g., is the axoneme defect is due to Epsilon tubulin in the axoneme or centriole?). In particular, it is interesting that in mice sperm, Epsilon tubulin is dispensable for centriole-mediated axoneme formation, its primary function in single-cell organisms (can this be due to compensation by the other tubulin isoforms?). Once the concerns are resolved, the paper will be significant for the cytoskeleton and reproductive research fields.

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Referee #1

Evidence, reproducibility and clarity

The ZED (zeta-, epsilon-, and delta-) tubulins are important, yet understudied, members of the tubulin superfamily. Here, Stathatos et al. build upon previously published work and leverage their expertise to uncover the roles of epsilon-tubulin in mouse male germ cells. The authors create a germ cell-specific Tube1 knockout mouse, using Stra8-Cre, which is active in spermatogonia before the meiotic divisions. The authors report that knockout of Tube1 results in a range of defects during spermatogenesis, including: 1) a loss of male germ cells 2) sperm motility defects 3) abnormally shaped sperm heads 4) abnormal meiotic spindle morphology and abnormal centrosome numbers 5) some defects in sperm axoneme ultrastructure, 6) disrupted manchette migration 7) increased levels of katanin subunits at the manchette. Most of the experiments are convincing and well done, and based on this work, the authors propose a novel model for regulation of the manchette. I believe this work is of interest and should be published with revisions addressing the following major and minor comments.

Major comment:

1. A major claim of the paper is that epsilon-tubulin plays a different role within mammalian germ cells (abstract, line 22; p9, lines 167-168; p15 lines 315-316), because the Tube1GCKO/GCKO mice can form some sperm with relatively normal ciliary ultrastructure, whereas ciliates lacking epsilon-tubulin fail to form cilia. However, it's unclear whether the centrioles that templated these normal cilia were formed before or after epsilon-tubulin loss. Given that centrioles are inherited from one generation to the next, it's possible that the few normal cilia may be templated by relatively normal parental centrioles. These parental centrioles would have been present in spermatogonia prior to Cre expression/epsilon-tubulin deletion, and inherited by a fraction of sperm after the mitotic and meiotic divisions, resulting in sperm with normal ciliary ultrastructure. Other spermatocytes may have inherited centrioles formed in the absence of epsilon-tubulin, resulting in aberrant centrioles similar to those reported in human somatic cells, but these would not form any sperm flagella due to a loss of cell viability, as has been reported for acentriolar cells in a p53+ background. Underscoring this point, Chlamydomonas and human somatic mutant cells constitutively lack epsilon-tubulin. In these systems, the parental centrioles were diluted from the population over many cell divisions, and phenotypic analysis would only include the centrioles that formed in the absence of epsilon-tubulin. To make their major claim, the authors need to demonstrate that the basal bodies of sperm flagella with normal ultrastructure were formed in the absence of epsilon-tubulin, and were not normal parental centrioles. Given the difficulty of this experiment, the authors may instead choose to remove their claim that epsilon-tubulin plays a different role within mammalian germ cells.

Minor comments:

1. The authors claim that because the TUBE1 knockout mouse have abnormal centrosome numbers during meiosis, there is a role for TUBE1 in suppressing supernumerary centriole formation. While this is one possibility, it's also possible that abnormal centrosome numbers arose as a result of cell division defects, especially because binucleate cells are present in mutants. The authors should edit the text to state that abnormal centrosome numbers may arise from either supernumerary centriole formation (by the templated or de novo pathways) or from failure to complete cell division.

OPTIONAL: to test these possibilities, the authors may choose to 1) count the number of centrioles in meiosis with two different centriole markers 2) stain for markers of mature centrioles, such as Cep164, to determine the number of parental centrioles. 2. In figure 5, based on quantification of fluorescence intensity, the authors conclude that loss of epsilon-tubulin results in an increase in the levels of KATNAL1, KATNAL2, and KATNB1. Given the inherent variability in immunofluorescence staining, the authors should at a minimum normalize their intensity measurements to those of an unrelated control protein stained in the same cell (ex: alpha-tubulin). It would be more convincing to quantify the levels of these proteins by Western blot (again, normalized to a control protein or to total cellular protein), which should be feasible given that the authors can isolate elongating spermatids.

Significance

The strengths of this study lie in the careful phenotypic analysis of loss of epsilon-tubulin, which is well-done and very thorough. The limitations of the study are in interpretation of the results, specifically as relates to centriole formation, but can be addressed as indicated above. This work will be of interest to cell and developmental biologists, especially those interested in centrosomes, cilia, and spermatogenesis.

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Reply to the reviewers

Reviewer 1 major comments:

The authors show one configuration of the E1-E2 heterodimer in Figure 4d. As shown, the E1 protein is exterior to the E2 protein and would suggest E1 is on the surface on the spike complex and virus surface. However, another configuration of the glycoproteins has E2 on the exterior of E1 and also on the exterior of the virus. The latter conformation is what has been observed in cryoEM studies of alphaviruses. The first configuration represents the E1-E2 between the three heterodimers which are important for spike assembly. The reason the orientation of the E2-E1 dimer is important is the authors speculate on the importance of the 6 CHIK residues not found in ONNV based on the structure, but the structural interpretation is, in my opinion, not correct.

We thank reviewer 1 for pointing out the correct E2-E1 heterodimer configuration. To address this, we corrected the position of E2 and E1 in Figure 4 based on previous cryoEM study1, keeping E2 always on the exterior in the E2-E1 heterodimer. We also replaced the Indian Ocean Lineage (IOL) E2-E1 structure1 in the original Figure 4 with the CHIKV 181/clone 25 structure which was recently analyzed by Katherine Basore et al.2. In a single E2-E1 heterodimer, all six unique CHIKV positive selection sites are located on the outside of the structure after correcting the configuration. In addition, we investigated two of the unique CHIKV positively selected sites that are important for virion production, E2-V135 (V460 in the original manuscript version) and E1-V220 (V1029 in the original manuscript version), in trimerized structure of E2-E1 heterodimers. We found that the E2-V135 and E1-V220 residues in one heterodimer are facing E2 of the neighboring heterodimer on either side. Interestingly, while V135 is embedded between the E2 proteins of two different heterodimers, E1-V220 is partially embedded by E1 and the neighboring E2 and partially exposed to the outside. This suggests that even though both E2-V135 and E1-V220 might be crucial for CHIKV E2-E1 trimerization, E1-V220 provides an additional docking site for host factor interactions. We thank review 1 again for this important comment leading to these new findings. We have updated Figure 4F-4G and the corresponding result section (lines 201-209) in this partially revised manuscript.

1. Validation of E1 interaction with SPSC3 and eIF3k needs to be stronger. Some concerns/questions are listed below. A myc tag was inserted between E3 and E2. How efficiently does furin cleave E3 from E2 in this virus and how are viral titers of the myc-tagged virus compared to the non-tagged virus? I ask because is the IP looking at what is being pulled down by E2 or E3-myc-E2 that could be part of the spike polyprotein? The authors found E2 interacts with E3, E1 and a list of other host proteins. These results suggest several interactions including E2-host factor, E2-E1, E2-E3, E2-E1-host factor, E2-E3-E1, E2-E3-host factor. In figure 6d, and the subsequent conclusions, the authors suggest E1 is interacting with the host factor and do not see E2 alone and very low amounts of E3-E2-6K-E1. based on how the IP was performed I am not sure how an interaction between E1 and SPCS3 alone, without E2, would be detected. I would also like to see a reciprocal pull down using E1 and also E2 to see if these host factors are pulled down.

We thank the reviewer for these concerns. Given the low viral protein expression in macrophages (Figure 1A), we need an efficient system to enrich for large amounts of CHIKV glycoproteins for identifying host interactors through mass spectrometry. Adding tag/reporter proteins, such as mCherry, between E3 and E2 have been used to label alphavirus glycoproteins in previous study2, which is why we chose to use this myc tag labeling strategy coupled with myc Ab-conjugated agarose beads for AP-MS. However, like reviewer 1 speculated, inserting myc tag between E3 and E2 does attenuate CHIKV infectivity according to the reduced supernatant viral titers of 293T cells transfected with CHIKV/myc-E2 genomic RNA in comparison to those of cells transfected with unmodified CHIKV vaccine strain 181/clone 25 genomic RNA (shown in revision plan). Despite the attenuation, CHIKV/myc-E2 harvested from transfected 293T cells still reaches a titer over 108 pfu/ml, which allowed us to identify interactors by AP-MS.

We further analyzed the cleavage efficiency of glycoproteins by comparing the expression levels of E3-E2-6K -E1, E3-E2 (p62), E2, and E3 in 293T cells transfected with unmodified CHIKV or CHIKV/myc-E2 genomic RNA (result shown in revision plan). We didn’t detect any uncleaved forms of glycoproteins in cells transfected with either unmodified CHIKV or CHIKV/myc-E2 RNA when we probed with E2 antibody. However, probing with E3 antibody prior to longer exposure of the immunoblot showed higher E3-E2-6k-E1 and E3-E2 (p62) levels in cells transfected with CHIKV/myc-E2 RNA, suggesting that both mature E2 and E2-containing precursor polyproteins are available to be pulled down. Overall, the expression levels of mature E2 detected by E2 antibody are similar.

We thank reviewer 1 for providing a thorough dissection of all the possible interactions between the identified host factors and cleaved/uncleaved glycoproteins. This is a very interesting question. As reviewer 1 mentioned that E1 usually appears with E2 or E3-E2 in heterodimer forms, we were also surprised to find that E2 does not interact with either of the two host factors. To address this, we plan to conjugate E2 and E1 to protein A/G beads, respectively, for a reciprocal pulldown to validate CHIKV glycoprotein interactions with SPCS3 and eIF3k. Results from this experiment will be included in the fully revised manuscript.

1. If CHIK E1 is interacting with the host factors and that is antagonizing the antiviral response of SPSC3 (as one example), then what do pull downs using ONNV structural proteins look like? One would expect reduced interactions because the different amino acid causes a different E2-E1 dimer or attenuates the E1-host factor binding site.

We thank Reviewer 1 for this insightful suggestion. We agree that it would be informative to examine the interactions between ONNV glycoproteins and identified host factors (SPCS3 and eIF3k). Unfortunately, there is no commercial ONNV glycoprotein antibody available making this experiment unfeasible. Interestingly, we did observe reduced interactions between the host factors SPCS3 and eIF3k and the CHIKV E1-V220I mutant (V1029I in original manuscript version) where the positively selected site in E1 was mutated to the homologous ONNV residue (please refer to our response to Reviewer 3’s major comment #1). This result suggests that the ONNV glycoproteins likely have an attenuated E1-host factor binding site as the reviewer speculated.We have included this as Figure 7A in partially revised manuscript.

1. E1 and E2 are thought to interact during polyprotein translation and the initial dimer forms in the ER. If E1 is interacting with SPSC3 in the ER, is E2 also present? Or is a population of E1 not interacting with E2 in order to inhibit SPSC3? I would love a model of how the authors see all these factors coming together for this new role of E1.

We thank Reviewer 1 for proposing this interesting hypothesis. Given the unexpected absence of E2 in our validation of host factor-E1 pulldown, we speculate that a group of free E1 proteins with distinct function is interfering with host factors in the ER, which is a model worth further investigation and discussion. A great example of this is the alphavirus nonstructural protein 3 (nsP3) that plays essential roles in RNA replication, although depending on the alphavirus not all of the nsP3 in the cell colocalizes with dsRNA, suggesting there is a separate distinct pool of nsP3 outside of active viral replication complex that interacts with host factors in these observed larger cytoplasmic aggregates3. To address this, we plan to use laser confocal microscopy to observe the interactions between host factors (SPCS3, eIF3k), and CHIKV E2 and E1. We will include this result as well as our proposed model in the fully revised manuscript.

Reviewer 1 minor comments:

1. In Figure 1c, (-) RNA is shown but in the rest of the figures (+) RNA is shown. Show both or select one. I do find it interesting the (-) RNA levels are similar over time, even at 4 hours post transfection (early time). Related to this, ONNV has higher levels of (-) RNA but what is known about structural protein levels in ONNV and CHIK in macrophages? Are there comparable levels of CP and GP being produced?

We thank Reviewer 1 for this comment. The (-) RNA is synthesized before the synthesis of subgenomic mRNA and therefore can reflect more accurately early viral replication and nonstructural protein functions. This is the reason why we consider the (-) RNA levels evaluated by specific nsP1 TaqMan probes to be more appropriate for determining early stage differences between ONNV and CHIKV replication in Figure 1 as the goal of that figure is to define the steps in CHIKV life cycle that are more efficient than those of ONNV in THP-1 derived macrophages. On the other hand, the (+) RNA evaluated by E1 primers that we used in the later figures monitors viral RNA synthesis over time in the reflection of genomic (+) RNA and subgenomic mRNA transcribed from (-) RNA templates. Similar levels of (+) RNA and contrasting virion titers really point the difference to the later stages of subgenomic mRNA translation, viral glycoprotein secretion, and assembly.

We have generated ONNV/myc-E2 reporter virus and assessed viral glycoprotein expression through flow cytometry using a FITC -conjugated anti-myc antibody in the THP-1 derived macrophages transfected with CHIKV/myc-E2 and ONNV/myc-E2 (shown in revision plan). The results show that the expression of ONNV glycoproteins is more inhibited than that of CHIKV glycoproteins, though both of their expression levels in macrophages seem to be suppressed. Since there is no commercial ONNV antibody available, we were unable to compare capsid expression levels between the two viruses. Overall, differences in the myc-tagged glycoprotein expression levels of the two viruses reveals ONNV defect in either structural protein translation or glycoprotein maturation .

1. Figure 2e and figure 3 have ONNV has the first bar followed by CHIK. In figure 1 and 2b, CHIK is first and then ONNV. helps the reader to have the controls in the same order.

We thank Reviewer 1 for this suggestion. We have changed the order of ONNV and CHIKV bars in figure 2E and figure3 so the CHIKV bar consistently comes first in all the figures.

1. Line 143-145 the authors discuss that when ONNV is the backbone and CHIK proteins are inserted the infection is more attenuated because of the E2 and E1 are from CHIK and ONNV, not the same virus (could also be E2-CP interactions are disrupted). However the chimeras made with the CHIK backbone (in Figure 2) have a mismatch between E2 and E1 as well.

We thank Reviewer 1 for this informative comment. We agree that the incompatible E2-E1 heterodimer formation may not be the only reason that causes attenuation of ONNV/CHIKV E1 and ONNV/CHIKV E2. There may be multiple factors contributing to the fitness of the chimeras, which requires more in-depth mechanistic investigations and is out of the scope of this study. We have now removed the explanation “potentially due to incompatible heterodimer formation between ONNV E2 and CHIKV E1” in line 144.

1. When discussing the residues that were found in the FEL and MEME analysis, the authors start the amino acid numbering from CP and continue along the polyprotein. Usually when discussing amino acids in the structural proteins, each protein starts at amino acid 1. So V460 would be E2-V135. It would also be useful to know what the residues in ONNV were at these positions to see if amino acids changed in charge, size, bond forming potential, etc. Showing these residues in the E2-E1 conformation found in the virion would also allow one to find adjacent residues that could explain differences in spike assembly and potentially where/how E1 is binding to a host protein.

We thank Reviewer 1 for this comment. We revised the amino acid numbers in the manuscript to start from the beginning of each structural protein. To look more into these residues in ONNV, we aligned CHIKV and ONNV from different lineages and compared the 6 positively selected sites (refer to our response to Reviewer 1’s minor comment #5). We found that E2-135 and E1-220 which are essential for CHIKV production are valines in all the aligned CHIKV strains. For the aligned ONNV strains, E2-135 are all leucines and E1-220 are all isoleucines. While valine, leucine and isoleucine are all amino acids with hydrophobic side chains, valine has the shortest side chain. The length of the side chains may lead to different hydrophobic properties that affect protein folding, which warrants further structural analysis.

1. How effective is a non-attenuated CHIK strain in infecting macrophages? Could you make a SINV-La Reunion chimeric virus (which is BSL2) to see if a higher percentage of macrophages are infected and is this potentially contributing to the increased pathogenesis of La Reunion? Also how different is 181/25 with a pathogenic strain in the E2 and E1 residues? and compared to ONNV?

We thank Reviewer 1 for this question, which is also raised by Reviewer 2. In order to address this question, we plan to use the virulent CHIKV La Reunion strain to study the infection of THP-1 derived macrophages with non-attenuated CHIKV in BSL-3. We are getting trained in the BSL-3 facility and will soon be certified.

We thank Reviewer 1 for this insightful suggestion on investigating the conservation of these positively selected sites in different strains. We have aligned the sequences of ONNV and CHIKV strains from different lineages, including CHIKV vaccine strain 181/clone 25 and Thai strain AF15561 (the parental strain of CHIKV 181/clone 25) (alignment shown in revision plan). We found that the two positively selected sites with negative effects on virion production, E2-135 and E1-220 (sites 460 and 1029 in original manuscript version), are very conserved in either CHIKV or ONNV strains. CHIKV E2-135 is always valine (V) regardless of the lineages, while ONNV E2-135 is always leucine (L). CHIKV E1-220 is always V, while ONNV E1-220 is always isoleucine (I).

We also analyzed the amino acid heterogeneity of E2-135 and E1-220 in 397 CHIKV patient sequences from NCBI Virus database. Most of the amino acids at these 2 sites are V. The counts of each amino acid at E2-135 and E1-220 is summarized in table below. This result suggests that valine residues at E2-135 and E1-220 are crucial for CHIKV fitness and strongly selected during viral evolution. The sequence alignment and table will be included and discussed in the fully revised manuscript .

E2-135

E1-220

Valine (V)

394

392

Alanine (A)

1

3

Methionine (M)

1

0

Glutamic acid (E)

0

1

Glycine (G)

1

0

Isoleucine (I)

0

1

1. When describing the last results section, "CHIKV E1 binding proteins exhibit potent anit-CHIV activities" the authors use macrophages. In the rest of the text they consistently use THP-1 macrophages or human primary monocyte derived macrophages. The details of the cell type are extremely useful to the reader and having those in the last results section would be great.

We thank Reviewer 1 for pointing out the importance of cell type clarification in the last results section. We now consistently use “THP-1 derived macrophages” instead of “macrophages” in this section.

1. The paper is well-written. There is a slight disconnect as the authors go from discussing results in Figure 4 to Figure 5.

We thank Reviewer 1 for the comment regarding the disconnection of the last two figures in this paper which is also shared by the other reviewers. We have taken 3 approaches to address this comment: 1) We performed a pulldown of the host factors (SPCS3, eIF3k) identified in Figure 5 with CHIKV positively selected mutants examined in Figure 4 with deficient virion production. The result is presented in our response to Reviewer 3’ s major comment #1, suggesting that the positively selected site in E1 is essential for CHIKV glycoprotein interaction with host factors. 2) To complement our first experiment, we will also determine structural protein expression and processing of parental and E1 mutant CHIKV in eIF3k CRISPR knockout 293T cells. 3) Finally, we plan to perform CORUM analysis to identify high confidence functional protein complexes using our 14 hits found in both mass spec experiments, which will provide mechanistic insights into how these identified cellular complexes and processes might modulate CHIKV infection.

Reviewer 2’s major comments

The authors elegantly demonstrate that CHIKV structural proteins confer an advantage over ONNV structural proteins in a step in the replication cycle downstream of virus RNA synthesis, possibly virion assembly. This point would be strengthened determining the particle-to-PFU ratio of the parental viruses and the chimeras . Presumably, the ratio would increase in the chimeras containing CHIKV structural proteins.

We thank Reviewer 2 for this comment. We agree that determining particle-to-PFU ratios of parental and chimeric viruses will strengthen this study. To obtain the particle-to-PFU ratio, we infected THP-1 derived macrophages with CHIKV, ONNV and chimeras containing CHIKV glycoproteins (Chimera I, and ONNV/CHIKV E2+E1) for 24 h. To quantify the secreted viral particles, we extracted viral RNA in the supernatant and detected (+) viral RNA through TaqMan assay with specific nsp1 probes. The released infectious virions were evaluated through plaque assay. The particle-to-PFU ratios are summarized in the table below. The results show that ONNV has the highest particle-to-PFU ratio (41398), suggesting defective ONNV genome encapsidated in particles leading to defective virion production. On the other hand, the particle-to-PFU ratio of CHIKV (747) is 55-fold lower than that of ONNV. Replacing E3-E2-6K-E1 of ONNV with CHIKV homologous proteins reduces the particle-to-PFU ratio by 8 fold to 4875. Replacing E2 and E1 of ONNV with the ones from CHIKV (ONNV/CHIKV E2+E1) reduces the particle-to-pfu ratio by 20 fold to 2017, suggesting that CHIKV glycoproteins enhance the infectivity of viral progenies produced by THP-1 derived macrophages. We have included the results in Figure 3D-3E in our partially revised manuscript and described in lines 149-158.

1. Additionally, the authors should consider performing virion assembly blocking assays with a small molecule inhibitor to determine if this abrogates the virus production advantage of CHIKV structural proteins within the ONNV backbone.

We thank Reviewer 2 for this insightful comment. As the secretory pathway is commonly important for alphavirus glycoprotein maturation and assembly, it will be informative to interrogate CHIKV glycoprotein trafficking and assembly through this pathway using specific inhibitors, such as dihydropyridine FLI-06 and golgicide A . Golgicide A is a reversible inhibitor of the cis-Golgi GBF1, which leads to rapid disassembly of the Golgi and trans-Golgi network (TGN)4. FLI-06 is a new inhibitor that interferes with cargo recruitment to ER-exit sites and disrupts Golgi without depolymerizing microtubules or interfering GBF15. We pretreated THP-1 derived macrophages with 10 uM FLI-06 or golgicide A for 30 mins prior to infection with CHIKV, ONNV, Chimera I, or ONNV/ CHIKV E2+E1. After 1 hour of virus adsorption in PBS with 1% FBS in the absence of the inhibitors, the cells were treated with the inhibitors at the same concentration (10uM) in complete medium for 24 h. The plaque assay result shows that all the viruses are sensitive to secretory pathway inhibition, however, the production of viruses containing CHIKV glycoproteins is significantly more attenuated by FLI-06 and golgicide A. This suggests that CHIKV glycoproteins-mediated trafficking and assembly is more heavily dependent on the host secretory pathway . We will include this result in the fully revised manuscript.

1. Finally, the authors should perform competition experiments with the chimeric viruses and ONNV in macrophages to determine if the chimeras can outcompete the parental ONNV strain. Based on their data, the chimeric viruses should outcompete.

We thank Reviewer 2 for this inspiring suggestion. The competition experiment is an innovative and informative way to evaluate whether CHIKV glycoproteins confer a selective advantage on virion production in THP-1 derived macrophages. We plan to infect THP-1 derived macrophages with ONNV and ONNV/CHIKV E2+E1 and detect the viral glycoproteins secreted in the supernatant by western blot, although there is a possibility that this experiment might not work due to superinfection exclusion. Given that there is no commercial antibody of ONNV available, we need to use tagged viruses for this competition experiment. We constructed ONNV/CHIKV myc-E2+E1 that has a myc tag at the N-terminus of CHIKV E2, and ONNV/HA-E2 that has a HA tag at the N-terminus of ONNV E2. Our first attempt at concentrating the viral progenies released by THP-1 derived macrophages infected with the two tagged viruses has not been successful. We performed sucrose gradient ultracentrifugation of the supernatant viral particles but the myc and HA tags were not detected in the expected sucrose layer. Next, we plan to use myc-Ab and HA-Ab conjugated beads to pull down the supernatant viral particles to detect the ratio of ONNV/CHIKV myc-E2+E1 and ONNV/HA-E2 secreted by THP-1 derived macrophages. This will determine whether ONNV containing CHIKV glycoproteins can outcompete ONNV in co-infected cells due to increased viral fitness.

1. The authors use both primary macrophages and macrophage cell lines as their in vitro model system and make one of their major points (listed in the title) that the determinants they identified in the CHIKV structural proteins convert macrophages into dissemination vessels; however, they do not show: 1) an in vivo model that the CHIKV-ONNV chimeras disseminate more efficiently than the parental ONNV; and 2) that these chimeras generate virus more efficiently specifically in macrophages. It would be useful to show that ONNV and CHIKV have equivalent virion production in other cell lines and that the advantage conferred by CHIKV structural proteins in the ONNV backbone is specific to macrophages. The authors should also change their title to reflect that dissemination is not directly being addressed in their study; the implications of their in vitro experimentation in a mammalian host would be more appropriate for the discussion.

We acknowledge the limitations of the study, which include a lack of direct demonstration of in vivo dissemination. To address these concerns, we will include further discussion of our in vitro findings in the context of viral dissemination in mammalian hosts in the fully revised manuscript. We are also testing ONNV, CHIKV, Chimera I and ONNV/CHIKV E2+E1 infections in 293T cells to investigate whether the advantage conferred by CHIKV glycoproteins are macrophage specific.

We have also updated the title to accurately reflect the significance of this research: “Chikungunya virus glycoprotein targeting of host factors increases viral fitness in human macrophage”.

Reviewer 2’s optional comments

1. The authors use CHIKV-ONNV chimeras but it would be interesting to test other chimeras to determine if CHIKV structural proteins confer the same advantage in the backbone of other arthritogenic alphaviruses. The study would also be strengthened by using a pathogenic strain of CHIKV instead of the vaccine strain, as this is significantly attenuated in vivo.

We thank Reviewer 2 for this suggestion which is also suggested by Reviewer 1 in their minor comment #5. We plan to use virulent CHIKV La reunion strain and carry out infection experiments in BSL-3 to strengthen this study. We are getting trained in the BSL-3 facility and will be certified soon.

1. In Figure 4, the authors identify residues in the CHIKV structural proteins that appear to be under positive selection in human subjects and generate point mutants in these residues with the corresponding ONNV residues. They find that one mutation, V1029I located in E1, completely abolishes virion production in THP-1 macrophage cell lines. However, in their previous chimeric experiments, they find that neither CHIKV E1 or E2 was sufficient to increase virus production in the ONNV backbone. The authors should address this discrepancy, otherwise they should consider moving the data in their point mutation experiments to a supplementary figure. While worthy of reporting, especially given the patient data, these experiments do not buttress the points made in the previous figures.

We thank Reviewer 2 for this insightful comment. According to previous studies, E2 and E1 always interact with each other from the step of the formation of single heterodimer in the ER to heterodimer trimerization before viral particle assembly. Although the E1-V220 site (previously called V1029) on the exterior of a single E2-E1 heterodimer appears to not be engaged in the E2-E1 interaction E1-V220 is partially exposed and protruding into the groove formed by E1 and the E2 of neighboring heterodimer, accessible to host factors. As such, mutating CHIKV E1-V220 to the ONNV residue (E1-V220I) may not only disrupt E2-E1 trimerization but also interfere viral glycoprotein interaction with host factors(presented in our response to Reviewer 1’s major comment #1). Similarly, solely swapping E2 or E1 with CHIKV substitute in the ONNV backbone would also affect the interaction between neighboring E2 and E1 in trimerized spike, which may explain why neither ONNV/CHIKV E2 or ONNV/CHIKV E1 rescues virion production in THP-1 derived macrophages . We have included this in the partially revised discussion section lines __ __296-313.

1. The authors conclude their manuscript with an assessment of several host proteins, namely SPCS3 and eIF3k, that were identified by mass spectrometry and whose knockdown results in increased virion production. The authors speculate about the role of these proteins but do not provide any mechanistic detail on how they might be playing a role. It is unclear that the putative antiviral role of these proteins involves steps downstream of virus replication, especially given that the authors speculate translation might be affected by eIF3k which, if the case, RNA synthesis should also be expected to be affected.

We thank Reviewer 2 for this comment. We acknowledge that we have yet a full mechanistic understanding of how SPCS3 and eIF3k impact virion production. We plan to investigate their antiviral roles in our follow-up studies. For our partial revision, we have constructed several single eIF3k knockout (KO) clones of 293T cells. The eIF3k sgRNA we designed targets exon 3 which would eliminate expression of all 3 splice isoforms of eIF3k (KO schematic and sequence verification of CRISPR KO shown in revision plan). Unfortunately, we failed to obtain single clones of 293T cells with SPCS3 complete KO, consistent with a previous study by Rong Zhang et al6 that were unable to recover SPCS3 KO clones likely due to the importance of SPCS3 in cell survival. We infected an eIF3k KO clone (clone 9) with CHIKV vaccine strain 181/clone 25, ONNV SG650, and SINV Toto1101. Interestingly, we found that the antiviral activity of eIF3k is specific to CHIKV as CRISPR KO of eIF3k increases CHIKV production by 2.5 fold but not ONNV or SINV production (shown in revision plan). We have included this in the partially revised manuscript in__ line 272-282 (Figure 7B-7D).__

We presume that Reviewer 2’s inference of eIF3k’s potential effects on viral RNA synthesis is based on our speculation of its antiviral role in viral translation, which may affect viral nonstructural gene expression. We would like to clarify that eIF3k is not an initiation factor traditionally needed for cap-dependent translation. It is also not clear what translation process (nonstructural polyprotein translation from viral genomic RNA or structural polyprotein translation from viral subgenomic mRNA) involves eIF3k if it indeed affects viral protein expression. Notably, previous SINV studies imply that alphavirus structural polyprotein translation may employ unique mechanisms without the requirement of several crucial initiation factors4,5. It will be interesting to see whether eIF3k participates in viral subgenomic mRNA translation as that would affect viral glycoprotein expression leading to reduced virion production. We have now included additional discussion on eIF3k antiviral mechanisms in the partially revised manuscript in lines 345-353.

1. Overall, while the initial chimeric virus and domain swap approach is strong, the manuscript would benefit with a more thorough examination of virion assembly steps and a mechanistic link to virion production. Otherwise, the authors should revise the structure of their manuscript by de-emphasizing points about virion assembly and leave room for other mechanistic explanations of their chimeric data that more clearly link the host antiviral factor/E1 binding studies.

We thank the reviewer for these positive comments and suggestions. We have addressed this by further interrogating the production kinetics of CHIKV, ONNV, and the chimeras containing CHIKV glycoproteins through determining their particle-to-PFU ratios as well as treating infected cells with secretory pathway inhibitors (refer to our responses to Reviewer 2 major comments #1 and #2). We have also included additional discussion on eIF3k antiviral mechanisms specifically on how it may affect other steps of the viral life cycle in the partially revised manuscript in lines 345-353 (refer to our response to Reviewer 2 optional comment #3).

Reviewer 3’s critique comments

1. Overall, the manuscript is well written but in its current state it is more like two different stories because the effects of envelope proteins and list of interactors are not brought together in one story. A possible fix to this problem would be inclusion of ONNV and CHIKV containing env mutations that do and do not restore viral release from macrophages into the pulldown/association experiments shown in Figure 6.

We thank Reviewer 3 for the insightful suggestions to better connect the first (CHIKV determinants) and second (CHIKV glycoprotein interactors) parts of the manuscript. In response to the Reviewer’s comment, we tested the binding of SPCS3 and eIF3k to CHIKV E1 with E1-V220I (V1029I in original manuscript version) mutation (shown in revision plan) which was shown to abrogate virion production in THP-1 derived macrophages in Figure 4E. We transfected plasmids expressing 3XFLAG-tagged SPCS3/eIF3k or empty vector for 24 h followed by transfection with plasmids expressing either the parental CHIKV vaccine strain 181/clone 25 poly-glycoproteins (E3-myc-E2-6K-E1) or poly-glycoproteins with the E1-V220I mutation. Interestingly, we found that mutating CHIKV E1-V220 to the homologous ONNV residue reduces the binding to either SPCS3 or eIF3k. This result strongly suggests that the positively selected E1-V220 is located in the interaction interface between E1 and SPCS3/eIF3k, confirming the genetic conflict between E1 and these host factors to be one of the major drivers of CHIKV evolution observed at site E1-V220. We have included this result in partially revised manuscript in Figure 7A and in lines 265-271.

1. The other major issue is the lack of protein data for the viral mutants relative to WT ONNV and CHIKV and assessment of viral RNA in the supernatants to determine whether the block is release or an earlier event since viral RNA levels in the cell seems to be the same or at least normalized.

We thank Reviewer 3 for pointing out the insufficient clarification of the block leading to defective CHIKV mutant virion production. We previously detected E2 expression from 293T cells transfected with poly-glycoproteins (E3-myc-E2-6K-E1) containing E2-V135L (V460L in original manuscript version), E2-A164T (A489T in original manuscript version), E2-A246S (A571S in original manuscript version) and E1-V220I (V1029I in original manuscript version). We found that only E2-V135L mutation can lead to unexpected E2 cleavage (shown in revision plan) as we mentioned but not shown in the original manuscript. This explains why E2-V135L mutation attenuates infectious CHIKV production.

The E2 expression of E1-V220I appears to be not affected in 293T cells transfected with poly-glycoproteins with E1-V220I (shown in revision plan ). In addition, the E1-host factor binding result in our response to Reviewer 3’s major comment #1 showed that E1 with the positively selected site mutation V220I can also be successfully expressed in 293T cells after transfection with poly-glycoprotein. Based on these current data, E1-V220I mutation likely abrogates virion production without affecting glycoprotein expression.

Our previous result of the ONNV particle-to-PFU ratio reveals that ONNV RNA is released but encapsidated in defective particles causing its attenuation in infected macrophages. Thus, even though the glycoproteins of E1-V220I can be expressed, the diminished virion production of CHIKV E1-V220I can still be ascribed to 1) blocked viral particle release and 2) production of defective particles like ONNV. Given that it is not feasible to obtain particle-to-PFU ratio of E1-V220I mutant which fails to form plaques, Reviewer 3’s suggestion to assess the supernatant viral RNA will be a nice approach to address this question. To further address this concern, we plan to transfect THP-1 derived macrophages with CHIKV E1-V220I mutant RNA to detect the intracellular viral glycoprotein expression and supernatant viral RNA levels through western blot and TaqMan assay, respectively.

1. Lastly, knockdown experiments indicate an effect of things like OAS3 or other innate immune modulators. There are no controls to demonstrate that these are specific to CHIKV infection or if knockdown would assist growth of ONNV as well.

We also thank Reviewer 3 for the suggestion to check whether the identified host factors specifically target CHIKV or inhibit the infection of ONNV as well. We previously tried but were facing some issues. Since only a small fraction of macrophages can be infected with CHIKV and even a smaller fraction can be infected with ONNV (Figure 1A), it is hard to elucidate the roles of these identified host factors in ONNV infection by siRNA knockdown. We decided to take a more rigorous approach to investigate the antiviral specificity of identified host factors, especially understudied SPCS3 and eIF3k, to different alphaviruses by generating complete knockout 293T single cell clones. Despite the fact that we did not successfully generate SPCS3 complete KO, we obtained an eIF3k KO single cell clone and infected it with CHIKV, ONNV and SINV (refer to our response to Reviewer 2 optional comment #3). We found that eIF3k only has antiviral activity against CHIKV with almost no effects on ONNV or SINV infection. We have included this in our partially revised manuscript in line 272-282 (Figure 7B-7D).

Reviewer 3's minor comments:

Other points to consider:

1. The title does not fit the manuscript findings and should be modified.

We thank Reviewer 3 for this important comment, which was also brought up by Reviewer 2. We have now changed our title to “Chikungunya virus glycoprotein targeting of host factors increases viral fitness in human macrophage”, which more accurately reflects the significance of our research.

1. It is unclear why the authors show results for SINV and RRV in Figure 1. Either these should be removed or the viruses should be carried throughout the experiments described in the Figure. Better yet would be to add additional alphaviruses to this analysis to determine if there are additional viruses that act similarly to CHIKV.

We apologize for the confusion caused by including SINV and RRV results in Figure 1. We intended to show the superiority of CHIKV in infecting primary monocyte derived macrophages among arthritogenic alphaviruses, which we speculate may provide the molecular basis for macrophage-mediated CHIKV dissemination and disease. We would like to keep the SINV and RRV infection results in Figure 1 to highlight the relative susceptibility of macrophages to CHIKV. To echo the additional alphaviruses tested in Figure 1 and bring the story full circle, we included the result of SINV infection of eIF3k CRISPR KO 293T cells in Figure 7B-7D. These results uncover inhibitory activities of eIF3k that are specific to CHIKV.

1. Is the data presented in Figure 1A significant?

We thank Reviewer 3 for this question. We infected both THP-1 derived macrophages and primary monocyte derived macrophages with EGFP-expressing alphaviruses each in duplicates for two independent times. The general low expression of EGFP in all virus-infected groups refrains us from drawing conclusions based on statistically significant differences observed with MFI, hence we chose to show representative scatter plots in the original manuscript. To address Reviewers 3's question, we plotted the infected cell (EGFP+) based on the percentages of the experimental duplicates (shown in revision plan), and found CHIKV infection to be the most significantly different from that of the other alphaviruses in primary monocyte derived macrophage . The numbers above the bar charts are the mean percentages of EGFP+ cells.

1. The justification for inclusion of Figure 4A is lacking. It is unclear what this panel is supposed to be demonstrating.

This is an excellent suggestion as the host factors identified by AP-MS not only contain interactors of CHIKV mature E2 but also those of uncleaved E2-containing precursor polyproteins. We modified Figure 4A to reflect all E2/E2-containing poly-glycoproteins present in CHIKV-infected cells (shown in revision plan).

1. There is little justification for the candidates assessed in

We understand Reviewer 3’s concern. Due to the nature of mass spectrometry studies which predict protein-protein interactions rather than direct functional validation, we acknowledge that we may miss some host candidates that have anti- or pro-CHIKV activities. Although justification of hit selection from mass spectrometry datasets is more difficult than that from CRISPR KO screen datasets, we set up specific criteria to identify host protein candidates with the greatest potential to functionally interact with CHIKV glycoproteins. Most of the proteins we chose to validate (Figure 6a) were identified in both of our independent AP-MS experiments, which both pass through a P-value threshold of 0.05 and log2 fold change of 0.

1. Extended data Figure 3 is very difficult to read due to the small font size.

We apologize for the small font in Extended data Figure 3. We plan to replace Figure EV3 ( Extended data 3 in unrevised version) with a CORUM protein-protein interaction network that centers on the significant hits identified by both AP-MS experiments, but includes hits from either one of the two experiments in these functional protein complexes. The figure will be more concise and centralized, and the font will be bigger.

1. Just to be clear, the blots shown in Figure 6D are different from those depicted in Extended data Figure 4b, because some of them look very similar.

We thank Reviewer 3 for this question. In Figure 6D, we expressed CHIKV glycoproteins through transfecting CHIKV genomic RNA into 293T cells, while, in Figure 4B, we expressed CHIKV glycoproteins through transfecting poly-glycoprotein plasmid (pcDNA3.1-E3-myc-E2-6K-E1) into 293T cells, which are complementary approaches to express CHIKV glycoproteins to validate their interactions with identified host factors. We have now added schematics to illustrate the different experimental strategies above the figures in this partially revised manuscript (shown in revision plan).

References:

Voss, J. E. et al. Glycoprotein organization of Chikungunya virus particles revealed by X-ray crystallography. Nature 468, 709–712 (2010). Jose, J., Tang, J., Taylor, A. B., Baker, T. S. & Kuhn, R. J. Fluorescent Protein-Tagged Sindbis Virus E2 Glycoprotein Allows Single Particle Analysis of Virus Budding from Live Cells. Viruses 7, 6182–6199 (2015). Götte, B., Liu, L. & McInerney, G. M. The Enigmatic Alphavirus Non-Structural Protein 3 (nsP3) Revealing Its Secrets at Last. Viruses 10, 105 (2018). Saenz, J. B. et al. Golgicide A reveals essential roles for GBF1 in Golgi assembly and function. Nat. Chem. Biol. 5, 157–165 (2009). Krämer, A. et al. Small molecules intercept Notch signaling and the early secretory pathway. Nat. Chem. Biol.9, 731–738 (2013). Zhang, R. et al. A CRISPR screen defines a signal peptide processing pathway required by flaviviruses. Nature 535, 164–168 (2016).

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Referee #3

Evidence, reproducibility and clarity

Review: In this manuscript the authors generated macrophages derived from the THP-1 cell line or human peripheral blood mononuclear cells stimulated with MCSF and infected them with alphaviruses some containing GFP expression cassettes. In Figure 1, they demonstrate that CHIKV infected these cells more robustly than RRV, SINV or the related ONNV. The authors generated an extensive array of CHIKV/ONNV chimeras to identify the viral proteins that dictate release from infected macrophages and narrowed it down to the envelop proteins E1 and E2. Fine mapping identified a couple of single mutations that affected macrophage infection outcomes. The authors then shifted their approach to identifying env protein interactors using a myc-tag pulldown methods followed by mass spectrometry. The assay identified a number of proteins including those involved in vesicular transport and interferon pathways. siRNA knockdown experiments were performed to identify interactors and many of them were shown to improve virus output.

Critique: Overall, the manuscript is well written but in its current state it is more like two different stories because the effects of envelop proteins and list of interactors are not brought together in on one story. A possible fix to this problem would be inclusion of ONNV and CHIKV containing env mutations that do and do not restore viral release from macrophages into the pulldown/association experiments shown in Figure 6. The other major issue is the lack of protein data for the viral mutants relative to WT ONNV and CHIKV and assessment of viral RNA in the supernatants to determine whether the block is release or an earlier event since viral RNA levels in the cell seems to be the same or at least normalized. Lastly, knockdown experiments indicate an effect of things like OAS3 or other innate immune modulators. There are no controls to demonstrate that these are specific to CHIKV infection or if knockdown would assist growth of ONNV as well.

Other points to consider:

1. The title does not fit the manuscript findings and should be modified.
2. It is unclear why the authors show results for SINV and RRV in Figure 1. Either these should be removed or the viruses should be carried throughout the experiments described in the Figure. Better yet would be to add additional alphaviruses to this analysis to determine if there are additional viruses that act similarly to CHIKV.
3. Is the data presented in Figure 1A significant?
4. The justification for inclusion of Figure 4A is lacking. It is unclear what this panel is supposed to be demonstrating.
5. There is little justification for the candiates assessed in
6. Extended data Figure 3 is very difficult to read due to the small font size.
7. Just to be clear, the blots shown in Figure 6D are different from those depicted in Extended data Figure 4b, because some of them look very similar.

Significance

The study provides a fresh look at Alphavirus replication in macrophages. There are a number of issues that should be worked out that would enhance impact and interpretation of this study.

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors utilize: 1) chimeric arthritogenic alphaviruses; evolution selection analyses with virus sequences isolated from human patients; and 3) mass spectrometry and proteomics to interrogate determinants of chikungunya virus (CHIKV) permissiveness in primary human macrophages and the human macrophage cell line, THP-1. The authors find that the vaccine strain, CHIKV 181/clone 25 replicates the most efficiently in primary monocyte-derived macrophages compared to other arthritogenic alphaviruses. Using o'nyong o'nyong (ONNV) as a comparison, the authors generate several chimeric viruses with CHIKV structural proteins and ONNV non-structural proteins (and vice versa) and perform a series of E1 and E2 domain swap experiments. They determine that both CHIKV structural proteins, E2 and E1, are necessary to confer efficient virus production over ONNV in the absence of a difference in viral RNA production. The authors also identify a specific residue in E1 that appears to be important for efficient virus production in THP-1 macrophage cell lines. Finally, using mass spectrometry, the authors identify two host proteins, SPCS3 and eIF3k, that bind to CHIKV E1 structural protein and appear to act as antiviral host factors.

Major comments: The authors elegantly demonstrate that CHIKV structural proteins confer an advantage over ONNV structural proteins in a step in the replication cycle downstream of virus RNA synthesis, possibly virion assembly. This point would be strengthened determining the particle-to-PFU ratio of the parental viruses and the chimeras. Presumably, the ratio would increase in the chimeras containing CHIKV structural proteins. Additionally, the authors should consider performing virion assembly blocking assays with a small molecule inhibitor to determine if this abrogates the virus production advantage of CHIKV structural proteins within the ONNV backbone. Finally, the authors should perform competition experiments with the chimeric viruses and ONNV in macrophages to determine if the chimeras can outcompete the parental ONNV strain. Based on their data, the chimeric viruses should outcompete. These experiments would likely take 3-4 weeks to complete.

The authors use both primary macrophages and macrophage cell lines as their in vitro model system and make one of their major points (listed in the title) that the determinants they identified in the CHIKV structural proteins convert macrophages into dissemination vessels; however, they do not show: 1) an in vivo model that the CHIKV-ONNV chimeras disseminate more efficiently than the parental ONNV; and 2) that these chimeras generate virus more efficiently specifically in macrophages. It would be useful to show that ONNV and CHIKV have equivalent virion production in other cell lines and that the advantage conferred by CHIKV structural proteins in the ONNV backbone is specific to macrophages. The authors should also change their title to reflect that dissemination is not directly being addressed in their study; the implications of their in vitro experimentation in a mammalian host would be more appropriate for the discussion.

OPTIONAL: The authors use CHIKV-ONNV chimeras but it would be interesting to test other chimeras to determine if CHIKV structural proteins confer the same advantage in the backbone of other arthritogenic alphaviruses. The study would also be strengthened by using a pathogenic strain of CHIKV instead of the vaccine strain, as this is significantly attenuated in vivo. In Figure 4, the authors identify residues in the CHIKV structural proteins that appear to be under positive selection in human subjects and generate point mutants in these residues with the corresponding ONNV residues. They find that one mutation, V1029I located in E1, completely abolishes virion production in THP-1 macrophage cell lines. However, in their previous chimeric experiments, they find that neither CHIKV E1 or E2 was sufficient to increase virus production in the ONNV backbone. The authors should address this discrepancy, otherwise they should consider moving the data in their point mutation experiments to a supplementary figure. While worthy of reporting, especially given the patient data, these experiments do not buttress the points made in the previous figures.

The authors conclude their manuscript with an assessment of several host proteins, namely SPCS3 and eIF3k, that were identified by mass spectrometry and whose knockdown results in increased virion production. The authors speculate about the role of these proteins but do not provide any mechanistic detail on how they might be playing a role. It is unclear that the putative antiviral role of these proteins involves steps downstream of virus replication, especially given that the authors speculate translation might be affected by eIF3k which, if the case, RNA synthesis should also be expected to be affected.

Overall, while the initial chimeric virus and domain swap approach is strong, the manuscript would benefit with a more thorough examination of virion assembly steps and a mechanistic link to virion production. Otherwise, the authors should revise the structure of their manuscript by de-emphasizing points about virion assembly and leave room for other mechanistic explanations of their chimeric data that more clearly link the host antiviral factor/E1 binding studies.

Minor comments: In Figure 3e, the line under "with CHIKV E1" should be moved over to include the E2-II+E1 virus.

Figure 5a, 5b, and 6a should be replaced with higher resolution images.

Significance

Strengths of the study include the initial chimeric virus and domain swap approach to determine factors that allow for the productive replication of chikungunya virus in macrophages compared to other arthritogenic alphaviruses. This approach yielded useful insights and could be adapted to other viruses. The study is limited, however, by the lack of mechanistic detail linking the antiviral host factors identified which bind to the E1 structural protein, and the advantage conferred by CHIKV structural proteins in the ONNV backbone. The study would be greatly improved by structural studies of the chimeric viruses that directly demonstrate more efficient virion production and that knockdown of the identified factors specifically affects virion production. This point could be addressed either through additional experimentation or tempering of the authors' conclusions about the mechanism by which CHIKV structural proteins provide an advantage over those of ONNV.

The study advances knowledge in the field on what might advantage different pathogenic alphaviruses and explain differences in disease pathology. Additionally, the authors devise a simple and clever strategy that could be applied across different alphaviruses and would be useful to test in vivo in future studies. This study would be useful to a virology-specific audience.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this work Yao et al. show CHIK is able to infect macrophages in contrast to other arthritogenic alphaviruses RRV, ONNV, and SINV. They use a series to chimeric viruses made with ONNV, the closest species to CHIK, and determine the E2-E1 proteins are important viral determinants which allow CHIK to replicate in machophages compared to ONNV. By comparing 397 CHIK sequences from infected patients, they identified 14 residues under pervasive and positive selection. Of these, 3 residues in E2 and 3 residues in E1 (amino acids) were different between CHIK and ONNV suggesting these residues contributed to the difference in macrophage tropism of CHIK compared to ONNV. The authors go on to determine what host factors the CHIK E2 protein is interacting with to presumably connect the viral and host determinants for CHIK infection in macrophages.

Major concerns:

1. The authors show one configuration of the E1-E2 heterodimer in Figure 4d. As shown, the E1 protein is exterior to the E2 protein and would suggest E1 is on the surface on the spike complex and virus surface. However, another configuration of the glycoproteins has E2 on the exterior of E1 and also on the exterior of the virus. The latter conformation is what has been observed in cryoEM studies of alphaviruses. The first configuation represents the E1-E2 between the three heterodimers which are important for spike assembly. The reason the orientation of the E2-E1 dimer is important is the authors speculate on the importance of the 6 CHIK residues not found in ONNV based on the structure, but the structural interpretation is, in my opinion, not correct.
2. Validation of E1 interaction with SPSC3 and eIF3k needs to be stronger. Some concerns/questions are listed below. A myc tag was inserted between E3 and E2. How efficeintly does furin cleave E3 from E2 in this virus and how are viral titers of the myc-tagged virus compared to the non-tagged virus? I ask because is the IP looking at what is being pulled down by E2 or E3-myc-E2 that could be part of the spike polyprotein? The authors found E2 interacts with E3, E1 and a list of other host proteins. These results suggest several interactions including E2-host factor, E2-E1, E2-E3, E2-E1-host factor, E2-E3-E1, E2-E3-host factor. In figure 6d, and the subsequent conclusions, the authors suggest E1 is interacting with the host facor and do not see E2 alone and very low amounts of E3-E2-6K-E1. based on how the IP was performed I am not sure how an interaction between E1 and SPCS3 alone, without E2, would be detected. I would also like to see a reciprocal pull down using E1 and also E2 to see if these host factors are pulled down.
3. If CHIK E1 is interacting with the host factors and that is antagonizing the antiviral response of SPSC3 (as one example), then what do pull downs using ONNV structural proteins look like? One would expect reduced interactions because the different amino acid causes a different E2-E1 dimer or attenuates the E1-host factor binding site.
4. E1 and E2 are thought to interact during polyprotein translation and the initial dimer forms in the ER. If E1 is interacting wht SPSC3 in the ER, is E2 also present? Or is a population of E1 not interacting with E2 in order to inhibit SPSC3? I would love a model of how the authors see all these factors coming together for this new role of E1.

Minor concerns:

1. In Figure 1c, (-) RNA is shown but in the rest of the figures (+) RNA is shown. Show both or select one. I do find it interesting the (-) RNA levels are similar over time, even at 4 hours post transfection (early time). Related to this, ONNV has higher levels of (-) RNA but what is known about structural protein levels in ONNV and CHIK in macrophages? Are there comparable levels of CP and GP being produced?
2. Figure 2e and figure 3 have ONNV has the first bar followed by CHIK. In figure 1 and 2b, CHIK is first and then ONNV. helps the reader to have the controls in the same order.
3. Line 143-145 the authors discuss that when ONNV is the backbone and CHIK proteins are inserted the infection is more attenuated because of the E2 and E1 are from CHIK and ONNV, not the same virus (could also be E2-CP interactions are disrupted). However the chimeras made witht he CHIK backbone (in Figure 2) have a mismatch between E2 and E1 as well.
4. When discussing the residues that were found in the FEL and MEME analysis, the authors start the amino acid numbering from CP and continue along the polyprotein. Usually when discussing amino acids in the structural proteins, each protein starts at amino acid 1. So V460 would be E2-V135. It would also be useful to know what the residues in ONNV were at these positions to see if amino acids changed in charge, size, bond forming potential, etc. Showing these residues in the E2-E1 conformation found in the virion would also allow one to find adjeacent residues that could explain differences in spike assembly and potentially where/how E1 is binding to a host protein.
5. How effective is a non-attenuated CHIK strain in infecting macrophages? Could you make a SINV-La Reunion chimeric virus (which is BSL2) to see if a higher percentage of macrophages are infected and is this potentially contributing to the increased pathogenesis of La Reunion? Also how different is 181/25 with a pathogenic strain in the E2 and E1 resdiues? and compared to ONNV?
6. When describing the last results section, "CHIK E1 binding proteins exhibit potent anit-CHIV activities" the authors use macrophages. In the rest of the text they consistently use THP-1 macrophages or human primary monocyte derived macrophages. The details of the cell type are extremely useful to the reader and having those in the last results section would be great.
7. The paper is well-written. There is a slight disconnect as the authors go from discussing results in Figure 4 to Figure 5.

Referees cross-commenting

I agree with R#2 that having some Particle:PFU data would add some data to determine why such differences in titers/infectivity.

I also see how this m/s could be split into two different m/s. One that focuses on the chimeric viruses and another that identifies the host factors important and goes in more depth with mechanism

Significance

Strengths:

The authors have tackeled an intriguing question: why do some alphaviruses infect macrophages and others do not. They have used a chimeric approached to very systematically identify the viral determinants E2 and E1 as being important in macrophage infection. Using AP-MS they identify host factors that interact with E2 (possibly E2 and E1, see comments above) but if their findings that E1 has a role in attenuating a host antiviral factor, this would be fantastic.

More and more examples of viral proteins having multiple roles during infection are in the literature. The idea that structural proteins also attenutate host antivirals is a developing field and vastly understudied. By fleshing out the results some more the authors might be onto something ery important in alphavirus virology.

Limitations:

The study has it is presented is limited in the validation of host factors and their interacting partners. I have many questions about the methodology, validation, and model from this last section.

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Reply to the reviewers

We thank the reviewers for their careful reading of the document and feedback which will help us to improve our manuscript. We will go through their comments one by one.

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

This study would be much convincing if additional line of eukaryotic cells can be used to demonstrate the GEF-GAP synergy tis important for cell physiology. In addition, it would be best to demonstrate the spatiotemporal interaction of GEF-GAP using high-resolution live cell imaging.

Response from the authors:

The reviewer requests additional in vivo data to support our in vitro findings:

(1) The reviewer requests in vivo data showing that GEF-GAP synergy is important for cell physiology. We believe that in order to show GEF-GAP synergy in vivo, Cdc42 cycling rates would need to be measured in vivo. For that single-molecule resolution is required – to track a single Cdc42 molecule and measure its GTPase cycling. We agree that such data would indeed be interesting, but are unaware of established techniques that would facilitate measurements of Cdc42 cycling rates in vivo.

(2) The reviewer requests in vivo data showing the spatiotemporal interaction of GEF-GAP. Cdc24 and Rga2 are shown to interact (direct or mediated by another protein) (McCusker et al. 2007, Breitkreutz et al. 2010, Chollet et al. 2020). Cdc24 and Rga2 share 11 binding partners (https://thebiogrid.org/31724/table/saccharomyces-cerevisiae-s288c/cdc24.html, https://thebiogrid.org/32438/table/saccharomyces-cerevisiae-s288c/rga2.html) and have been found at the polarity spot (Gao et al. 2011). Live cell imaging of fluorescently tagged Cdc24 and Rga2 will show that they exhibit some interaction, but not specify the role of the interaction nor if the interaction is direct or mediated by one of the shared binding partners. In order to show a direct interaction between Cdc24 and Rga2, one could consider (A) super-resolution imaging or (B) FRET experiments: For both fluorescently tagged Cdc24 and Rga2 cell lines would need to be constructed.

(A) Super-resolution imaging could show direct interaction between Cdc24 and Rga2, but even with the techniques available this would be on the limit. Further, it is usually done in fixed cells, and not in live cells (as requested from the reviewer).

(B) To show a direct interaction of Cdc24 and Rga2 using FRET, suitable protein constructs would need to be engineered. We believe that the main obstacle in showing direct binding of Cdc24 and Rga2 using FRET is to design the fluorophore linker. The linker would need to be designed in such a way that it is flexible enough to give a FRET signal even if the two large proteins bind on the opposite sites of the fluorophore, but also is stiff/short enough to not show binding if both proteins are in close proximity through binding to a common binding partner.

__We believe that an investigation of GEF GAP binding in vivo is beyond the scope of this study. Instead, we will further explore one possible mechanism underlying GEF GAP synergy - Cdc24 Rga2 binding - through conducting Size-Exclusion Chromatography Multi-Angle Light Scattering experiments with purified Cdc24 and Rga2 (alone and in combination). __

Reviewer #1 (Significance (Required)):

The revised study would provide first line evidence that GEF-GAP synergy to be general regulatory property in eukaryotic kingdom.

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

The study entitled, "The GEF Cdc24 and GAP Rga2 synergistically regulate Cdc42 GTPase cycling" by Tschirpke et al., uses an in vitro GTPase assay to examine the GTPase cycle of Cdc42 in combination with its GEF and GAP effectors. The authors find that the Cdc24 GEF activity scales non-linearly with its concentration and the GAP Rga2 has substantially weaker effect on stimulating Cdc42 GTPase activity. Not surprisingly, the combined addition of Cdc24 and Rga2 lead to a substantial increase in Cdc42 GTPase activity.

**Referees cross-commenting**

In Zheng, Y., Cerione, R., and Bender, A. (1994) J. Biol. Chem. 269: 2369-2372 (Fig. 3C), the authors show that Cdc24 combined with the GAP Bem3 lead to a large synergy in boosting Cdc42 GTPase activity.

Reviewer #2 (Significance (Required)):

There is very little new information in this manuscript. Previous studies (Rapali et al. 2017) have shown that the scaffold protein Bem1 enhances the GEF activity of Cdc24. It is expected that the reconstitution of a GEF and GAP protein promote the GTPase cycle and indeed Zheng et al. (1994) showed that that Cdc24 combined with the GAP Bem3 lead to a large synergy in boosting Cdc42 GTPase activity. Hence the only potentially interesting finding in this work is that, in solution Cdc24 activity scales non-linearly with its concentration. However as this GEF and Cdc42 are associated with the membrane, the relevance of solution studies are less clear and furthermore the mechanistic basis for the non-linearity is not explored in detail. Given the limited new information from this work, the findings are, in their current form, too preliminary.

Response from the authors:

__We appreciate the reviewer recognizing our work on the non-linear concentration-dependence of Cdc24’s activity. We disagree that this is the only new finding in our study: __

We explore the effect of Cdc24 and Rga2 on Cdc42’s entire GTPase cycle and show that Cdc24 and Rga2 synergistically upregulate Cdc42 cycling. So-far Cdc42 effectors were only characterized in isolation (with the exception of Cdc24-Bem1 (Rapali et al. 2017)) and through how they affect a specific GTPase cycle step. The regulation of single GTPase cycle steps through an effector yields mechanistic insight into this specific GTPase cycle step. However, it does not show how the effector affects overall GTPase cycling of Cdc42 – a process Cdc42 constantly undergoes in vivo. Our approach allows us to study synergistic effects between proteins affecting different GTPase cycle steps. Synergies are another regulatory layer of the polarity system, adding further complexity: Which polarity proteins exhibit synergy, to which extend? The assay employed here, which studies the entire GTPase cycle, enables studying the effect of any GTPase cycle regulator, alone and in combination with another regulator.

The reviewer states that the GEF GAP synergy is to be expected, as it was already shown in Zheng et al. 1994. In Fig. 3C Zheng et al. shows the time course of the GTPase activity of Cdc42 in presence of Cdc24, Bem3, and Cdc24 plus Bem3. Fig. 3C is the only data in which the combined effect of a GEF (Cdc24) and a GAP (Bem3) is investigated. The data indicates synergy, but is neither discussed as such in the text of the publication, nor analyzed quantitatively. Further, only one concentration of each effector (GEF/GAP) is used and the study uses a Bem3 peptide containing codons 751-1128 (30%) of the full-length BEM3 gene. Zheng et al. 1994 gives an early indication of GEF GAP synergy, but does not claim, discuss, or further investigate the synergy as such. In contrast, we use full-length Rga2 (not Bem3) as GAP, conduct several concentration-dependent assays, and analyze them quantitatively. We thank the reviewer for pointing out the pioneering character of Zheng et al.‘s study and will mention it more prominently in our report. However, we disagree that Zheng et al. sufficiently studied the GEF GAP interaction. To our awareness no theoretical studies include a GEF GAP synergy term, which we would expect if GEF GAP synergy is well-established in the field.

The reviewer criticizes the relevance of bulk in vitro studies (lacking membranes) of proteins that bind to membranes in vivo. We agree that the presence of a membrane can affect the protein’s property, and we can not exclude that membrane-binding could alter the magnitude of a GEF GAP synergy. However, we believe that membrane-binding does not impede the GEF GAP synergy altogether. If membrane binding would influence GTPase properties that strongly, other studies on Cdc42’s GTPase activity and GEF and GAP activity, that do not include a membrane, would be inconclusive as well (e.g. Zheng et al. 1993, Zheng et al. 1994, Zheng et al. 1995, Zhang et al. 1997, Zhang et al. 1998, Zhang et al. 1999, Zhang et al. 2000, Zhang et al. 2001, Smith et al. 2002, Rapali et al. 2017). Both studies mentioned by the reviewer (Zheng et al. 1994, Rapali et al. 2017) were also conducted without membranes present.

We believe that an inclusion of membrane-binding into reconstituted Cdc42 systems will enhance our understanding of Cdc42 and recognize it as a next step, which could be enabled by the assay used in our study.

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

This work reports a biochemical analysis of the effects of a recombinant yeast GEF (Cdc24) and GAP (Rga2) on Cdc42 GTPase cycling in vitro. The central conclusion is that the GEF and GAP act "synergistically", which occurs "due to proteins enhancing each other's effects". By this they appear to mean that the GEF enhances the GAP's activity and vice versa. I was not persuaded that this is correct, and was confused by many aspects of the approach and interpretation, as outlined below.

1. GEF and GAP are expected to accelerate GTPase cycle synergistically even with no effect on each other's activity:

The Cdc42 GTPase cycle is understood to occur via distinct steps (GDP release, GTP binding, and GTP hydrolysis): GDP release and GTP hydrolysis are intrinsically slow steps that are accelerated by GEFs (GDP release) and GAPs (GTP hydrolysis). This fundamental biochemistry was established in the 1990s using biochemical assays that measure each step independently. Here instead the authors use an assay that measures [GTP] decline in a mix with 5 uM starting GTP, 1 uM Cdc42, plus or minus some amount of GEF or GAP. They assume exponential decline of [GTP] with time, yielding a cycling "rate". If that is so, then one would expect that added GEF would accelerate only the first step, leaving a slow GTP hydrolysis step that limits the overall cycling rate, while added GAP would accelerate only the last step, leaving a slow GDP release step that limits the overall cycling rate. Adding both together would speed up both steps, and should therefore "synergistically" accelerate cycling. This would be expected based on previous work and does not imply that GEF or GAP are affecting each other's action (except trivially by providing substrate for the next reaction). If the authors wish to demonstrate that something more complex is indeed happening, they need to use assays that directly measure the sub-reaction of interest, as done by prior investigators.

Response from the authors:

The reviewer raises the point that we do not consider a simpler, rate-limiting model and that this rate-limiting model could explain our synergy between GAP and GEF in accelerating the GTPase cycle.

We very much welcome this consideration of the reviewer! We will add a clarification to our manuscript to explain why a rate-limiting model/interpretation does not match our data.

Intuitively, the rate-limiting model is appealing, as it permits interpretation of cycle rate increases in terms of individual biochemical steps. So, a consideration of this model is indeed relevant. However, as also noted by the reviewer in the next points, data from e.g., figure 3e are not compatible with a simple rate-limiting model with two steps (hydrolysis and nucleotide exchange). We will explain how the acceleration of the total rate by both GAP and GEF individually does not match the rate-limiting model, even if we assume maximal effects of adding GAPs and GEF to the cycle. For this purpose, we consider the rate-limiting model scenario where the sensitivity of the GTPase cycle to adding GAP/GEF is maximized, so the best case-scenario for the rate limiting step-model.

In the rate-limiting step model, we assume that we have a GTPase cycle in which at least one of the three GTPase cycle steps is rate-limiting: (A) GTP binding, (B) GTP hydrolysis, and (C) GDP release.

We assume that the addition of a GEF and GAP only accelerates GDP release and GTP hydrolysis respectively. Biochemically, all three steps in the GTPase cycle are expected to be relevant. However, here we will consider only the final two steps, as sensitivity to rate limitation by GAP/GEF is maximized when time spent in the GAP/GEF-independent step in the cycle (step A: GTP) is negligible (i.e. never rate-limiting). The two-step model thus consists of (1) a nucleotide exchange step (step C+A) which is dominated by GDP release (step C) and assumed to be accelerated exclusively by the GEF, and (2) a GTP hydrolysis step (step B) exclusively enhanced by the GAP.

In the rate limiting step model GEF-GAP synergy can appear if one of the conditions applies:

1. the addition of a GAP speeds up the GTP hydrolysis step so much that the hydrolysis step stops (or almost stops) being the rate-limiting step, or
2. the addition of a GEF speeds up the GDP release step so much that the release step stops (or almost stops) being the rate-limiting step. In these conditions, the acceleration of the GTPase cycle, accomplished by adding only a GAP or adding only a GEF, is interdependent. Therefore, we consider the possible acceleration of the GTPase cycle by GAP and GEF individually, and compare these to our observations to determine whether the rate-limiting step model can explain our data.

The GTPase cycle time Tc is thus composed of hydrolysis Th and nucleotide exchange time Te, and the rates r are connected through:

1/rc=1/rh + 1/re

If we compare the ratio of the rates with protein (GAP/GEF) added in the assay (index 1) with the basal rate without protein added (index 0), we obtain the cycle acceleration factor alpha:

alpha=rc1/rc0=(1/rh0 + 1/re0)/(1/rh1 + 1/re1)=(re0 + rh0)/(re0*rh0/rh1 + rh0*re0/re1)

Here, rc1 and rc0 are the total GTPase cycle rate with and without effector respectively, rh1 and rh0 are the GTP hydrolysis rate with and without effector respectively, and re1 and re0 are the nucleotide exchange rate with and without effectors respectively.

There is indeed an interdependence created between how much the GAP and GEF can both accelerate the total cycle, if the GAP and GEF are assumed to only accelerate GTP hydrolysis and nucleotide exchange respectively. E.g., how much the total GTPase cycle rate rc is accelerated by an increase in GTP hydrolysis rate rh depends on and can be limited by the current nucleotide exchange rate re. However, this interdependence is too strict to match the data in Figure 3e, as we will explain in the next paragraphs:

When we only add a GAP and the GAP accelerates only the GTP hydrolysis rate (re1=re0), then the maximal total GTPase cycle rate acceleration alphaGAP that the GAP can accomplish is when rh1>>rh0,re0:

alphaGAP=rc1/rc0=(1/rh0 +1/re0)/(1/rh1+1/re0)=(re0+rh0)/(re0*rh0/rh1+rh0)

~(re0+rh0)/rh0=1+ re0/rh0

We thus assume the GAP accelerates the cycle so much that the hydrolysis step is much faster than the exchange step, at which point the effect of adding more GAP would saturate. We note that we do not consider the GAP concentration regime where we see saturation, thus in reality the acceleration by the GAP is more restricted than predicted here.

Analogously, if the GEF accelerates only the nucleotide exchange rate (rh1=rh0), then the maximum GTPase cycle rate ratio will be when re1>>re0,rh0 , yielding acceleration factor alphaGEF :

alphaGEF= rc1/rc0=1+ rh0/re0

Again, note we assume the GEF accelerates the cycle so much that the exchange step is much faster than the hydrolysis step, at which point the effect of adding more GEF would saturate. We note that we do not observe the GEF concentration regime where we see saturation, thus in reality the acceleration by the GEF is more restricted than predicted here.

We see that the maximum gain in rates for GAP-only and GEF-only assays is limited by the same basal GTP hydrolysis and nucleotide exchange rates (rh0 and re0), leading to the following interdependence:

alphaGAP=1+ 1/(alphaGEF -1)=alphaGEF/(AlphaGEF -1)

In our GAP-only and GEF-only assays (Fig. 3e, Tab. 2), we see both a 2-fold and 100-fold increase in the total rate respectively. A 100-fold acceleration factor of the GEF would maximize the GAP acceleration factor to 1.01 (or alternatively, the 2-fold GAP acceleration would maximize the GEF acceleration to 2), which are both significantly lower than what we observe. So even though we made favorable assumptions for the rate-limiting model to maximize rate sensitivity to GAP/GEF, namely neglecting nucleotide binding and assuming GAP/GEF concentrations that saturate in their effects, we still cannot reproduce the acceleration factors in our GAP-only and GEF-only assays.

Moreover, a rate-limiting step model would also imply saturation effects as stated in the next point of the reviewer. While we observe saturation in total rate acceleration for certain GAP concentrations, we use GEF and GAP concentrations in the combined protein assays for which no saturation effects were observed. Absence of saturation in both cycle steps simultaneously is also not reconcilable with the rate-limiting step model, as will be further discussed in the next point of the reviewer.

In summary, this means that the rate-limiting model is not sufficient to explain our results: the GAP/GEF synergy we observe is not simply resulting from GEF and GAP independently lifting two different rate-limiting steps.

Model-based interpretation of the GTPase assay is poorly supported:

The assay employed measures overall GTP concentration with time. It is assumed (but not well documented-see below) that [GTP] declines exponentially, and that the rate constant for a particular condition can be fit by the sum of a series of terms that are linear or quadratic in the concentrations of Cdc42, GEF, and GAP. There is no theoretical derivation of this model from the elementary reactions, and the assumptions involved are not well articulated.

As discussed in point 1 above, one would expect that a GEF or GAP alone could only accelerate the cycle to a certain point, where the other (slow) reaction becomes rate limiting. But that does not appear to be true for their phenomenological model, where slow steps (small terms in the sum) will always be overwhelmed by fast steps. This is not the traditional understanding of how GTPases operate.

Response from the authors:

The reviewer expresses the concern that because we do not derive our coarse-grained model from elementary reactions, we miss important effects that can occur when adding GAP and GEFs, particularly saturation.

We understand the concern of the reviewer that if a rate-limiting step model is considered, saturation effects of GAP/GEF will limit the amount with which these effectors can speed up the total cycle. Our coarse-grained model indeed does not account for this saturation. However, as discussed in the previous point of the reviewer, we do not opt for the rate-limiting model interpretation, as the GAP and GEF effects are not compatible with the rate-limiting step model.

Secondly, we agree that for high enough concentrations of GEF and GAPs, we would experience a saturation in the effect of adding the effectors. We are aware of this possibility, and we verify that we are not in saturation regimes with our added proteins by checking the plots of the individual protein titrations (see Figure 3a-d). If we enter the saturation regime, we expect a negative second derivative in the rate as function of protein concentration (the curve shallows off). We do not see this for any protein except for Rga2 at some point, as discussed in our main text of the manuscript. However, for this protein we only use the data in the linear regime for further analysis. In short, we understand the concern of the author but we empirically check that we are not in the saturation regime.

Data that do not conform to expectation are not explained: Strangely, the data (as interpreted by the model assumptions) also appear inconsistent with the expectation of rate-limiting steps. GEF addition (alone) is said to accelerate cycling 100-fold, while GAP addition (alone) accelerates it 2-fold. But that would seem to imply that GDP release takes up >99% of the basal cycle (so accelerating that step alone reduces cycling time 100-fold), while GTP hydrolysis takes up >50% of the basal cycle (so accelerating that step alone reduces cycling time 2-fold). In the conventional understanding of GTPase cycles, these cannot both be be true (as the steps would then add to >100% of the basal cycle). There is no attempt to reconcile these findings with previous work.

Response from the authors:

The reviewer raises the point that our findings do not match the expectations of the rate-limiting model perspective.

We fully agree with the reviewer that our data is not compatible with the rate-limiting step model. The 100-fold and 2-fold gain of the total cycle rates for GEF-only and GAP-only assays are one of our arguments against the rate-limiting model view, as described in the first point of the reviewer. Also, our lack of saturation as described in the previous point of the reviewer provides another argument against using expectations based on rate-limiting steps to interpret our findings.

Lack of detailed timecourse data:

The decline in [GTP] with time is stated to be exponential, allowing extraction of an overall cycling "rate". But this claim is supported only weakly (S3 Fig. 1 uses only 3 timepoints, is not plotted on semi-log axis, and does not report fit to exponential vs other models) and only for the Cdc42-alone scenario: no data at all are presented to support exponential decline in reactions with GEF or GAP. Most assays seem to measure only a single timepoint, so extraction of a "rate" is very heavily influenced by the unsupported assumption of exponential decline. And if the decline is not exponential, it becomes extremely difficult to interpret what a single timepoint means.

Response from the authors:

The reviewer requests additional timeseries data with GEF and GAP to support the assumption of an exponential decline of GTP in the assay and requests to plot it on a semi-log axis.

We will add data for Cdc42 + Cdc24 and for Cdc42 + Rga2 with two to three time points, and plot it as requested on a semi-log axis.

Other issues with interpretation of the data:

(i) It is unclear why the authors chose to employ an assay that is much harder to interpret than the biochemical assays used by others. In biochemical studies, assays that report an output of multiple reactions are always harder to interpret than assays targeting a single reaction. As well-established assays are available for each individual step in GTPase cycles, any conclusions must be supported using such assays.

Response from the authors:

The reviewer wonders why an assay that investigates several GTPase steps at once was chosen over assays that investigate sub-steps of the GTPase cycle, given that these give more mechanistic insights.

We agree that assays investigating GTPase cycle substeps can give more mechanistic insights into these specific steps. However, they do not allow to study how proteins affecting different steps act together. We were interested in investigating the overall GTPase cycle of Cdc42 and a possible interplay of GEFs and GAPs. Cdc42 GTPase cycling was found to be a requirement for polarity establishment (Wedlich-Soldner et al. 2004) and Cdc42 GTPase cycling is physiologically relevant. Ultimately, we hope that in vitro results provide stepping stones towards understanding the complex and less controlled in vivo environment. The in vivo environment often entails the output of many reactions combined, so there is every incentive to study aggregated effects of a full cycle which are not necessarily the sum of individual outputs.

__We believe that both assay types – assays that investigate sub-steps and yield mechanistic details, and assays that investigate the entire cycle – are important and disagree that one assay type is superior to the other. Instead, we believe they complement each other. __

(ii) The reported basal (and GEF/GAP-accelerated) rates are very slow, perhaps due to poor folding of recombinant proteins. This raises the possibility that much of the Cdc42 is inactive. If so, then accelerated GTP hydrolysis could come from increasing the active fraction of Cdc42, rather than catalyzing a specific step.

Response from the authors:

The reviewer wonders whether the reported rates are slow due to poor folding of recombinant Cdc42. We used S. cerevisae Cdc42, for which it has been shown that it has a significantly lower basal GTPase activity than Cdc42 of other organisms (see Zhang et al. 1999). Many other studies on Cdc42 were conducted with human Cdc42, which has a significantly higher basal GTPase activity (Zhang et al. 1999). We assessed the activity of several recombinantly expressed Cdc42 constructs previously (Tschirpke et al. 2023). We there observed that most constructs had a similar GTPase activity, only some purification batches and constructs had a significantly reduced GTPase activity (which might be linked to poor folding). The Cdc42 construct used here shows a similar activity as the active Cdc42 constructs in Tschirpke et al. 2023, and we therefore believe that it exhibits proper folding. If recombinant Cdc42 folds poorly, we would expect greater variations between Cdc42 constructs and purification batches (caused by different levels of folding/ a different fraction of active Cdc42) than what we observed previously (see Tschirpke et al. 2023).

Tschirpke et al. 2023:

Tschirpke et al. A guide to the in vitro reconstitution of Cdc42 activity and its regulation (2023) BioRxiv. (https://doi.org/10.1101/2023.04.24.538075) (in submission at Current Protocols)

(iii) The GEF and GAP preparations include multiple partial degradation products and it is unclear whether the measured activities come from full-length proteins or more active fragments.

Response from the authors:

We agree with the reviewer that the Cdc24 and Rga2 preparations contain degradation products.

It would be more ideal if the protein purifications were entirely pure, but this is experimentally very difficult to achieve for the used proteins (which are large and partially unstructured, making them prone to partial degradation). Further, it is not uncommon to use protein preparations where some degradation products were present (e.g. Zheng et al. 1993, Zheng et al. 1994). Other studies did not show their purified preparations.

The vast majority of the Cdc24 preparation is the full-length protein. We therefore expect that the degradation fragments only contribute in a small extend to the overall protein behavior.

The Rga2 preparation contains a higher amount of degradation product, but only larger size protein fragments (> 60kDa), suggesting that the fragments contain at least and more than 1/3 of the full-length protein (the protein fragments are thus the size or larger than of the GAP peptides used previously). The fragments could in principle have a higher or lower activity. We account for fragments of no/lower activity by comparing our cycling rates to those of BSA/Casein, which has no specific effect on Cdc42. The cycling rate Rga2 is almost an order of magnitude greater than that of BSA/Casein, suggesting that the effect of the full-length protein dominates. We could only imagine that a Rga2 fragment has a higher GAP activity if the fragment consists mainly of the GAP domain and if in Rga2 the activity of the GAP domain is downregulated. Nevertheless, we will do an additional experiment using a purified GAP domain peptide to assess that if a GAP domain by itself has a higher GAP activity than our Rga2 preparation. Using that data, we will discuss possible implication of the GAP fragments in our manuscript.

(iv) Cdc42 cycling is also accelerated by BSA and casein, suggesting that there are poorly understood aspects of the assay and that GEF and GAP actions may (like BSA and casein) involve non-canonical effects on Cdc42. As GEF and GAP are expected to interact better with Cdc42 than BSA or casein, these effects could dominate the observed changes in GTP levels.

Response from the authors:

The reviewer raises the concern that the effects of the added effector proteins on the rates could be caused by non-canonical effects. We do not believe non-canonical effects play a relevant role in our assays. While BSA and casein accelerate the GTPase cycle in our assays, the GAP effect and GEF effect are orders of magnitude stronger.

(v) Cdc42-alone cycling assays are said to be reproducible. However, assays with added GEF/GAP/BSA/Casein yield rates that vary almost an order of magnitude between replicates. This poor reproducibility further reduces confidence in the findings.

Response from the authors:

The reviewer is concerned about the variations in Cdc42 effector rates.

__We disagree that the variations are concerning and believe to have accounted for them in our analysis: __The Cdc42 (Cdc42 alone) data is very reproducible (see Tschirpke et al. 2023). The GTPase assay is generally sensitive to small concentration changes and errors introduced through pipetting small volumes (as required for the assay). We believe that the small variation observed for Cdc42 alone is because Cdc42 has such a low basal rate and therefore the small concentration changes due to pipetting have a smaller effect. Once other effectors are added, especially highly GTPase stimulating ones as Cdc24, small concentration changes due to pipetting can lead to larger variations between assays (small variations in Cdc24 concentration lead to larger changes in remaining GTP due to Cdc24’s strong and non-linear effect on Cdc42). We conduct the assays multiple times to account for these variations. In our analysis we do not compare single rate numbers but the orders of magnitude of the rate, and report the variations present. Even given the present variations, the differences in effect sizes are still significant. We map and discuss assay variation in (Tschirpke et al. 2023), to which we refer to several times throughout the manuscript.

Tschirpke et al. 2023:

Tschirpke et al. A guide to the in vitro reconstitution of Cdc42 activity and its regulation (2023) BioRxiv. (https://doi.org/10.1101/2023.04.24.538075) (in submission at Current Protocols)

(vi) It is unclear what timepoint was used for the different assays. 1.5 h at 30 degrees seems to be the standard here for the Cdc42-alone assays, but I assume that cannot be what was measured to assess GTP decline for GEF-containing assays as there would be very little GTP left at 1.5 h.

Response from the authors:

We used 60-100 min as incubation times for all assays. The assay data will be published on a data server, where all these numbers can be checked. We further added a clarification to the materials and methods section. In order to still have remaining GTP for the Cdc42 GEF mixtures after 60-100 min, we lowered the used protein concentrations.

(vii) The graph reporting GEF activity is plotted only for [GEF]Response from the authors:

The graphs show the full range of protein concentrations used.

In order to calculate K1, K2, K3,Cdc24, K3,Rga2, K3,Cdc24,Rga2 from k1, k2, k3,Cdc24, k3,Rga2, k3,Cdc24,Rga2, …, a protein concentration has to be included in the term (as K1 = k1 [Cdc42], ….). In order to make K comparable, we chose to use 1uM for all protein concentrations. This was done to compare the cycling rate values of different proteins. 1uM was a choice, in the same fashion 0.2uM could have been chosen.

__We will further discuss in the manuscript how the choices in protein concentration affect the effector strength on Cdc42. __

(viii) S8 Data with casein seems very noisy and it is no longer at all clear that the quadratic fit for [Cdc24] is justified. Also, the symbol colors are very similar so it is hard to tell what data corresponds to what condition. The synergy between Cdc24 and Rga2 is also very noisy and the fits seem arbitrary.

Response from the authors:

The reviewer is concerned with (1) the noise in the S8 data, and (2) the Cdc42-Cdc24-Rga2 fits.

(1) We acknowledge in the manuscript that the S8 data is noisy and should be viewed with caution. We do not put much emphasis on these data sets and their interpretation and show them only in the supplement.

(2) We disagree that the Cdc42-Cdc24-Rga2 fits are arbitrary. The fits contain several data points per protein, and reproduce the rate values from Cdc42-Cdc24 and Cdc42-Rga2 assays well.

The reviewer is concerned with the color scheme choice in the fits.

__We will adapt the color scheme of the fits to make the colors more distinguishable. __

(ix) It is disturbing that different Cdc42 constructs behave quite differently (S4). This suggests that protein behavior is influenced by the various added epitope tags and protease cleavage sites (they also leave the C-terminal CAAX box rather than removing the AAX as would happen in vivo). These features raise the concern that these findings may not be directly relevant to the situation with endogenous yeast Cdc42. Of course, it is also the case that relevant Cdc42 biochemistry occurs with prenylated Cdc42 on membranes.

Response from the authors:

The reviewer is concerned that the behavior of the Cdc42 constructs is influenced by their tags. In a previous manuscript (Tschirpke et al. 2023) we explored the effect of various N- and C-terminal tags on Cdc42, by comparing it to Cdc42 that is not tagged in that position. We found that most tags, including the tags present in the Cdc42 construct used here, do not affect Cdc42’s properties.

Instead, we found a general, tag independent, heterogeneity in Cdc42 behavior (which can occur between purification batches and between constructs (but not between different assays)): in some batches GTPase activity depended quadratically on its concentration, others showed a linear relationship. Most batches exhibited a mixed behavior. The differences between the batches are generally small, and only visible in the activity to concentration plots and because of the assay’s high accuracy. We use a two-parameter fit (k1 [Cdc42] + k2 [Cdc42]2) to phenomenologically account for this heterogeneity, and to estimate the basal Cdc42 GTPase activity. We do not interpret this heterogeneity, as more research is needed. We believe that Cdc42 still has unexplored properties, of which this heterogeneous behavior can be one. We speculate in Tschirpke et al. 2023 that it is linked to Cdc42 dimerization mediated by its polybasic region, a relationship that is far from being fully understood yet. __We believe that it is of scientific interest to point out heterogeneous behaviors to encourage more research. __

Tschirpke et al. 2023:

Tschirpke et al. A guide to the in vitro reconstitution of Cdc42 activity and its regulation (2023) BioRxiv. (https://doi.org/10.1101/2023.04.24.538075) (in submission at Current Protocols)

The reviewer is concerned that our findings are biologically not relevant, as our experiments (1) included Cdc42 that was not prenylated and (2) did not include membranes.

(1) We here used recombinantly purified proteins, which do not contain posttranslational modifications, such as prenylations. So-far Cdc42’s prenyl group, which is responsible for binding it to membranes, has not been linked to its GTPase properties. We therefore believe that unprenylated Cdc42 is an equal choice to prenylated Cdc42 when studying Cdc42’s GTPase cycle. Further, the use of recombinantly purified proteins can be of advantage: when proteins are purified from their native host, the post-translationally modified protein is purified. However, many proteins contain a multitude of post-translational modifications (PTMs). Thus, the purified protein is a mixture of protein with different PTMs. For example, S. cerevisae Cdc42 undergoes ubiquitinylation (Swaney et al. 2013, Back, Gorman, Vogel, & Silva 2019), phosphorylation (Lanz et al. 2021), farnesylation and geranyl-geranylation (Caplin, Hettich, & Marshall 1994). We here used protein preparations that do not contain PTMs, and show how they behave. Natively purified proteins would be mixtures of various PTMs, and the observed protein behavior would be that of the mixture. If Cdc42’s PTMs affect it’s GTPase behavior, the observed behavior of natively purified Cdc42 would represent the average behavior of the mixture. It then would require additional work to disentangle which PTMs affect the GTPase cycling in which way. The use of recombinantly expressed Cdc42 does not require this work, and can set the baseline for how Cdc42 without PTMs behaves. If in the future a link between Cdc42’s GTPase behavior and PTMs are found, the work here could be used as a baseline for Cdc42’s behavior when it is without PTMs.

(2) The concern about missing membranes was also raised by reviewer 2 (significance), and we like to refer to our response there.

Reviewer #3 (Significance (Required)):

The basic biochemistry of Cdc42 cycles was figured out about 30 years ago. However, those studies did not examine how combinations of Cdc42 regulators (as opposed to individual regulators) might interact to produce effects not expected from combining their individual actions. Recently, this combination approach did lead to interesting findings by Rapali et al. This approach is worthwhile and addresses a major question of interest to the broader field of GTPase biochemistry.

One main limitation of this study is technical: the main assay is less informative (though perhaps easier) than traditional assays, and it is unclear whether the recombinant proteins employed retain their normal activities. Another limitation is the model-based interpretation of the assay that does not include the potential for rate-limiting steps.

Response from the authors:

We thank the reviewer for the detailed comments.

One important point of confusion originated from our lack of discussion concerning a rate-limiting step model, which is an obvious starting point for modelling the GTPase cycle. We thank the reviewer for pointing this out, and we will include an explanation in our manuscript why we reject this model and instead opt for a coarse-grained model.

Firstly, a rate-limiting model would generate saturation effects that we would observe when adding GEF and/or GAPs. In assays exploring GEF GAP synergy we use GEF and GAP concentrations for which no saturation effects were observed.

Secondly, in our data we observed a two-fold increase of the total GTPase cycling rate when adding a GAP and a 100-fold rate increase when a GEF is added. These increases are not compatible with a model where either hydrolysis or nucleotide exchange limits the GTPase cycle. While a synergy could arise from the rate-limiting model perspective, the incompatibility of the rate-limiting model with the GAP-only and GEF-only assay data excludes this synergy explanation. Finally, through coarse-graining our model we avoid using single step parameters from literature which are incompatible in terms of proteins/buffers used. (For example; the mayor studies that kinetically characterized the individual GTPase steps of Cdc42 used human Cdc42 (Zhang et al. 1997, Zhang et al. 2000). Because human Cdc42 exhibits a higher basal GTPase activity (Zhang et al. 1999) we are skeptical how useful it is to transfer these parameters to S. cerevisae Cdc42.)

At the same time, coarse-graining our model permits absorbing unidentified molecular details which is essential when we wish to incorporate BSA and casein rate contributions.

The reviewer finds our assay, which investigates the GTPase cycle as a whole, less informative. Assays investigating single GTPase cycle sub-steps give more mechanistic insights into these steps. We opted for an assay that studies GTPase cycling as a whole instead, as we were interested in studying how proteins effecting different steps act together. We believe that both assay types are important as they complement each other.

The reviewer is concerned about our use of recombinant proteins, and whether they retain their normal activities. We assessed Cdc42’s GTPase activity and the influence of added purification tags extensively (Tschirpke et al. 2023), and found that added tags do not affect Cdc42’s GTPase properties. We checked Cdc24’s GEF activity using the GTPase assay and found that it bound strongly to Bem1, as expected (Tschirpke et al. 2023). The Cdc24 concentrations needed to affect Cdc42’s GTPase activity were similar to those used previously (Rapali et al. 2017), suggesting that it is fully active. A similar comparison for Rga2 was not possible, as so-far only domains of Rga2 were used (Smith et al. 2002). We here used recombinantly purified proteins, which do not contain posttranslational modifications (PTMs). To our knowledge the PTMs of the herein used proteins are not linked to their GTPase/GEF/GAP properties. Thus, a lack of PTMs does not diminish our findings. Further, when proteins are purified from their native host, the post-translationally modified protein is purified. However, many proteins contain a multitude of post-translational modifications in vivo. Natively purified proteins would be mixtures of various PTMs, and the observed protein behavior would be that of the mixture. We here used protein preparations that do not contain PTMs, and show how they behave, setting the baseline for proteins without PTMs behaves. If in the future a link between GTPase behavior and PTMs are found, the work here could be used as a baseline for the proteins behavior when it is without PTMs.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Summary

The GTPase cdc42 is a key determinant of yeast polarization. Its activity is amplified at the site of polarization through a poorly defined positive feedback mechanism, and depends on numerous GAPs regulating GTP hydrolysis and the GEF cdc24 that regulates GDP release. These components have previously been evaluated for their quantitative effects on the individual steps in the GTPase cycle that they modulate, but potential interactions between the cdc24 GEF and any GAP could not be examined based on these assays. The authors validate and employ a bulk assay of the total GTPase cycle based on GTP consumption to study the activities of and potential interactions between cdc24 and the GAP Rga2. Fitting their data to a mathematical model, they come to three central conclusions: (1) the activating activity of cdc24 to activate cdc42 GTPase activity is nonlinear, showing a quadratic relationship, (2) Rga2 shows a much lower activating activity that is linear at low levels before saturating, and (3) there is a strongly synergistic interaction between the activating activities of cdc24 and Rga2. Some hypotheses for the mechanistic bases of these findings are hypothesized, but not further investigated. Their conclusions are well supported by the data which appears to be of sufficient rigor.

Major comments

The three main conclusions of the manuscript are well supported by the data and associated modeling.

One unresolved issue is the discrepancy between the authors' conclusion that the non-linear activation by cdc24 is likely a result of oligomerization, whereas Mionnet et al 2008 reach the opposite conclusion. It seems that the authors wish to discount the Mionnet results because they used truncated constructs to test deficient oligomerization and an engineered construct to test induced oligomerization. If the authors are correct, then a relatively easy test would be to introduce the oligomerization deficient mutants defined by Mionnet into their fuill length construct and compare to wild type protein. While the authors' measured results don't depend on the offered mechanism and this experiment is therefore optional, their explanation is quite unsatisfying, especially since an experiment to resolve the difference is entirely feasible and not very strenuous.

Response from the authors:

__The reviewer suggests to conduct experiments with oligomerization deficient Cdc24 mutants to test our hypothesis that the non-linear concentration dependence of Cdc24’s activity is due to Cdc24 oligomerization. __

We agree that this is an insightful experiment, and will conduct it. In order to observe the effect in our GTPase assays, we require a mutant that is oligomerizes substantially less than wild-type protein. Mionnet et al. constructed several Cdc24 mutants, but none were entirely oligomerization deficient. However, the DH5 (L339A/E340A) mutant showed a 10-fold reduction in oligomerization and the DH3 (F322A) mutant exhibited 2.5-fold reduction in oligomerization. We will therefore use the DH5 and DH3 mutant for two additional experiments.

Minor comments

The results in Fig S4 serve as assay validation, and this should be pointed out early in the Results section. I was initially concerned when the assay was described as based on consumption of GTP that a significantly diminished pool would alter the rate and thereby distort results, and being made aware of the S4 result would have alleviated that concern as I read further.

Response from the authors:

We believe that the reviewer refers to S3 (not S4). We appreciate this suggestion and now mention it earlier.

On page 4 and Fig S4 the authors mention several cdc42 constructs, some of which show linear activity curves and others slightly non-linear curves. I was unable to find where these constructs or their differences are discussed. The authors should also tell us if the construct used for the remaining experiments was one of the two shown in S4, or a different one.

Response from the authors:

We added the requested information and explanations to the manuscript.

It seems that in Fig 4 and Fig S8, some points are missing from the graphs. Were all concentrations for each condition not always assayed, or is some data omitted for some reason? For example, for the 0.125 microM Rga2 condition, only two points are shown vs 4 for some other conditions, and the two missing ones are expected to not be excluded by the >5% GTP remaining criterion.

Response from the authors:

The reviewer wonders whether Fig.4 and Fig. S8 miss data points. This is not the case, and __we added clarifying information to the manuscript. __

In detail: Not all assays contain the same amount of data points/ concentrations for each protein. We first assessed Cdc42 alone using several Cdc42 concentration. We then examined the individual Cdc42 – effector mixtures, using a larger number of effector concentrations. We included a reduced number of effector concentrations in the assays containing two effectors and Cdc42. It would be ideal to include more concentrations, but this is not always feasible: The assay involves a multitude of pipetting steps and is sensitive to any pipetting errors. Further, assays can vary slights from each other, therefore all samples that ought to be compared need to be included in each assay.

Each three-protein assay contains samples shown (Cdc42, Cdc42 + effector 1, Cdc42 + effector 2, Cdc42 + effector 1 + effector 2) and additional ‘buffer’ wells used for normalization. Each data point shown corresponds to the average of 3-4 replica samples per assay. We therefore did not include all concentrations in all conditions. As pointed out, Fig. 4a only shows two data points for the 0.125uM Rga2 axis (Rga2 + Cdc42 and Rga2 + Cdc24 + Cdc42). The rational was the following: We included three Cdc24 concentrations (for proper fitting for K3,Cdc24), three Rga2 concentrations (for proper fitting for K3,Rga2), and 5 mixtures of the used Cdc24 and Rga2 concentrations (for proper fitting for K3,Cdc24,Rga2).

The Cdc42-Rga2-BSA and Cdc42-Rga2-Casein data is rather sparse and would benefit from additional data points. However, we only use those as control experiments and are cautious in their interpretation.

In these graphs, a diamond symbol of slightly varying color is used for the different conditions. The different colors are hard to distinguish. Please use different shape symbols for the different conditions, and choose colors that are more distinct.

Response from the authors:

We will adapt the color scheme of the fits to make the colors more distinguishable.

There are a few sentences that are of unclear meaning, for example on page 10, "It was suggested that each GAP plays a distinct role in Cdc42 regulation, of which the level of GAP activity could be a part of [Smith et al., 2002]." There are also typos and grammatical errors that should be fixed.

Response from the authors:

__We will further check the document for potentially unclear sentences and will try to clarify them, as well as further check for grammatical and spelling errors. __

Reviewer #4 (Significance (Required)):

Significance

The most novel and important finding is the strong synergy observed between cdc24 and Rga2 in activating cdc42 GTPase activity. This is undoubtedly an important mechanism underlying positive feedback in polarization. The measured non-linear activity of cdc24 alone is also quite important given that availability of cdc24 is thought to be a critical in vivo stimulus for polarization. However, the unexplained discrepancy between this result and that of Mionnet leaves one to wonder which result is more reliable. Only Mionnet attempts to directly test whether oligomerization is important in cdc24 activity.

The conclusions are of importance to a broad audience of cell biologists, though the lack of any mechanism for the synergy or the non-linearity of cdc24 activity somewhat diminishes significance.

Note that my expertise and that of my co-reviewer is in the biology, and while we are able to follow the contributions of the modeling, we do not have the expertise to critically evaluate for potential errors or weaknesses in the modeling itself.

The reviewer wonders whether our data or the data of Mionnet et al. on the link between Cdc24 oligomerization and its GEF activity is more reliable and suggests to conduct experiments with oligomerization deficient Cdc24 mutants.

We thank the reviewer for this recommendation and we will do the suggested experiments to resolve the seemingly contradicting observations by us and Mionnet et al..

The reviewer would find mechanistic insights into (2) the non-linear concentration dependence of Cdc24’s activity and (2) the Cdc24-Rga2 synergy useful.

(1) We will conduct experiments with partially oligomerization deficient Cdc24 mutants, as suggested by the reviewer.

(2) We speculate that Cdc24-Rga2 binding could lead to the synergy. ____We will add data on Cdc24 – Rga2 binding (in vitro: Size-Exclusion Chromatography Multi-Angle Light Scattering) to this study.

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

Summary

The GTPase cdc42 is a key determinant of yeast polarization. Its activity is amplified at the site of polarization through a poorly defined positive feedback mechanism, and depends on numerous GAPs regulating GTP hydrolysis and the GEF cdc24 that regulates GDP release. These components have previously been evaluated for their quantitative effects on the individual steps in the GTPase cycle that they modulate, but potential interactions between the cdc24 GEF and any GAP could not be examined based on these assays. The authors validate and employ a bulk assay of the total GTPase cycle based on GTP consumption to study the activities of and potential interactions between cdc24 and the GAP Rga2. Fitting their data to a mathematical model, they come to three central conclusions: (1) the activating activity of cdc24 to activate cdc42 GTPase activity is nonlinear, showing a quadratic relationship, (2) Rga2 shows a much lower activating activity that is linear at low levels before saturating, and (3) there is a strongly synergistic interaction between the activating activities of cdc24 and Rga2. Some hypotheses for the mechanistic bases of these findings are hypothesized, but not further investigated. Their conclusions are well supported by the data which appears to be of sufficient rigor.

Major comments

The three main conclusions of the manuscript are well supported by the data and associated modeling.

One unresolved issue is the discrepancy between the authors' conclusion that the non-linear activation by cdc24 is likely a result of oligomerization, whereas Mionnet et al 2008 reach the opposite conclusion. It seems that the authors wish to discount the Mionnet results because they used truncated constructs to test deficient oligomerization and an engineered construct to test induced oligomerization. If the authors are correct, then a relatively easy test would be to introduce the oligomerization deficient mutants defined by Mionnet into their fuill length construct and compare to wild type protein. While the authors' measured results don't depend on the offered mechanism and this experiment is therefore optional, their explanation is quite unsatisfying, especially since an experiment to resolve the difference is entirely feasible and not very strenuous.

Minor comments

The results in Fig S4 serve as assay validation, and this should be pointed out early in the Results section. I was initially concerned when the assay was described as based on consumption of GTP that a significantly diminished pool would alter the rate and thereby distort results, and being made aware of the S4 result would have alleviated that concern as I read further.

On page 4 and Fig S4 the authors mention several cdc42 constructs, some of which show linear activity curves and others slightly non-linear curves. I was unable to find where these constructs or their differences are discussed. The authors should also tell us if the construct used for the remaining experiments was one of the two shown in S4, or a different one.

It seems that in Fig 4 and Fig S8, some points are missing from the graphs. Were all concentrations for each condition not always assayed, or is some data omitted for some reason? For example, for the 0.125 microM Rga2 condition, only two points are shown vs 4 for some other conditions, and the two missing ones are expected to not be excluded by the >5% GTP remaining criterion.

In these graphs, a diamond symbol of slightly varying color is used for the different conditions. The different colors are hard to distinguish. Please use different shape symbols for the different conditions, and choose colors that are more distinct.

There are a few sentences that are of unclear meaning, for example on page 10, "It was suggested that each GAP plays a distinct role in Cdc42 regulation, of which the level of GAP activity could be a part of [Smith et al., 2002]." There are also typos and grammatical errors that should be fixed.

Significance

The most novel and important finding is the strong synergy observed between cdc24 and Rga2 in activating cdc42 GTPase activity. This is undoubtedly an important mechanism underlying positive feedback in polarization. The measured non-linear activity of cdc24 alone is also quite important given that availability of cdc24 is thought to be a critical in vivo stimulus for polarization. However, the unexplained discrepancy between this result and that of Mionnet leaves one to wonder which result is more reliable. Only Mionnet attempts to directly test whether oligomerization is important in cdc24 activity.

The conclusions are of importance to a broad audience of cell biologists, though the lack of any mechanism for the synergy or the non-linearity of cdc24 activity somewhat diminishes significance.

Note that my expertise and that of my co-reviewer is in the biology, and while we are able to follow the contributions of the modeling, we do not have the expertise to critically evaluate for potential errors or weaknesses in the modeling itself.

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

This work reports a biochemical analysis of the effects of a recombinant yeast GEF (Cdc24) and GAP (Rga2) on Cdc42 GTPase cycling in vitro. The central conclusion is that the GEF and GAP act "synergistically", which occurs "due to proteins enhancing each other's effects". By this they appear to mean that the GEF enhances the GAP's activity and vice versa. I was not persuaded that this is correct, and was confused by many aspects of the approach and interpretation, as outlined below.

1. GEF and GAP are expected to accelerate GTPase cycle synergistically even with no effect on each other's activity:

The Cdc42 GTPase cycle is understood to occur via distinct steps (GDP release, GTP binding, and GTP hydrolysis): GDP release and GTP hydrolysis are intrinsically slow steps that are accelerated by GEFs (GDP release) and GAPs (GTP hydrolysis). This fundamental biochemistry was established in the 1990s using biochemical assays that measure each step independently. Here instead the authors use an assay that measures [GTP] decline in a mix with 5 uM starting GTP, 1 uM Cdc42, plus or minus some amount of GEF or GAP. They assume exponential decline of [GTP] with time, yielding a cycling "rate". If that is so, then one would expect that added GEF would accelerate only the first step, leaving a slow GTP hydrolysis step that limits the overall cycling rate, while added GAP would accelerate only the last step, leaving a slow GDP release step that limits the overall cycling rate. Adding both together would speed up both steps, and should therefore "synergistically" accelerate cycling. This would be expected based on previous work and does not imply that GEF or GAP are affecting each other's action (except trivially by providing substrate for the next reaction). If the authors wish to demonstrate that something more complex is indeed happening, they need to use assays that directly measure the sub-reaction of interest, as done by prior investigators. 2. Model-based interpretation of the GTPase assay is poorly supported:

The assay employed measures overall GTP concentration with time. It is assumed (but not well documented-see below) that [GTP] declines exponentially, and that the rate constant for a particular condition can be fit by the sum of a series of terms that are linear or quadratic in the concentrations of Cdc42, GEF, and GAP. There is no theoretical derivation of this model from the elementary reactions, and the assumptions involved are not well articulated.

As discussed in point 1 above, one would expect that a GEF or GAP alone could only accelerate the cycle to a certain point, where the other (slow) reaction becomes rate limiting. But that does not appear to be true for their phenomenological model, where slow steps (small terms in the sum) will always be overwhelmed by fast steps. This is not the traditional understanding of how GTPases operate. 3. Data that do not conform to expectation are not explained: Strangely, the data (as interpreted by the model assumptions) also appear inconsistent with the expectation of rate-limiting steps. GEF addition (alone) is said to accelerate cycling 100-fold, while GAP addition (alone) accelerates it 2-fold. But that would seem to imply that GDP release takes up >99% of the basal cycle (so accelerating that step alone reduces cycling time 100-fold), while GTP hydrolysis takes up >50% of the basal cycle (so accelerating that step alone reduces cycling time 2-fold). In the conventional understanding of GTPase cycles, these cannot both be be true (as the steps would then add to >100% of the basal cycle). There is no attempt to reconcile these findings with previous work. 4. Lack of detailed timecourse data:

The decline in [GTP] with time is stated to be exponential, allowing extraction of an overall cycling "rate". But this claim is supported only weakly (S3 Fig. 1 uses only 3 timepoints, is not plotted on semi-log axis, and does not report fit to exponential vs other models) and only for the Cdc42-alone scenario: no data at all are presented to support exponential decline in reactions with GEF or GAP. Most assays seem to measure only a single timepoint, so extraction of a "rate" is very heavily influenced by the unsupported assumption of exponential decline. And if the decline is not exponential, it becomes extremely difficult to interpret what a single timepoint means. 5. Other issues with interpretation of the data:

(i) It is unclear why the authors chose to employ an assay that is much harder to interpret than the biochemical assays used by others. In biochemical studies, assays that report an output of multiple reactions are always harder to interpret than assays targeting a single reaction. As well-established assays are available for each individual step in GTPase cycles, any conclusions must be supported using such assays.

(ii) The reported basal (and GEF/GAP-accelerated) rates are very slow, perhaps due to poor folding of recombinant proteins. This raises the possibility that much of the Cdc42 is inactive. If so, then accelerated GTP hydrolysis could come from increasing the active fraction of Cdc42, rather than catalyzing a specific step.

(iii) The GEF and GAP preparations include multiple partial degradation products and it is unclear whether the measured activities come from full-length proteins or more active fragments.

(iv) Cdc42 cycling is also accelerated by BSA and casein, suggesting that there are poorly understood aspects of the assay and that GEF and GAP actions may (like BSA and casein) involve non-canonical effects on Cdc42. As GEF and GAP are expected to interact better with Cdc42 than BSA or casein, these effects could dominate the observed changes in GTP levels.

(v) Cdc42-alone cycling assays are said to be reproducible. However, assays with added GEF/GAP/BSA/Casein yield rates that vary almost an order of magnitude between replicates. This poor reproducibility further reduces confidence in the findings.

(vi) It is unclear what timepoint was used for the different assays. 1.5 h at 30 degrees seems to be the standard here for the Cdc42-alone assays, but I assume that cannot be what was measured to assess GTP decline for GEF-containing assays as there would be very little GTP left at 1.5 h.

(vii) The graph reporting GEF activity is plotted only for [GEF]<0.2 uM, but the rates used in the subsequent experiments are reported for mixtures with 1 uM GEF. The full range of GEF data should be plotted.

(viii) S8 Data with casein seems very noisy and it is no longer at all clear that the quadratic fit for [Cdc24] is justified. Also, the symbol colors are very similar so it is hard to tell what data corresponds to what condition. The synergy between Cdc24 and Rga2 is also very noisy and the fits seem arbitrary.

(ix) It is disturbing that different Cdc42 constructs behave quite differently (S4). This suggests that protein behavior is influenced by the various added epitope tags and protease cleavage sites (they also leave the C-terminal CAAX box rather than removing the AAX as would happen in vivo). These features raise the concern that these findings may not be directly relevant to the situation with endogenous yeast Cdc42. Of course, it is also the case that relevant Cdc42 biochemistry occurs with prenylated Cdc42 on membranes.

Significance

The basic biochemistry of Cdc42 cycles was figured out about 30 years ago. However, those studies did not examine how combinations of Cdc42 regulators (as opposed to individual regulators) might interact to produce effects not expected from combining their individual actions. Recently, this combination approach did lead to interesting findings by Rapali et al. This approach is worthwhile and addresses a major question of interest to the broader field of GTPase biochemistry.

One main limitation of this study is technical: the main assay is less informative (though perhaps easier) than traditional assays, and it is unclear whether the recombinant proteins employed retain their normal activities. Another limitation is the model-based interpretation of the assay that does not include the potential for rate-limiting steps.

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Referee #2

Evidence, reproducibility and clarity

The study entitled, "The GEF Cdc24 and GAP Rga2 synergistically regulate Cdc42 GTPase cycling" by Tschirpke et al., uses an in vitro GTPase assay to examine the GTPase cycle of Cdc42 in combination with its GEF and GAP effectors. The authors find that the Cdc24 GEF activity scales non-linearly with its concentration and the GAP Rga2 has substantially weaker effect on stimulating Cdc42 GTPase activity. Not surprisingly, the combined addition of Cdc24 and Rga2 lead to a substantial increase in Cdc42 GTPase activity.

Referees cross-commenting

In Zheng, Y., Cerione, R., and Bender, A. (1994) J. Biol. Chem. 269: 2369-2372 (Fig. 3C), the authors show that Cdc24 combined with the GAP Bem3 lead to a large synergy in boosting Cdc42 GTPase activity.

Significance

There is very little new information in this manuscript. Previous studies (Rapali et al. 2017) have shown that the scaffold protein Bem1 enhances the GEF activity of Cdc24. It is expected that the reconstitution of a GEF and GAP protein promote the GTPase cycle and indeed Zheng et al. (1994) showed that that Cdc24 combined with the GAP Bem3 lead to a large synergy in boosting Cdc42 GTPase activity. Hence the only potentially interesting finding in this work is that, in solution Cdc24 activity scales non-linearly with its concentration. However as this GEF and Cdc42 are associated with the membrane, the relevance of solution studies are less clear and furthermore the mechanistic basis for the non-linearity is not explored in detail. Given the limited new information from this work, the findings are, in their current form, too preliminary.

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Referee #1

Evidence, reproducibility and clarity

This study would be much convincing if additional line of eukaryotic cells can be used to demonstrate the GEF-GAP synergy tis important for cell physiology. In addition, it would be best to demonstrate the spatiotemporal interaction of GEF-GAP using high-resolution live cell imaging.

Significance

The revised study would provide first line evidence that GEF-GAP synergy to be general regulatory property in eukaryotic kingdom.

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Reply to the reviewers

We would like to thank Review Commons for their innovative approach to scientific peer-review and publishing. We thank all the Reviewers for their positive, highly complementary assessment of the manuscript and for highlighting the high quality and reproducibility of the work and the novelty and significance of the results: “The experiments are well-designed and perfectly executed and presented”; “I felt that this is a strong manuscript for peer-review as it serves diversified interests in modern cell biology.”; “The manuscript would be of interest to basic researchers working on epithelial development. Also potentially to basic researchers working on cancer, due to the mitotic errors described.”. We are grateful for the Reviewers’ comments and suggestions that have contributed to improving the revised manuscript. We have addressed all the Reviewers’ concerns, as detailed below in the point-by-point response to the Reviewers. Textual changes in the revised manuscript are marked in Blue.

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

*The manuscript "Crosstalk between the plasma membrane and cell-cell adhesion maintains epithelial identity for correct polarised cell divisions" by Dr. Hosawi and colleagues reports the characterisation of the mitotic connection between plasma membrane dynamics and division orientation in polarised mammalian epithelial cells in culture. The authors start from the comparison of mitotic events of human mammary MCF10A cells grown at optimal density or at low density. They observed that only at optimal density MCF10A cells polarise by E-cadherin mediated cell-cell contacts, and display uniform membrane enrichment at the cortex, whereas cells grown at low density do not show cortical E-Cadherin enrichment, and distribute aberrantly the plasma membrane at one side and in cytoplasmic vesicles, generating daughter cells with unequal size. Consistently, further analyses revealed that low-density MCF10A cells undergo misoriented mitosis, with chromosome congression and misegregetion defects. Mechanistically, low density MCF10A cells fail to organise a symmetric mitotic spindle and center it in metaphase. This is due to an increased cortical actomyosin thickness coupled to abnormal astral microtubule stability. Building on previous data from the Elias lab, the authors uncover a role of the membrane-associated S100A11 protein in maintaining correct plasma membrane dynamics and E-cadherin localisation in mitosis. Further dissection of the molecular mechanism underlying this mitotic function od S10011A revealed that it enriches at the cortex only in optimal-density MCF10A cells, and promotes spindle orientation by association with LGN and E-cadherin, upstream of E-cadherin. This evidence depicts the plasma membrane and S100A11 proteins as a key mechanical sensors of cell-cell adhesion orchestrating the recruitment of E-cadherin and LGN-dependent force generators to ensure correct division orientation. *

*Major points: *

*- Important information is presented in Supplementary Figure S3. I suggest to move these panels in the main figures. Specifically, I would replace figure 4A with S3A showing the distribution of endogenous S100A11 in MCF10A cells, rather than the one of the GFP-tagged version which is over-expressed. *

__Authors response: __We thank the Reviewer for this suggestion. We have now moved Figure S3A to Figure 4, to replace Figure 4A and show the localisation of endogenous S100A11 during mitosis and included new quantifications in new Figure 4B. We have moved Figure 3A to supplementary figures (new Figure S4A). We have amended the text of the results section and the Source Data file accordingly.

*- The mechanisms of division orientation governed by S100A11 seems to impinge on the control of cortical F-actin and astral microtubule dynamics. This is illustrated in figure S3C, which in my opinion should be shown in the main figures with some more explanation / experiments. The authors mention the " tight actin F-actin bundles at the cell-cell contacts" that are lost in S100A11-depleted cells, and that interact with astral microtubules. However this is not fully clear in figure S3C. I think the authors should find a way to present better these evidence which is key in supporting their molecular model. *

__Authors response: __As requested by the Reviewer we have now moved Figure S3C to the main manuscript, as new Figure 5. To clarify further the effect of S100A11 depletion on the tight actin bundle formation at the cell-cell contacts, we have now included a new illustration in new Figure 5C. Additionally, we have clarified further these findings in the results section (page 11). While we agree with the Reviewer that additional experiments, for example using live imaging of MCF-10A cells co-labelled for F-actin and tubulin, would help assess further the crosstalk between cortical actin and astral microtubules, based on our experience these live imaging experiments are challenging and can take up to several months to optimise and may not warrant successful outcome.

*- I think the discussion would benefit from the addition of a graphical cartoon model illustrating the role of S100A11 in controlling plasma membrane dynamics in mitosis and spindle orientation. *

__Authors response: __We thank the Reviewer for this suggestion. We have now added a graphical cartoon (new Figure 7), summarising the role of S100A11-mediated regulation of plasma membrane dynamics in polarised cell division orientation, progression and outcome. We hope this new illustration clarifies further the mechanisms described in this study.

*- Finally, to understand the relevance of S100A11 in the context of 3D polarised mammary epithelia, it would be very interesting to analyse the effect of S100A11 knock-downn in mouse mammary epithelial acini grown in matrigel. This is not essential for the proposed studies, but would add biological relevance to the mechanisms characterised in 2D colture. *

__Authors response: __We agree with the Reviewer that validating our findings in 3D cultures of mammary epithelial cells will be important to determine the influence of S100A11-mediated regulation of plasma membrane dynamics during mitosis on lumen formation and tissue morphogenesis. This is exactly the direction where the follow-up of these findings will go. While the first author who led this work has graduated and left our lab, we have recently recruited a new PhD student to address this important question, which will need a few years of investigation to provide important insights, similarly to what we did in our previous work (Fankhaenel et al., 2023 Nat Commun).

*Minor comments: *

*- It would be preferable to mention the known functions of S100A11 in the introduction rather than at the beginning of the paragraph at pg. 9. *

__Authors response: __In response to the Reviewer’s suggestion, we have now moved the paragraph describing known functions of S100A11 to the introduction of the revised manuscript (see page 5).

*- at pg 10, beginning of paragraph, I find it a weird phrasing that "LGN interacts with F-actin". As reported in the reference cited here, this is through Afadin, which binds simultaneously LGN and cortical F-actin. I would rephrase it. *

__Authors response: __We thank the Reviewer for clarifying this point, which we have now rectified in the revised manuscript (see page 11).

__Reviewer #1 (Significance (Required)): __

*The description of cell adhesion as key factor instructing correct mitotic progression and execution of oriented division of vertebrate epithelial cells by controlling plasma membrane dynamics is novel and interesting for scientist in the spindle orientation/polarity field. The experiments are well-designed and perfectly executed and presented. I am in favour of publication of the manuscript, providing that a few points are addressed. *

Authors response: We thank the Reviewer for their very positive evaluation of our work.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

*Establishment and maintenance of cell polarity are fundamental processes for physiology in multi-cellular organism given the fact that more than 380 million epithelial cell renewal for every second in human adults. However, the precise mechanisms linking plasma membrane polarity and cortical cytoskeleton dynamics of epithelial cells during mitotic exit and interphase remain ill-illustrated. Salah Elias and her colleagues experimentally manipulated the density of mammary epithelial cells in culture, which led to several mitotic defects. Specifically, they found that perturbation of cell-cell adhesion integrity impairs the dynamics of the plasma membrane during mitosis, affecting the shape and size of mitotic cells and resulting in defects in mitosis progression and generating daughter cells with aberrant cytoarchitecture. In these conditions, F-actin-astral microtubule crosstalk is impaired leading to mitotic spindle misassembly and misorientation, which in turn contributes to chromosome mis-segregation. Mechanistically, they identified the S100 Ca2+-binding protein A11 as a key membrane-associated regulator that forms a complex with E-cadherin and LGN to coordinate plasma membrane remodelling with E-cadherin-mediated cell adhesion and LGN-dependent mitotic spindle machinery. I felt that this is a strong manuscript for peer-review as it serves diversified interests in modern cell biology. *

Authors response: We thank the Reviewer for their overall very positive feedback on our manuscript.

__Reviewer #2 (Significance (Required)): __

Several key cellular experiments should be repeated using a second line of epithelial cells such as RPE1.

__Authors response: __We agree with the Reviewer it will be interesting to test our findings in other epithelial cells, including RPE1 cells, a widely used epithelial cell model to study the mechanisms controlling cell division. Nonetheless, we would like to emphasise that while our work demonstrates the importance of the interplay between plasma membrane dynamics and cell-cell adhesion for correct execution of polarised cell divisions in mammary epithelial cells, our aim is not to generalise the role of these S100A11-mediated mechanisms. An elegant study has shown that the mechanisms controlling plasma membrane remodelling and elongation during mitosis to ensure correct positioning of the mitotic spindle and symmetric division differ between HeLa cells and RPE1 cells (Kiyomitsu and Cheeseman, 2013 Cell). Additional experiments in a second cell line will require a thorough characterisation of the expression and localisation of S100A11 during the cell cycle, as well as the use of extensive and time-consuming knockdown and imaging experiments over several months and may lead to different observations requiring further mechanistic investigation, which is beyond the initial scope of this study. Additionally, the PhD student who led this study has graduated and left the lab and presently we don’t have capacity or resources to conduct these suggested experiments. Finally, to precisely address the Reviewer’s concern, we have now amended the revised manuscript to make our statements more specific to mammary epithelial cells throughout the text.

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

*Summary: your understanding of the study and its conclusions. *

*The scope of the study is to understand the links between cell-cell adhesion integrity, plasma membrane dynamics and mitotic spindle in mammalian epithelial tissues. To test this, the authors cultured mammary epithelial cells at optimal or low density as a way of perturbing cell-cell adhesion. The authors conclude that perturbing cell-cell adhesion alters plasma membrane dynamics, causing mitotic defects and that S100A11 coordinates this link via E-cadherin. Whilst this is an interesting manuscript, illustrating the differences of mitotic success in optimal density vs. low density cell cultures, I do not think that the conclusions are supported by the evidence presented for the reasons stated below. *

*Major comments: major issues affecting the conclusions. *

*- The manuscript clearly shows that culturing cells at a lower density results in a higher incidence of asymmetric division (figure 1) and mitosis defects (figure 2). Cells round more and faster and there is more actin at the cortex during rounding (figure 3). However, whilst differences in cell-cell adhesion are likely to play a role in mediating these effects, I don't think that it is possible to claim from the data presented that these defects are specifically due to cell-cell adhesion differences. This is because the morphology of cells at low density is also very different - cells appear more mesenchymal, with migratory front-rear polarity instead of apical-basal polarity. These cells will therefore have many differences between them, cell-adhesion being just one. The data is also not showing a 'loss' of cell-cell adhesion integrity but are rather illustrating the differences between cells that have formed cell-cell adhesions and those that have not. To really test the specific role of cell-cell adhesions, the authors would need to inhibit adhesions directly but without altering the cell density - for example via chemical or genetic perturbation within a confined environment. I suggest that the authors either need to do these experiments or to requalify what their data is telling us. *

__Authors response: __We thank the Reviewer for their insightful discussion of the proposed mechanisms described in our manuscript. Several of the Reviewer’s comments pinpoint and exactly match the messages that we would like to convey to the scientific community. Therefore, to address the Reviewer’s comments, we have carefully requalified our statements in several places in the revised manuscript, to ensure they are more clear and more precise.

We agree with the Reviewer’s comment that our experiments using sub-optimal density of mammary epithelial cells rather prevents the formation of cell-cell adhesions than disturbing them. The Reviewer is right, our experiments in low-density cultures suggest that perturbation of cell-cell adhesion formation impairs mammary epithelial identity, where cells lose their polarity and adopt a more mesenchymal phenotype, associated with plasma membrane remodelling defects. This affects the dynamics and progression of cell division. Nonetheless, our observations suggest an interplay between cell-cell adhesion and the plasma membrane to maintains correct cell shape during mitosis. To test this hypothesis, we explored the function of S100A11 which we have identified in the LGN interactome in mitotic mammary epithelial cells (Fankhaenel et al., 2023 Nat Commun), and which has been shown to interact with E-cadherin at adherens junctions in MDCK cells (Guo et al., 2014 Sci Signal). This, together with the fact that S100A11 controls plasma membrane repair (Jaiswal et al., 2014 Nat Commun), suggested S100A11 as an interesting candidate to investigate the interplay between cell-cell adhesion and membrane remodelling during mitosis. The data presented here suggest that we were right and the perturbation of our membrane-bound target, S100A11, indeed leads to the same mitotic phenotypes. S100A11 RNAi-mediated knockdown (48h) affects E-cadherin localisation at the plasma membrane and impairs cell-cell adhesion formation with effects on plasma membrane dynamics that phenocopy the defects observed in our low-density culture experiments. Remarkably, perturbation of cell-cell adhesions persisted in cell treated with si-S100A11 for 72h (see Figure S3). Of note, all our siRNA experiments have been carried out in cells cultured at optimal density to establish cell-cell adhesions. Thus, S100A11 knockdown allows genetic perturbation of E-cadherin-mediated cell-cell adhesion and recapitulates the plasma membrane and mitotic defects observed in sub-optimal cultures of mammary epithelial cells. Future experiments will be key to dissect these S100A11-mediated mechanisms to further understand how plasma membrane remodelling and cell-cell adhesions are coordinated during mitosis. Finally, as suggested by the Reviewer, we have now requalified our conclusions as appropriate in the revised manuscript.

*- The current manuscript also demonstrates that cell adhesion is affected when S100A11 is knocked down (figure 4). It shows binding between and colocalization of S100A11 and E-cadherin, and shows that LGN cortical distribution is affected when S100A11 is knocked down (Figure 5). The results presented are suggestive of S100A11 being upstream of E-cadherin. However, I don't understand how the data shows "crosstalk between the plasma membrane, cell-cell adhesion, and the cell cortex during mitosis". For example, on P9: "We observed unequal distribution of CellMaskTM in a vast majority of S100A11-depleted cells (si-S100A11#1: ~79% versus si-Control: ~26%), indicating defects in plasma membrane remodelling (Figures 4B and 4C)." I don't agree that this demonstrates a defect in PM remodelling. Rather the cells in the representative images are less adherent and have adopted a more migratory cell state similar to that seen in figure 1 when seeded at low density. The fluidity of the much larger cells shown in knock down cells in panel F also appears higher, again suggesting an adhesion defect. *

• *

__Authors response: __The Reviewer has raised very important points here, which we would like to clarify.

We agree with the Reviewer that our results in S100A11-depleted cells indicate impaired cell adhesions which generates cells displaying an invasive/migratory behaviour. However, our analysis of S100A11-depleted mitotic cells labelled with CellMaskTM reveals abnormal plasma membrane elongation generating two daughter cells displaying defective geometry as compared to control cells. These defects in the plasma membrane and cell shape were not noticeable upon E-cadherin knockdown (see previous Figures 5K and 5L; now new Figures 6K and 6L). Thus, our results strongly suggest that S100A11 acts as an upstream cue that coordinates plasma membrane dynamics with E-cadherin-mediated cell adhesions, and that additional mechanisms may be regulated by S100A11 to coordinate cell-cell adhesion with plasma membrane remodelling. How S100A11 ensures such a dynamic interplay between the plasma membrane and E-cadherin during mitosis remains a key question that we have not fully addressed in this initial study. An attractive mechanism could be mediated by the function of S100A11 in regulating the dynamic interaction between F-actin and the plasma membrane, as previously reported (Jaiswal et al., 2014 Nat Commun). Increasing evidence shows the importance of the crosstalk between the plasma membrane, the cortex and cell shape for correct execution of mitosis (Rizzelli et al., 2020 Open Biol). In our experiments, we show that impaired plasma membrane remodelling and cell shape are associated with defects in F-actin and astral microtubule organisation. Thus, our findings reinforce a model whereby S100A11 is a key membrane-associated protein that coordinates the crosstalk between the plasma membrane, cell-cell adhesion, and the cell cortex during mitosis. It will be key to characterise the interactome of S100A11 during mitosis to provide important mechanistic insights into this new role of S100A11; it is our intention to investigate this in the future.

To address the points raised by the Reviewer, we have changed and clarified the statements they highlighted above, in the revised manuscript (pages 10 and 11).

*- An earlier paper from the same lab this year identified Annexin A1 as directing mitotic spindle orientation via localising LGN at lateral cortex. During this earlier paper they also identified S100A11, which is a partner for Annexin A1. The authors could more clearly explain what S100A11 is in the current manuscript and how the current study builds on this earlier study. *

__Authors response: __We thank the Reviewer for highlighting our previous work characterising the interactome of LGN in mitotic mammary epithelial cells (Fankhaenel et al., 2023 Nat Comms), and identifying Annexin A1 (ANXA1) as a polarity cue regulating the localisation and function of the evolutionarily conserved mitotic spindle orientation LGN complex. We also showed that ANXA1 direct partner S100A11 co-purifies with LGN and that perturbation of the ANXA1-S100A11 complex impairs the localisation of the LGN complex at the cell cortex during mitosis. Thus, as rightly pointed out by the Reviewer, this work builds on our previous work discussed above, but also on previous studies establishing S100A11 as a key regulator of plasma membrane repair by regulating the dynamic interplay between F-actin and the plasma membrane (Jaiswal et al., 2014 Nat Commun), and studies showing that S100A11 interacts with E-cadherin at adherens junctions (Guo et al., 2014 Sci Signal). To address the Reviewer’s point (also raised by Reviewer 1), we have now included a paragraph in the introduction (page 5) and results (page 10) of the revised manuscript describing these and other functions of S100A11 to provide a strong rational to our decision to investigate this protein.

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*- Based on the data presented, I suggest that the authors should requalify their data. I suggest that the conclusions that can be drawn from the data are that cellular state is important for regulating mitosis orientation and fidelity (i.e. adherent epithelia cells vs. less adherent more migratory cells). S100A11 is important for promoting cell-cell adhesions and might be upstream of the known role of E-cadherin in regulating spindle orientation. Whilst I suggest that more quantified experiments would need to be included in order to assess possible effects on plasma membrane remodelling, the manuscript could be generally improved by a clearer explanation of the open question that they are addressing and what specific advance this manuscript has made in relation to the current literature, including their own. I do not currently feel that the title of the manuscript is appropriate since I don't think that a crosstalk between the plasma membrane and cell-cell adhesion has been shown here. *

__Authors response: __We would like to reiterate our agreement with the Reviewer’s suggestion about the conclusions drawn from our data. In the initial submission we proposed that perturbation of S100A11-mediated regulation of cell adhesion and plasma membrane impairs the identity of mammary epithelial cells, which affects their shape during mitosis leading to aberrant mitotic progression and outcome. While we have not checked the migratory behaviour of cells not forming cell-cell adhesions, we suggested that the cells adopted a mesenchymal phenotype. Furthermore, we discussed the implication of epithelial-to-mesenchymal transition on chromosome segregation fidelity and execution of mitosis, and how precisely they link with our study (see initial submission’s pages 14 and 19). As suggested by the Reviewer, we have now clarified further these observations in the results (pages 7 and 11) and discussion (pages 15 and 19) of the revised manuscript.

We have quantified several aspects of the changes in plasma membrane dynamics and remodelling throughout, in the initial manuscript (Figure 1D-H; Figure 4C). To address the Reviewer’s point, we have now added quantifications of membrane blebbing (new Figure 1I).

We would like to emphasise that the introduction of the initial manuscript has included the open questions that led to this study. These questions have been addressed further in the discussion, where we have also formulated new hypotheses and discussed what we think are the important outstanding questions for future investigations, in light of our findings. In this study we demonstrate that maintaining epithelial identity is essential for correct execution of polarised cell divisions. Our findings indicate that mammary epithelial cells grown at sub-optimal density lose their epithelial identity, which results in several mitotic defects. We propose a novel mechanism in which S100A11 acts as a molecular sensor of external cues coordinating the interplay between plasma membrane dynamics and cell-cell adhesion to maintain epithelial identity and integrity, thereby ensuring correct progression, orientation, and outcome of cell division. As suggested by the Reviewer, we have clarified further the advances made in this study, in the revised Results and Discussion sections.

To address the Reviewer’s final point, we would like to suggest the following revised title “Interplay between the plasma membrane and cell-cell adhesion maintains epithelial identity for correct polarised cell divisions”, which we hope reflects better the results described in our studies.

*Minor comments: important issues that can confidently be addressed. *

- P3: I wouldn't describe the junctional proteins listed as polarity proteins.

__Authors response: __We have now made this rectification in page 3, as suggested by the Reviewer.

*- Figure 1 - can the membrane blebbing phenotype by quantified? At the moment this part is observational so can't really be used to determine the role of plasma membrane remodelling. *

• *

__Authors response: __We have now included quantifications of blebbing in the revised manuscript, as suggested by the Reviewer (new Figure 1I).

*- Figure 3. I'm not sure what the 'subcortical actin cloud' measurement is. Figure 3G suggests it may be the distance from the cortex to the spindle pole but how does this relate to actin? *

__Authors response: __The Reviewer is right, the subcortical actin cloud includes a pool of dynamic subcortical actin that extends from the cortex (excluding the stiff cortical actin) to the cytoplasm, interacting with the centrosomes and concentrating near the retraction fibres. The subcortical actin cloud has been shown to mediate cortical forces and to concentrate force-generating proteins at the retraction fibres acting on centrosome dynamics and pulling on astral microtubules to orient the mitotic spindle (for example, please see Kwon et al., 2015 Dev Cell). We have now included this clarification in the revised manuscript (page 10).

*- Figure 4A. I can't see GFP-S100A11 accumulating at the cell surface. To me these images suggest that it is relatively ubiquitously expressed throughout the cytoplasm and surface, which is different to the later antibody stains, that show localisation at the cell surface. *

__Authors response: __A similar point has been raised by Reviewer 1. Although our retroviral-mediated transduction allows to avoid excessive expression of GFP-S100A11, the ectopic S100A11 is expressed at higher levels as compared to its endogenous counterpart. Our live images show an accumulation of the protein at the cell surface, but relatively high levels are also visible in the cytoplasm (previous Figure 4A, new Figure S4A). By contrast immunolabelling for endogenous S100A11 shows an obvious accumulation of the protein at the plasma membrane. This difference could also be due to a dynamic behaviour of the protein translocation of GFP-S100A11 between the cell surface and cytoplasm that is captured in our live imaging. Similar slight differences between immunofluorescence and live imaging of cortical proteins involved in mitosis, such as Dynein, NuMA, LGN and CAPZB, have been reported in several studies (to cite a few: di Pietro et al., 2017 Curr Biol; Elias et al., 2014 Stem Cell Rep; Fankhaenel et al., 2023). To address this point, we have now moved the panel showing S100A11 immunofluorescence in Figure S3A to new Figure 4A (also see response to Reviewer 1 Major Point 1).

*- Fig 4H doesn't show an active process of translocation of E-Cadherin to the cytoplasm. It shows representative images with slightly higher levels of E-Cadherin in the cytoplasm. This could be due to translocation or it could be to do with lack of E-Cadherin assembly. *

• *

__Authors response: __We thank the Reviewer for pointing this out. We have rectified this statement accordingly (page 11).

*- 4I I don't understand where the line profile is derived from - where is apical and where is basal in the images? Could a diagram be included? *

__Authors response: __We have now included an illustration of this quantification, in the revised manuscript (new Figure 4J).

- The discussion could be shortened and more clearly written - perhaps with subheadings of the main findings.

__Authors response: __We have clarified several ideas and statements, based on the specific points addressed above. While it is challenging to reduce the size of this section, given that the study addresses several mechanisms of mitosis, we have now shortened the discussion in the revised manuscript.

*- Methods: Why is cholera toxin used in the cell culture medium? *

• *

__Authors response: __Cholera toxin is a key component of MCF-10A medium, which has been shown to stimulate cAMP activation promoting cell proliferation in culture. This culture protocol is a gold standard in the field (Debnath et al., 2023 Methods). Given that cholera toxin is a highly regulated chemical and takes several months to purchase, we have tried culturing MCF-10A without the toxin, but this negatively affected proliferation and passage of this cells. Therefore, we concluded that adding it to the culture medium is important.

__Reviewer #3 (Significance (Required)): __

*In general, this is an interesting paper about the fidelity of mitosis in cells in adherent monolayers vs. in more migratory, non-adherent states. There is existing literature on this topic (some cited in the manuscript, alongside reviews of the topic). *

• *

*The main conceptual advance, as far as I can see, is that S100A11 is important for promoting cell-cell adhesions and might be upstream of the known role of E-cadherin in regulating spindle orientation via LGN. The main limitation is that plating cells at different densities is not a direct 'perturbation' of cell-cell adhesion. This means that the phenotypes seen could be due to many factors, not just cell adhesion. Assessment of plasma membrane and cytoskeletal dynamics are also often observational and not conclusive. *

• *

*The manuscript would be of interest to basic researchers working on epithelial development. Also potentially to basic researchers working on cancer, due to the mitotic errors described. *

• *

*I have expertise in epithelial cell biology. *

I estimate the authors would need between 3 and 6 months for revisions if they decide to do further experiments and between 1 and 3 months if they decide to re-qualify their claims.

• *

__Authors response: __We thanks the Reviewer for their overall positive feedback on our work and its broader importance for researchers in epithelial development and cancer biology.

We would like to reiterate our agreement with the Reviewer’s assessment of the conceptual advances of our work. We show that S100A11 complexes with E-cadherin and LGN during mitosis to control cell-cell adhesion assembly and the mitotic spindle machinery, respectively, which in turn ensures faithful chromosome segregation. Our results also suggest that S100A11 lies upstream of E-cadherin in the regulation of the LGN-mediated mitotic spindle machinery. We also agree with the Reviewer that plating epithelial cells at low density does not directly affect cell-cell adhesion, because, in these culture conditions, cells are not dense enough to establish cell-cell contacts necessary to assemble stable adherens junctions. Rather, and as rightly pointed out by the Reviewer, cells grown at low density fail to maintain their epithelial identity and adopt a more mesenchymal and elongated behaviour, which is accompanied by dramatic changes in plasma membrane remodelling throughout mitosis. Interestingly, our results show that both S100A11 and E-cadherin do not localise at the plasma membrane in these sub-optimal culture conditions. This along with our results showing that depletion of S100A11 phenocopies the effect of low-density culture conditions on plasma membrane remodelling and E-cadherin mediated cell-cell adhesion assembly, allow us to propose a mechanism whereby the membrane-associated S100A11 protein acts as a molecular sensor of external cues bridging plasma membrane remodelling to E-cadherin-dependent cell adhesion to coordinate correct progression and outcome of mammary epithelial cell divisions.

We are grateful for the Reviewer’s insightful discussion of our findings. As we discussed above in our responses to their specific points, we have requalified many of our statements to clarify further our main findings and conclusions throughout the revised manuscript. We have also added new quantifications in response to the Reviewer’s suggestions. We believe, that together, these revisions have advanced further the initial manuscript.

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Referee #3

Evidence, reproducibility and clarity

Summary: your understanding of the study and its conclusions.

The scope of the study is to understand the links between cell-cell adhesion integrity, plasma membrane dynamics and mitotic spindle in mammalian epithelial tissues. To test this, the authors cultured mammary epithelial cells at optimal or low density as a way of perturbing cell-cell adhesion. The authors conclude that perturbing cell-cell adhesion alters plasma membrane dynamics, causing mitotic defects and that S100A11 coordinates this link via E-cadherin. Whilst this is an interesting manuscript, illustrating the differences of mitotic success in optimal density vs. low density cell cultures, I do not think that the conclusions are supported by the evidence presented for the reasons stated below.

Major comments: major issues affecting the conclusions.

The manuscript clearly shows that culturing cells at a lower density results in a higher incidence of asymmetric division (figure 1) and mitosis defects (figure 2). Cells round more and faster and there is more actin at the cortex during rounding (figure 3). However, whilst differences in cell-cell adhesion are likely to play a role in mediating these effects, I don't think that it is possible to claim from the data presented that these defects are specifically due to cell-cell adhesion differences. This is because the morphology of cells at low density is also very different - cells appear more mesenchymal, with migratory front-rear polarity instead of apical-basal polarity. These cells will therefore have many differences between them, cell-adhesion being just one. The data is also not showing a 'loss' of cell-cell adhesion integrity but are rather illustrating the differences between cells that have formed cell-cell adhesions and those that have not. To really test the specific role of cell-cell adhesions, the authors would need to inhibit adhesions directly but without altering the cell density - for example via chemical or genetic perturbation within a confined environment. I suggest that the authors either need to do these experiments or to requalify what their data is telling us. The current manuscript also demonstrates that cell adhesion is affected when S100A11 is knocked down (figure 4). It shows binding between and colocalization of S100A11 and E-cadherin, and shows that LGN cortical distribution is affected when S100A11 is knocked down (Figure 5). The results presented are suggestive of S100A11 being upstream of E-cadherin. However, I don't understand how the data shows "crosstalk between the plasma membrane, cell-cell adhesion, and the cell cortex during mitosis". For example, on P9: "We observed unequal distribution of CellMaskTM in a vast majority of S100A11-depleted cells (si-S100A11#1: ~79% versus si-Control: ~26%), indicating defects in plasma membrane remodelling (Figures 4B and 4C)." I don't agree that this demonstrates a defect in PM remodelling. Rather the cells in the representative images are less adherent and have adopted a more migratory cell state similar to that seen in figure 1 when seeded at low density. The fluidity of the much larger cells shown in knock down cells in panel F also appears higher, again suggesting an adhesion defect. An earlier paper from the same lab this year identified Annexin A1 as directing mitotic spindle orientation via localising LGN at lateral cortex. During this earlier paper they also identified S100A11, which is a partner for Annexin A1. The authors could more clearly explain what S100A11 is in the current manuscript and how the current study builds on this earlier study.

Based on the data presented, I suggest that the authors should requalify their data. I suggest that the conclusions that can be drawn from the data are that cellular state is important for regulating mitosis orientation and fidelity (i.e. adherent epithelia cells vs. less adherent more migratory cells). S100A11 is important for promoting cell-cell adhesions and might be upstream of the known role of E-cadherin in regulating spindle orientation. Whilst I suggest that more quantified experiments would need to be included in order to assess possible effects on plasma membrane remodelling, the manuscript could be generally improved by a clearer explanation of the open question that they are addressing and what specific advance this manuscript has made in relation to the current literature, including their own. I do not currently feel that the title of the manuscript is appropriate since I don't think that a crosstalk between the plasma membrane and cell-cell adhesion has been shown here.

Minor comments: important issues that can confidently be addressed.

P3: I wouldn't describe the junctional proteins listed as polarity proteins. Figure 1 - can the membrane blebbing phenotype by quantified? At the moment this part is observational so can't really be used to determine the role of plasma membrane remodelling.

Figure 3. I'm not sure what the 'subcortical actin cloud' measurement is. Figure 3G suggests it may be the distance from the cortex to the spindle pole but how does this relate to actin?

Figure 4A. I can't see GFP-S100A11 accumulating at the cell surface. To me these images suggest that it is relatively ubiquitously expressed throughout the cytoplasm and surface, which is different to the later antibody stains, that show localisation at the cell surface.

Fig 4H doesn't show an active process of translocation of E-Cadherin to the cytoplasm. It shows representative images with slightly higher levels of E-Cadherin in the cytoplasm. This could be due to translocation or it could be to do with lack of E-Cadherin assembly.

4I I don't understand where the line profile is derived from - where is apical and where is basal in the images? Could a diagram be included?

The discussion could be shortened and more clearly written - perhaps with subheadings of the main findings.

Methods: Why is cholera toxin used in the cell culture medium?

Significance

In general, this is an interesting paper about the fidelity of mitosis in cells in adherent monolayers vs. in more migratory, non-adherent states. There is existing literature on this topic (some cited in the manuscript, alongside reviews of the topic).

The main conceptual advance, as far as I can see, is that S100A11 is important for promoting cell-cell adhesions and might be upstream of the known role of E-cadherin in regulating spindle orientation via LGN. The main limitation is that plating cells at different densities is not a direct 'perturbation' of cell-cell adhesion. This means that the phenotypes seen could be due to many factors, not just cell adhesion. Assessment of plasma membrane and cytoskeletal dynamics are also often observational and not conclusive.

The manuscript would be of interest to basic researchers working on epithelial development. Also potentially to basic researchers working on cancer, due to the mitotic errors described.

I have expertise in epithelial cell biology.

I estimate the authors would need between 3 and 6 months for revisions if they decide to do further experiments and between 1 and 3 months if they decide to re-qualify their claims.

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Referee #2

Evidence, reproducibility and clarity

Establishment and maintenance of cell polarity are fundamental processes for physiology in multi-cellular organism given the fact that more than 380 million epithelial cell renewal for every second in human adults. However, the precise mechanisms linking plasma membrane polarity and cortical cytoskeleton dynamics of epithelial cells during mitotic exit and interphase remain ill-illustrated. Salah Elias and her colleagues experimentally manipulated the density of mammary epithelial cells in culture, which led to several mitotic defects. Specifically, they found that perturbation of cell-cell adhesion integrity impairs the dynamics of the plasma membrane during mitosis, affecting the shape and size of mitotic cells and resulting in defects in mitosis progression and generating daughter cells with aberrant cytoarchitecture. In these conditions, F-actin-astral microtubule crosstalk is impaired leading to mitotic spindle misassembly and misorientation, which in turn contributes to chromosome mis-segregation. Mechanistically, they identified the S100 Ca2+-binding protein A11 as a key membrane-associated regulator that forms a complex with E-cadherin and LGN to coordinate plasma membrane remodelling with E-cadherin-mediated cell adhesion and LGN-dependent mitotic spindle machinery. I felt that this is a strong manuscript for peer-review as it serves diversified interests in modern cell biology.

Significance

Several key cellular experiments should be repeated using a second line of epithelial cells such as RPE1.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Crosstalk between the plasma membrane and cell-cell adhesion maintains epithelial identity for correct polarised cell divisions" by Dr. Hosawi and colleagues reports the characterisation of the mitotic connection between plasma membrane dynamics and division orientation in polarised mammalian epithelial cells in culture. The authors start from the comparison of mitotic events of human mammary MCF10A cells grown at optimal density or at low density. They observed that only at optimal density MCF10A cells polarise by E-cadherin mediated cell-cell contacts, and display uniform membrane enrichment at the cortex, whereas cells grown at low density do not show cortical E-Cadherin enrichment, and distribute aberrantly the plasma membrane at one side and in cytoplasmic vesicles, generating daughter cells with unequal size. Consistently, further analyses revealed that low-density MCF10A cells undergo misoriented mitosis, with chromosome congression and misegregetion defects. Mechanistically, low density MCF10A cells fail to organise a symmetric mitotic spindle and center it in metaphase. This is due to an increased cortical actomyosin thickness coupled to abnormal astral microtubule stability. Building on previous data from the Elias lab, the authors uncover a role of the membrane-associated S100A11 protein in maintaining correct plasma membrane dynamics and E-cadherin localisation in mitosis. Further dissection of the molecular mechanism underlying this mitotic function od S10011A revealed that it enriches at the cortex only in optimal-density MCF10A cells, and promotes spindle orientation by association with LGN and E-cadherin, upstream of E-cadherin. This evidence depicts the plasma membrane and S100A11 proteins as a key mechanical sensors of cell-cell adhesion orchestrating the recruitment of E-cadherin and LGN-dependent force generators to ensure correct division orientation.

Major points:

• Important information is presented in Supplementary Figure S3. I suggest to move these panels in the main figures. Specifically, I would replace figure 4A with S3A showing the distribution of endogenous S100A11 in MCF10A cells, rather than the one of the GFP-tagged version which is over-expressed.
• The mechanisms of division orientation governed by S100A11 seems to impinge on the control of cortical F-actin and astral microtubule dynamics. This is illustrated in figure S3C, which in my opinion should be shown in the main figures with some more explanation / experiments. The authors mention the " tight actin F-actin bundles at the cell-cell contacts" that are lost in S100A11-depleted cells, and that interact with astral microtubules. However this is not fully clear in figure S3C. I think the authors should find a way to present better these evidence which is key in supporting their molecular model.
• I think the discussion would benefit from the addition of a graphical cartoon model illustrating the role of S100A11 in controlling plasma membrane dynamics in mitosis and spindle orientation.
• Finally, to understand the relevance of S100A11 in the context of 3D polarised mammary epithelia, it would be very interesting to analyse the effect of S100A11 knock-downn in mouse mammary epithelial acini grown in matrigel. This is not essential for the proposed studies, but would add biological relevance to the mechanisms characterised in 2D colture.

Minor comments:

• It would be preferable to mention the known functions of S100A11 in the introduction rather than at the beginning of the paragraph at pg. 9.
• at pg 10, beginning of paragraph, I find it a weird phrasing that "LGN interacts with F-actin". As reported in the reference cited here, this is through Afadin, which binds simultaneously LGN and cortical F-actin. I would rephrase it.

Significance

The description of cell adhesion as key factor instructing correct mitotic progression and execution of oriented division of vertebrate epithelial cells by controlling plasma membrane dynamics is novel and interesting for scientist in the spindle orientation/polarity field. The experiments are well-designed and perfectly executed and presented. I am in favour of publication of the manuscript, providing that a few points are addressed.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

This MS contains carefully carried out and well controlled experiments describing a new pFFAT in ELYS. There is a similarly convincing demonstration of functionally relevant colocalisation by proximity ligation assay (PLA), particularly that both ELYS and VAP are nuclear envelope proteins in interphase without interacting (neg control in Fig 4D).

Major Issue: Functional significance

A key conclusion is that experiments prove that "ELYS serves as the crucial initiation factor for post-mitotic NPC-assembly" (p5). However, evidence for this is lacking as this would require reconstitution of NPC assembly with a mutant form of ELYS carefully changing the FFAT motif (e.g. 1321A 1324E) and exclusion of other probable VAP targets in experiments with mutant VAP. VAPs are among the proteins with the highest number of documented interactors (see Huttlin 2015/7 etc, e.g. PMID 26186194), so knocking down VAP may have pleiotropic effects and quite indirect read-outs in many aspects of cell function. In addition, for this work specifically there are other NE proteins that are known interactors of VAP: Emerin (EMD) and LBR both interact with VAP (high-throughput data, VAPA and VAPB). EMD has a motif similar to the canonical phospho-FFAT: 98 SYFTTRT 104. LBR has no motif. These findings should not be overlooked in this work. For example, was the interaction with emerin (page 4) sensitive to mutating VAP or ELYS? Could the effect seen in Figure 5 result from interactions with proteins other them ELYS?

Further experiments should be carried out to justify all statements in the current MS of functional significance. Instead of doing more experiments, an alternative for the authors would be to describe the current set of results more cautiously. However, that would require changing much of the impact of the current MS, from the title onwards.

Moderate Issue: VAPA

From the start of the Introduction and some elements of the Discussion, include VAPA in equal measure with VAPB. When describing interactions of ELYS with VAP note that Huttlin et al., reported interactions twice for each of VAPA and VAPB. When describing own results (James et al. 2019) and those of others (Saiz-Ros et al., 2019) that focused on VAPB, clarify if the authors' view is that VAPA would (or would not) have the same interaction.

Is there any evidence that only VAPB is on NE? Note that some refs in the Introduction relate to VAPA: Mesmin (not VAPB); ACBD5: although article titles refer to VAPB, early work (10.1083/jcb.201607055) showed almost identical involvement of VAPA. Also, this redundancy likely explains "function of VAPB in mitosis is not essential," (in Discussion). The lack of effect of VAPA knock-down may indicate that in these cells VAPB is dominant, but does not exclude a role for VAPA when VAPB is reduced. That might be tested by depleting both. Even following that, there is MOSPD2 to consider

Other aspects of the writing

"two amino acid residues are crucial for the interaction (VAPB K87 and M89)." This is wrong. Many residues are critical, these are merely 2 of possibly >10 that were chosen by Kaiser et al (2005) to create their non-binder.. Others have used different mutations to block FFAT binding.

"They may exhibit a certain binding preference to specific members of the VAP ... family...". I cannot think of any example. I note no citation is given.

When listing many or all MSP proteins, the text should state that MOSPD2 is uniquely close to VAPA/B. CFAP65 is typically not mentioned in the VAP-like lists as it does not have any of the conserved sequence that binds FFAT. If however the authors wish to include all human MSP domain protein, they should also include Hydin.

Slightly wrong to cite De Vos et al., 2012 about PTPIP51's FFAT as that paper makes no mention of the motif. Better pick Di Mattia (again)

On VAPB (and also A) on INM: there are references to be cited esp. relating to intranuclear Scs2 in yeast (Brickner et al 2004, Ptak et al 2021)

Citations for VAP at ER-mito contacts "De Vos et al., 2012; Gómez-Suaga et al., 2019; Stoica et al., 2014)". These all refer to the same bridging protein, PTPIP51. Reduce to one citation. Then mention other proteins at the same site VPS13A, mitoguardin(MIGA)-2 ...

"The domain interacts with characteristic peptide sequences ..." add citation to this sentence

"Several variants of such motifs have been described: (i)" ... "(ii)": (i) and (ii) are entirely unlinked. Delete these and also "Several variants of such motifs have been described." Which is repeated later

"FFAT-like motifs come in different flavors and may even lack the two phenylalanine residues (Murphy and Levine, 2016)": while motifs can tolerate variation at both positions, this text is misleading as it implies much more variation than is known. The 1st F can only be conservatively substituted (Y).

Minor aspects in Results:

ORP1L peptide as positive control: cite Kaiser 2005

Was phosphoproteomics done in such a way as to find peptides that have both S1314 and S1326?

Figure 4D, row 2: Comment on intranuclear staining in Prophase (at approx 4 o'clock) of both ELYS & VAP that is PLA positive

Referees cross-commenting

I agree with this point from Reviewer #1. We all agree that the main issue can be resolved experimentally to determine the effect of subtle point mutations in ELYS. Both other reviewers have done a good job in finding issues with the experiments that can also be addressed.

Significance

This work documents an interaction between the protein ELYS, that is involved in the reformation of nuclear pore complexes after mitosis, and the ER membrane protein VAPB. The interactions was previously known through high-throughput studies, along with many 100's of others for VAP, but here it is studied in detail and with care, identifying how the motif is induced by phosphorylation of ELYS. The two proteins are co-localised using convincing proximity ligation assays. This biochemistry and cell biological localisation is well done.

Functional experiments then show that VAP (in this case VAPB) knock-down affects mitosis and chromosome segregation. While the result is incontrovertible, it has many possible interpretations, mainly because VAP has hundreds of interactions, including with multiple proteins involved in mitosis beyond just ELYS. This means that there are major limitations on how the interaction and co-localisation should be interpreted, reducing the advance associated with the current manuscript to incremental, and the limiting the audience to specialized.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, James et al. follow up on their prior discovery that the ER contact site protein VAPB localizes to the nuclear envelope and is a putative binding partner of the nucleoporin ELYS, which coordinates nuclear envelope reformation (NER) with nuclear pore complex (NPC) biogenesis at mitotic exit and is also a constituent of the nuclear facing Y-complexes of mature NPCs. Using a series of complementary biochemical approaches the authors 1) demonstrate that VAPB and ELYS directly interact, 2) map the binding sites on ELYS that are sufficient to bind VAPB, 3) show that mutations that disrupt VAPB-FFAT motif binding also abrogate binding to ELYS including of the full-length protein, 4) define mitotic phosphorylation sties on VAPB-bound ELYS, 5) demonstrate that phosphorylation of ELYS, specifically at the FFAT2 motif, is required for binding to VAPB, and 6) demonstrate that the phosphorylation of ELYS that regulates VAPB binding occurs in mitosis. Turning to cell biology, the authors find that VAPB, which is an established ER protein, has some preference for non-core regions during NER (like ELYS). In addition, PLA analysis suggests that the interaction of VAPB and ELYS is most robust during anaphase and is somewhat disrupted when the binding of VAPB to FFAT motifs is lost due to targeted mutation. Last, the authors demonstrate that depletion of VAPB leads to metaphase delay and lagging chromosomes.

Major comments:

The data supporting direct binding of peptides encoding the FFAT 1 and FFAT2 motif derived from ELYS to VAPB in a manner similar to other FFAT sequences is strong, as is the effect of phosphorylation of FFAT1 on the strength of this interaction.

The evidence supporting the mitotic-specific nature of the ELYS-VAPB interaction is strong, and that this interaction is direct, is also strong, and was rigorously tested using a combination of endogenous expression, heterologous expression, and recombinant protein approaches. Moreover, the sensitivity of this interaction to established mutations in VAPB abrogating FFAT interactions reinforces the outlined underlying biochemical interaction mechanism. The essentiality of ELYS phosphorylation (and therefore the mechanism underlying the mitotic specificity of the interaction) is also strongly supported by the data using phosphatase treatment. Although it is an intuitive model, whether the cell biological evidence support the simplest view that the ELYS-VAPB complex bridges the nuclear envelope to chromatin during NER in late anaphase / at mitotic exit is far less solid and, at a minimum, alternative models should be considered/discussed. For example, how a delay in metaphase in the siVAPB condition is consistent with a role in NER, which occurs exclusively post-metaphase, is unclear. Is it not possible that the VAPB-ELYS complex is regulated by phosphorylation during mitotic progression such that VAPB and/or ELYS can only exert their biological effects when released from the complex? In other words, might ELYS be licensed to act in NER only when it is released from VAPB, which could prevent premature NER/NPC biogenesis? Subtleties of when during mitosis the phosphorylation occurs is challenging, and it could be that the anaphase A to anaphase B transition, when many mitotic entry phosphorylation events begin to be reversed, could be relevant here. Along these lines, in Fig. 5 how the VAPB knock-down does or does not recapitulate the phenotype of an ELYS knock-down in this cell type (and the effect of the combination, to address epistasis) is needed for context, as is whether VAPB knock-down affects ELYS distribution in mitosis. ELYS knock-down would also be very beneficial for the PLA analysis to establish the "floor" of measurable signal. Last, it is also possible that VAPB has other roles in mitosis that should be acknowledged - for example although it is in yeast, it is relevant that a VAPB orthologue Scs2 is required for normal nuclear envelope expansion in mitosis by regulating SUMOylation (Ptak, Saik et al., JCB, 2021 and Saik et al., JCB, 2023) - this work should be referenced as well. Of course, the ideal experiment would be one in which an ELYS knock-down is complemented with a resistant form that encodes the S to A mutations in the FFAT2 region to assess its localization and to see if it can complement the knock-out function of ELYS in post-mitotic NPC assembly or, as suggested by a sequestration model, it can drive the same metaphase delay seen upon VAPB knock-down. This is technically challenging for sure, particularly given the size of the ELYS gene, but it would address the cell biological function of this interaction in the most direct manner. Several other observations that could warrant further comment or study include 1) is there a VAPB signal at the metaphase poles as suggested by Fig. 4A and, if so, could this represent aa distinct mitotic function?; 2) Does the HA-VAPB KD/MD mutant localize differently in mitosis compared to the WT - it appears that it might be less enriched in non-core regions (Fig. 4E)?; 3) does VAPB alter post-mitotic NPC biogenesis/number?

Minor comments:

I would suggest avoiding the use of "novel" when describing newly assembled NPCs or post-mitotic nuclear envelope reformation, as its other meaning of "non-standard" makes this wording confusing. It is unclear whether when the authors state that ELYS localizes "to the nuclear side of the nuclear envelope" they are referring to the nuclear aspect of the NPC and/or a separate pool at the INM - please edit to clarify. More descriptive y-axes for the plots in Fig. 4F and 5F and related legends would be useful; although the details are in the methods section, it would be nice not to have to hunt them down. Also, please clarify the meaning of blue and orange points in Fig. 4F.

Significance

General assessment: The biochemical analysis is rigorous and compelling and establishes the mitotic-specific interaction of VAPB and ELYS including detailed information about the binding interface and its regulation by phosphorylation. The new insight provided into the function of this VAPB-ELYS interaction is somewhat less well developed as the current manuscript, in its current form, does not yet mechanistically define the function of the VAPB-ELYS interaction in mitosis.

Advance: Conceptually, to the best of my knowledge, the idea that VAPB contributes to mitosis in mammalian cells is novel and is therefore impactful and will motivate further work. As the authors connect VAPB biochemically to ELYS, an established factor that promotes the coordination of NER and NPC biogenesis, this interaction is likely to be mechanistically important, although the specific details by which this interaction facilitate normal mitotic progression is not yet clear.

Audience: This work will be of interest to a broad swath of cell biologists including those interested in NPCs, the nuclear envelope, the ER, membrane remodeling, and chromosome segregation.

My expertise is in nuclear envelope dynamics, nuclear pore complexes, and chromatin organization.

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Referee #1

Evidence, reproducibility and clarity

Summary

The VAP proteins are well established as tail anchored proteins of the ER membrane. VAPs mediates co-operation between the ER and other organelles by creating a transient molecular tether with binding partners on opposing organelles to form a membrane contact site over which lipids and metabolites are exchanged. Proteins which bind VAPs generally contain a short FFAT motif, of varying sequence which binds the MSP domain of VAP. More recently the FFAT motif has been more extensively analysed in multiple different proteins and differential phosphorylation of the FFAT motif has been shown to either enhance or block VAP binding depending on the position of the phosphosite.

Recent work conducted by the authors demonstrated that a small population of VAPB is not exclusively localised to the ER and can also reach the inner nuclear membrane. They also identified ELYS as a potential interaction partner of VAPB in a screening approach. ELYS is a nucleoporin that can be found at the nuclear side of the nuclear envelope where it forms part of nuclear pore complexes. During mitosis, ELYS serves as an assembly platform that bridges an interaction between decondensing chromosomes and recruited nucleoporin subcomplexes to generate new nuclear pore complexes for post-mitotic daughter cells. In this manuscript, James et al seek to explore this enigmatic potential interaction between ELYS and VAPB to address why VAPB may be found at the inner nuclear membrane.

Peptide binding assays and some co-immunoprecipitation experiments are used to demonstrate that interactions occur via the MSP-domain of VAPB and FFAT-like motifs within ELYS. In addition, it is demonstrated that, for the ELYS FFAT peptides, the interaction is dependent on the phosphorylation status of serine residues of a particular FFAT-motif that can either promote or reduce its affinity to VAPB. Of most relevance is a serine in the acidic tract (1314) which, when phosphorylated increases VAPB binding. This is completely in line with what is already known about the FFAT motif and so is not surprising, in particular when using a peptide in an in vitro assay.

The authors then utilise cell synchronisation techniques to provide evidence that both phosphorylation of ELYS and its binding to VAPB are heightened during mitosis. Immunofluorescence and proximity ligation assays are used to demonstrate that the proteins co-localise specifically during anaphase and at the non-core regions of segregating chromosomes.

The manuscript is concluded by investigating the effect of VAPB depletion on mitosis with some evidence to suggest that transition from meta-anaphase is delayed and defects such as lagging chromosomes are observed.

Major comments

Overall, this manuscript is well written and the data presented in Figures 1-3 convincingly show the nature of the interaction between ELYS and VAPB. Clearly the proteins interact via FFAT motifs and this interaction appears to be enhanced during mitosis. However, the work as is, relies heavily on peptide binding assays and would benefit from additional experiments to further support the results. The authors need to more clearly show that this specific phosphorylation happens during mitosis, they may have this data but it is not clearly explained. In addition, the data that VAPB-ELYS interaction contributes to temporal progression of mitosis (as per the title) is not sufficiently clear. VAPB silencing appears to have some impact on mitosis but this is not the same thing. So this section needs to be strengthened before this statement can be made.

The authors claim that the study "suggests an active role of VAPB in recruiting membrane fragments to chromatin and in the biogenesis of a novel nuclear envelope during mitosis". Given the data presented in Figures 4 and 5, this appears to be rather speculative with little evidence to support it, so data should be provided or this statement toned down. Currently, without additional supporting data the authors may wish to revise the overarching conclusions of the study and change the title.

Specific points.

Peptide pull down assays clearly show which FFAT-like motifs are important in facilitating binding. The co-immunoprecipitation systems used in Figure 2 also provide useful information on the interaction in a cell context. The authors should combine these findings by introducing full length ELYS mutants with altered FFAT-like motifs into their stably expressing GFP-VAPB HeLa cell line and then performing Co-IPs to help identify which FFAT motif/s drive the mitotic interaction. Other mutants of ELYS harbouring either phosphomimetic or phospho-resistant residues may also be introduced to further investigate mechanisms of the molecular switch in a cellular environment to support the work currently done with peptides alone. This is an obvious gap in the work which, based on the other data the authors have shown, should presumably be straightforward and would also lead directly into the next major point.

• Whilst silencing VAPB does appear to delay mitosis, no reference is made to ELYS throughout Figure 5 nor as part of its associated discussion. Given that VAPB has more than 250 proposed binding partners, the observed aberration of mitotic progression could result from a huge number of indirect processes. Further work is needed to link the experiment specifically to the VAPB-ELYS interaction and not just loss of VAPB. We would suggest generating a complementation system where ELYS is either knocked out or silenced and then wild-type ELYS and an ELYS FFAT mutant (which cannot interact with VAPB),and/or a phospho mutant (whose interaction cannot be regulated during mitosis) are introduced. Then the observed effects can be better attributed to the VAPB-ELYS interaction and not just loss of VAPB.
• The immunofluorescence and PLA results in Figure 4 could be strengthened by including other ER markers. This would show that co-localisation of ELYS at the non-core region is specific to VAPB protein, not any ER protein or rather than an artefact of the ER being pushed out of the organelle exclusion zone during mitosis and therefore 'bunching' at the periphery of the nuclear envelope. It would be worthwhile repeating these experiments with candidates such as VAPA, other ER membrane proteins or at least GFP-KDEL, to make this phenomenon more convincing. As part of this the authors should ideally generate a complemented ELYS KO (see point above) to avoid the residual activity attributed to endogenous background in the PLA Figure 4E.
• Authors should clarify if the phosphorylation events (in particular S1314) only occur or are increased during mitosis. This may be data they have from the MS experiment in Figure 3 or it could also be shown using a phospho-antibody (although this can be challenging if a suitable antibody cannot be made).
• The authors should clarify why they need to do these semi in-vitro assays with purified GST-VAPB-MSP on beads and then lysates added and not just a standard co-IP. If this is simply signal intensity due to a very small proportion of VAPB binding to ELYS then this is fine but this should be stated and it should be made clear that ELYS is not a major binding partner - most of VAPB is on the ER. Otherwise, this is misleading.

I estimate that the suggested alterations above would incur approximately 3-6 months of additional experimental work, depending on if KO cell lines were required.

Minor comments

• To show that the observed interactions and potential role of VAPB-ELYS interaction is universal it would be useful to have at least a subset of experiments also shown in another cell line or system - this is now also a requirement for some journals.
• Consider re-wording the title of the manuscript to better reflect the data presented within the study. Alternatively, provide further evidence that VAPB-ELYS interactions directly affect temporal progression of mitosis to validate this claim, as discussed above.
• Quantification of blots in Figure 2A could allow measurement of relative binding affinities between VAPB-ELYS throughout the cell cycle. The same could be applied to the effect of phosphorylation on binding affinity in Figure 2D.
• The cells used are never clearly mentioned in the text - I assume this is always in HeLa but this should be added in all cases for clarity
• Page 8: "As shown in Fig. 2A,a large proportion of GFP-VAPB was precipitated under our experimental conditions." - I don't understand how this is shown in this figure as the non-bound fraction is not shown?
• Please provide some controls to demonstrate the extent to which the samples used are asyn, G1/M or M.
• Page 9 - why are Phos-tag gels not shown as this would make this result more convincing?
• Figure 3A - I find the SDS-PAGE gel confusing. Why not show the whole gel and why is the band size apparently reduced in the mitotic fraction when previously it was increased (by phosphorylation)? It would also be useful to see if there were any other band shifts.
• "FFAT-2 of ELYS is regulated by phosphorylation" The way you have setup the experiment leads the reader to think you are going to show which sites are differentially phosphorylated in mitosis, but then this is not the case - so there seems no purpose to doing the experiment this way. If you used TMT MS approach you would be able to potentially quantify the change in phosphorylation at the FFAT motif sites in mitosis. Otherwise what is the purpose of using these 2 samples, mitotic and AS?
• For all of the antibodies used, in particular for the PLA, please provide evidence of validation of the antibodies.
• Just a minor point to consider - In the methods for your lysis buffer you use 400mM NaCl - might this slightly reduce the VAPB-FFAT interaction? Worth considering reducing this?
• "The rather small difference observed between the wild-type and the mutant protein observed in this experiment probably results from the presence of endogenous VAPB in the stable cell lines, which could form dimers with the exogeneous HA-tagged versions." If this is the case then please demonstrate that this is happening, or use the KO approach in the major points above.
• "we now show that the proteins can indeed interact with each other, without the need for additional bridging factors (Figs. 1 and 3)." You show that the peptides can bind - but this is not the same thing as the peptide in the full context of the protein - so this should be toned down or removed.
• "Remarkably, this region is highly conserved between species, suggesting that it is important for protein functions (data not shown)". Please show the alignments so the reader can judge for themselves. It is conserved in ALL species and the phosphosites are also conserved??
• "In our experiments, knockdown of VAPA alone did not lead to a delay in mitosis (data not shown). " Why not show this data - as this is a very interesting and potentially important observation? Also add the validation of knockdown of VAPA.
• I find the end to the discussion to the paper rather abrupt. It would be interesting to discuss further how VAPB, but not apparently VAPA reaches the INM and if so why this function is required of an ER adaptor and not another more obvious adaptor protein. In short - why would VAPB be performing this role?

Referees cross-commenting

I agree with the comments of the other reviewers, and they are very much in line with my own review. We all seem convinced that VAPB binds ELYS via a pFFAT, and that this interaction is enhanced during mitosois. However the role of this interaction in mitotic progression remains unclear and based on this data should not be claimed in the title or discussion of the paper.

Significance

Overall, if the manuscript could be improved with the suggested changes, then this could be a considerable conceptual advance in how we understand the VAP proteins, showing functions beyond those as an ER adaptor. This would be significant for the field.

In the context of the existing literature the work does not advance our knowledge of FFAT-VAP interactions, this has already been shown, but it would give a nice example of how this can be regulated during mitosis and how VAP can contribute beyond just as an ER adaptor at membrane contact sites.

There would be a wide audience in the cell biology field and more widely as mutations in VAPB cause a form of ALS, and many people are working in this area.

My field of expertise is in organelle cell biology and membrane contact sites.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

This work uses state-of-the art cell imaging and careful image quantification to study early secretory pathway dynamics during budding yeast gametogenesis. The work builds on previous findings of roles for Sec16 in ER exit site formation, Sec-body formation during specific developmental stages, and for Vps13 in lipid homeostasis. The work appears to be carefully conducted and is nicely presented.

Much of the early work - here relating to meiosis in budding yeast, reflects that from studies of mitosis in other systems. This work therefore adds nicely to our understanding of membrane dynamics during cell division. Figures 1 and 2 are useful additions to the literature in this regard. I would have preferred images to be presented in magenta/green rather than red/green for wider accessibility.

The advance is therefore not conceptual but functional. It would, in my view, be unfair to dismiss this as incremental.

Major

My major comment here relates to the FRAP data - the difference in half-life of recovery is clear but there are also substantial differences in the immobile fraction. It is vital that this is expanded on and discussed - it has direct relevance to the conclusions relating to the ongoing functional activity of ERES and the comparison to Sec bodies. Is it not possible that the immobile element here is a functional "reserve" like with Sec bodies? This might be consistent with multiple pools of COPII proteins acting at different stages to maintain then promote secretory activity. Some consideration needs to be given to expanding this and possibly including these data in the main figure. Further analysis and controls should also be included here, other COPII proteins and other markers that one might predict would not alter dynamics in these conditions.

The key mechanistic advance in the manuscript relates to the role of Gip1 with clearly defined outcomes showing its role in ERES remodelling in nascent spores, regeneration of the Golgi and PSM elongation. The context of this part of the work is most important. Specifically, the comparison to VPS13 mutant needs to be expanded on and better explained. The analysis in Fig.4 needs a clearer explanation within the figure of how localization to the PSM is defined. The detail in the methods is also insufficient and the "custom R script" should be published with the work (or on a publicly accessible repository such as Git/Zenodo etc).

The development of this work with the delta-sep mutant gives useful insight and the analysis of Sec16 does indeed support a model where this is an early marker for the process. Despite the link to septins no direct analysis of YSW1 is included (which suppresses the sporulation defect in gip1 ts alleles.

Minor:

Figure 3 introduces new data on reticulons and their impact on ER membrane shape. Again, this reflects findings in other systems but does not add much to the specific narrative of this story but is useful for those in the field. Similar to this, the data on Sec4 are of interest to the specialist but add little to the overall story.

The discussion is quite lengthy and speculative dealing with themes and ideas that are not addressed directly by this work. My comments on the FRAP data relate directly to the models in Figure 8 and this discussion. Given the emphasis on nutrient starvation in the final discussion more detail is needed on the relative experimental conditions used here and in flies/mammals.

Some relevant prior work should also be cited e.g. on the role of Sec16 on exit from mitosis PMID: 21045114, other work relating to gip1 mutants (PMID: 19465564).

Consider presenting images as magenta/green.

Referees cross-commenting

I agree broadly with the other reviewers comments.

While there are elements that could be developed much further. I am not familiar with the role of GIP1 in transcriptional regulation - is this from work in yeast or solely Arabidopsis (is GIP1 here - GBF1 interacting protein, a true equivalent?).

I agree with the comments on the need for further - and well explained - statistical analyses.

Significance

Overall, the work is solid and adds nicely to our understanding. It is likely to be of most interest to a quite specialist audience. The work on PSM formation and spore formation is a clear advance with significant sections of the work being of interest to a wider audience working on early secretory pathway (notably COPII dynamics). Deeper mechanistic insight is missing but non-trivial. More depth would be added by studying further deletion mutants but I am not entirely convinced that this will rapidly advance the field further than this current presentation.

My expertise is in early secretory pathway function.

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Referee #2

Evidence, reproducibility and clarity

Suda et al. conducted an in-depth investigation of gametogenesis in budding yeast, focusing on the formation of the prospore membrane (PSM) through membrane trafficking rearrangement. They made an interesting observation that the number of endoplasmic reticulum exit sites (ERES) fluctuates during PSM formation, transitioning from decreasing to increasing. The study proposed that ERES regeneration, facilitated by protein phosphatase-1 and its specific subunit, Gip1, plays a crucial role in this process. However, the mechanism by which Gip1 regulates ERES numbers remains unclear, and the authors primarily used Gip1 mutants that may affect transcriptional regulation through Glc7, raising concerns about potential indirect effects. It is essential for the authors to experimentally validate the key mechanisms underlying their findings to strengthen their conclusions.

Major Points:

1. The conclusion that the loss of ERES causes a transient stall in membrane trafficking and leads to Golgi loss is based on the phenotype of GIP1 KO and SED4 KO cells. However, how Gip1 regulates ERES numbers remains unclear. The authors need to define whether Gip1 mediates this regulation through Glc7 dephosphorylation or via transcriptional regulation.
2. The claim of ERES fluctuation during gametogenesis lacks statistical validation (Figure 1D). Since the difference is very small, the authors should perform a statistical analysis to determine if there is a significant difference in ERES numbers during different stages of gametogenesis.
3. The conclusion regarding the loss and regeneration of the Golgi apparatus is based on qualitative observations of Mnn9, Sys1, and Sec7 signals. A quantitative analysis is necessary to strengthen these findings, as some cells may retain these signals despite their disappearance in representative images.
4. Based on phenotypic similarity between GIP1 KO and SED4 KO cells, they concluded that Gip1 regulates the ERES number required for PSM expansion. They demonstrated that the number of ERES and Golgi dramatically decreased in GIP1 KO cells. The authors also need to do this experiment in SED4 KO cells? Since Sed4 affects ER function in general, the authors should demonstrate that SED4 KO cells are appropriate to make a conclusion about ERES regulation and PSM expansion.

Referees cross-commenting

Consistent with the other two reviewers, we feel our comments should be addressed prior to publication of this manuscript.

Significance

Overall, the study presents a high-quality imaging analysis of gametogenesis in budding yeast. However, the authors should experimentally validate the mechanisms underlying ERES regulation by Gip1 and conduct rigorous statistical analyses to support their observations. Additionally, since gametogenesis and Gip1 are yeast specific, the significance of this study might be limited.

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Referee #1

Evidence, reproducibility and clarity

Summary: Yeast gametogenesis requires major membrane reorganization to ensure proper spore formation for survival during starvation, but many questions remain for how this process occurs. This current manuscript by Suda et al. uses fluorescence live imaging to visualize the dynamics of secretory pathway components which are critical for contributing lipids to the prospore membrane (PSM) in the developing spore. The authors find that ER exit sites (ERES) initially decrease and then gradually increase, coinciding with their appearance inside the PSM, suggesting that new lipids for PSM growth are trafficked through the secretory pathway from within the PSM. By screening through known genetic mutants that cause meiosis defects, the authors identify Gip1p, an adaptor for protein phosphatase 1, as a master upstream factor for prospore-associated ERES formation. Interestingly, the authors additionally identify a non-essential component of ERES in vegetative cells, sed4, to be important for sporulation and ERES PSM localization.

Overall, the biological question is interesting and the imaging quality is appropriate. The general conclusion that ERES foci localize inside developing PSMs in a gip1- and sed4- dependent manner is supported by the data. However, the manuscript is purely descriptive; not much molecular insight is gleaned into how secretory pathway components localize to the inside of the PSM, nor is it clear how important this localization is in contributing new lipids to the PSM. Additionally, there are multiple points within the writing and presentation of the results, some specified below, that require clarification; more details in the quantifications also need to be included to ascertain whether the data robustly support the authors' current conclusions.

Major comments:

• The loss of gip1 affects multiple aspects of sporulation and leads to an early termination of spore formation, giving little insight into how ERES are established inside the PSM. The most intriguing result is that loss of sed4, a nonessential paralog of the membrane-bound Sar1 GEF, leads not only to sporulation defects, but also affects the localization of Sec13/ERES to the spores. Given that some spores still form in the sed4 cells, more experiments detailing ERES and golgi localization within the forming spores could be done. Does the golgi no longer localize within the PSM in sed4 cells? Is there are a PSM size difference between those that do and do not have ERES foci in this genetic background? Where does Sed4 localize in gip1 cells?
• While Vps13 is introduced as an additional pathway for supplying lipids, this manuscript does not address the relative contribution of vesicular trafficking versus vps13 lipid transport in PSM formation. Where does Vsp13 localize in the sed4 cells? Are they enriched around/within those spores that do form?
• The clarity of writing in the results and discussion section could be improved, some of which I point out below. The discussion could also be shortened.

Specific comments:

• For all quantifications, more information is necessary, including sample sizes, mean/median values, and number of biological replicates. It may be helpful to include these values in a separate supplemental table.
• Relatedly, for 1D, 3C, and 4C graphs: It is difficult to judge whether the changes of ERES # are significantly different across the various genetic backgrounds as displayed, and given the large spread and small changes, statistical analyses are required to make such conclusions. Could the authors comment on why there is a minor yet noticeable percent of cells with very high ERES numbers?
• To make specific conclusions that ERES 'regenerate' inside PSMs, more detailed quantifications of ERES foci # inside the developing prospores should be included, with appropriate statistical analysis.
• Figure 6A, B: The localization of Glc7 does not look different to me, as claimed. The septin-like cable localization presumably occurs during elongation, as seen in 6A, and gip1D cells do not enter this phase, then it should be expected that there would be no septin-like localization. In 6B, the lower panels seem to show mature, closed PSMs; can the authors label the phases and explain why this is?
• Figure 8, Top panels, indicate the purple coverage is PSM. It is unclear why the authors suddenly say that ERES are 'transiently inactivated' here and in the discussion to describe the lower # of ERES foci, whereas the appearance of PSM-associated ERES foci is considered 'regenerated' (which implies de novo assembly). In general, from the present data, one cannot conclude inactivation vs. formation/regeneration, so some caution in terminology is warranted.

Minor comments:

• A schematic showing the different stages of meiosis and of PSM formation would be useful.
• Scale bar dimensions are missing for most of the figures.
• It may be helpful to use an alternate color combination for merged images (i.e. cyan/yellow, red/cyan, or magenta/green), to accommodate colorblind readers.
• For Figure 1C, authors should show orthogonal views along the z plane at timepoint 8 to show that ERES foci are indeed inside the PSM.
• Figure 1E legend, define closed arrowhead; additionally, include an explanation in the main text of what the Spo20(51-91) marker is.
• For kymograph displays (Figures 1E, 5A, 7E), please include time points in each frame.
• Figure 4D, 4E legend, the multiple terms describing PSM circumference length is confusing: 'cell perimeter, 'PSM perimeter' and 'PSM length'. Please choose one term and describe this fully in the text.
• Fig 5: The images in Fig 5 are dim and the gain should be adjusted accordingly. Figure 5B, is this an intensity trace of one punctum, or punctae from multiple cells as implied in the text?
• More details, not just references, in methods for sporulation induction and image analysis should be included.

Referees cross-commenting

I also agree that our comments should be addressed prior to publication. Of the existing data, the need for further statistical analysis is a high priority.

Significance

The data and conclusions presented here are for a specialized, basic audience interested in yeast meiosis, especially focused on how membranes and the secretory pathway are remodeled during this process. The paper's results have some implications for the reproductive aging field, but this area is not directly investigated in this current manuscript. The paper uses mostly established organelle markers and gene mutants previously known to be involved. The finding of Sed4's involvement in sporulation is, to my knowledge, novel and intriguing.

Reviewer Expertise: organelle morphology, the secretory pathway, protein aggregation, stress responses, aging, fluorescence microscopy, yeast, C. elegans, mammalian cells, biochemistry

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Reply to the reviewers

I - General criticisms

Reviewer #1: My main criticism is unfortunately inherent to the approach: comparative studies are absolutely critical, but they can only provide a very sparse sampling of diversity. Fortunately, thanks to high-throughput sequencing, bioinformatic analyses can now be performed on a large number of species, but experimental validation is typically restricted to two or three species. The consequence of this for the present manuscript is that while the functional conservation of the Gwl site is convincingly shown, the exact mechanisms responsible for the reduced effect of PKA phosphorylation remain relatively vaguely defined. Indeed, in their Discussion the authors list a number of experimental approaches to address this - but I understand that these would all involve substantial efforts to address. In particular, testing chimeric constructs around the consensus PKA site and from multiple species could be very informative.

We completely agree with the reviewer that comparative approaches are critical to understanding biological mechanisms, and are excited by the increasing possibilities to perform not only sequence and descriptive comparisons but functional studies across a range of emerging model organisms. We hope that more and more researchers in cell and molecular biology will profit from experimental tools and techniques now available in such species, and to pioneer new ones. Of course, and he/she rightly points out, conclusions are currently limited by the number of species studied, but comparisons between two judiciously chosen species can already be very informative. Thus, in our study, the use of Xenopus and Clytia allowed us to make significant progress towards our main objective of understanding the cAMP-PKA paradox in the control of oocyte maturation; specifically by showing both that PKA phosphorylation of Clytia ARPP19 is lower in efficiency and that the phosphorylated protein has a lower effect on oocyte maturation than the Xenopus protein. As the reviewer points out, unravelling the exact mechanisms underlying these differences will require a large amount of additional work and is beyond the scope of the current study. Actually, we have embarked on several series of experiments to this end using some of the approaches listed in the Discussion. Specifically, we are testing the biochemical and functional properties of chimeric constructs containing the consensus PKA site from various species. This is a substantial undertaking which will require one to two years to complete, but is already giving some very interesting findings.

Reviewer #1: The figures and text could be slightly condensed down to about 6 figures.

We have reduced the number of figure panels but we prefer to maintain the number of figures, because the experimental data presented in them is essential to the interpretation of our results and the overall conclusions of the article. If the journal editor would like us to reduce the number of figures, we could do this by displacing Figure 4 and some panels of other figures (to then fuse some of them) to supplementary material, but this would be a pity.

____________II - Abstract

As recommended by Reviewer #2, we have reworked the Abstract to make it more accessible to new readers, attempting to bring out more clearly and simply the main results and conclusions of the study. We correspondingly simplified and shortened the title of the article. Changes: Page 2.

____________III- Introduction points

Reviewer #2: I believe that it would be interesting to include some time-references when introducing the prophase arrest of Clytia and Xenopus oocytes. How long is prophase arrest in Xenopus compared to Clytia or other organisms? How can this affect the prophase arrest mechanisms? It seems that the prophase arrest in Xenopus oocytes is found to be significantly more prolonged compared to Clytia and various other organisms, and also meiotic maturation proceeds much more rapidly in Clytia than in Xenopus. This should be indicated in the introduction with a short introduction of why, and not others, were these species chosen for this study.

Differences in timing of oocyte prophase arrest and in maturation kinetics across animals are indeed highly relevant in relation to the underlying biochemical mechanisms. Unfortunately, not enough information is currently available concerning the duration of the successive phases of oocyte prophase arrest across species to make any meaningful correlations with PKA regulation of maturation initiation. We have nevertheless expanded the Introduction to cover this issue as follows:

• We start the introduction by mentioning how the length of the prophase arrest varies across species. Changes: Page 3, lines 5-11.
• We have added examples of species which likely have similar durations of prophase arrest but show cAMP-stimulated vs cAMP-inhibited release. Changes: Page 4, lines 28-35.
• We have specified the temporal differences in meiotic maturation in Xenopus (3-7 hrs) and Clytia (10-15 min). Changes: Page 5, lines 32-33.

Reviewer #2: why, and not others, were these species [Xenopus, Clytia] chosen for this study. A brief justification is included in lines 1-page 5 "..a laboratory model hydrozoan species well suited to oogenesis studies", but it does not explain why this and not other hydrozoan species like Hydra, that has also been used for meiosis studies.

As requested by Reviewer #2, fuller details are now included about the advantages of Clytia compared to other hydrozoan species, citing several articles and recent reviews here and also in the Discussion. Changes: Page 5, lines 21-32 & 37-39.

Hydra is a classic cnidarian experimental species and has proved an extremely useful model for regeneration and body patterning, but is not suitable for experimental studies on oocyte maturation because spawning is hard to control and fully-grown oocytes cannot easily be obtained, manipulated or observed. In contrast many hydromedusae (including Clytia, Cytaeis, and Cladonema) have daily dark/light induced spawning and accessible gonads, so provide great material for studying oogenesis and maturation. Of these, Clytia has currently by far the most advanced molecular and experimental tools.

Reviewer #2: The proteins MAPK is not introduced properly, as it is first mentioned in the results section in line 12. Given the importance of the results provided with it, it should be presented in the introduction prior to the results section.

As requested by Reviewer #2, the involvement of MAPK activation during Xenopus oocyte meiotic maturation is now introduced, explaining how its phosphorylation serves as a marker of Cdk1 activation. Changes: Page 5, lines 1-5.

Reviewer #2: These sentences need a more elaborate explanation: Page 4 Lines 16-17 "... no role for cAMP has been detected in meiotic resumption, which is mediated by distinct signaling pathways" Which pathways?

We now give the example of the well-characterized pathway Gbg-PI3K pathway for oocyte maturation initiation in the starfish. Changes: Page 4, lines 1-15.

Reviewer #2: Page 4 line 34-39. Introduction indicates that the phosphorylation of ARPP19 on S67 by Gwl is a poorly understood molecular signaling cascade (line 34). However, the positive role of ARPP19 on Cdk1 activation, through the S67 phosphorylation by Gwl, appears to be widespread across all eukaryotic mitotic and meiotic divisions studied (lines 36-37). These two sentences seem a little contradictory. If the general pathway has been identified but the signaling cascade is still not well described, please indicate that in a clearer way.

We apologise that the wording we used was not clear and implied that the mechanisms of PP2A inhibition by Gwl-phosphorylated ARPP19 were poorly understood. On the contrary, they are very well studied. The part that remains mysterious concerns the upstream mechanisms. We have reworded the paragraph to make this point unambiguous. Changes: Page 5, lines 1-8.

____________IV - Results

Reviewer #2: The text of the results is generally well described; however, all the sections start with a long introductory paragraph. I believe this facilitates the contextualization of the experiments, but please try to summarize when possible. For example, in page 5 lines 12-25, or page 7 lines 30-37, are all introduction information.

As requested by Reviewer #2, we have shortened or removed the introductory passages of the Results section paragraphs, which were redundant with the information given in the introduction. We did not restrict to the two examples cited by the reviewer, but have shortened all the Results passages that repeat information already provided in the Introduction. Changes: Page 7, lines 3-4 & 14-16 & 36-37 - Page 8, lines 12-15 - Page 8, lines 37-40 & Page 9, lines 1-6.

Reviewer #2: Page 7, Lines 14-19 present a general conclusion of the findings explained in lines 20-27. I think these results are important and they should be explained better, in my opinion they are slightly poorly described.

We have followed the reviewer's recommendation. The explanation of the experiments and the results are more detailed and the paragraph ends with a general conclusion which came too early in the previous version. Changes: Page 8, lines 22-24 & 32-34.

Reviewer #2: Page 8, lines 16-17: "It was not possible to increase injection volumes or protein concentrations without inducing high levels of non-specific toxicity". What are the non-specific toxicity effects? How was this addressed? What fundaments this conclusion?

Clytia oocytes are relatively fragile. Sensitivity of oocytes to injection varies between batches, while in general increasing injection volumes or protein concentrations increases the levels of lysis observed. We do not know exactly what causes this but lysis can happen either immediately following injection or during the natural exaggerated cortical contraction waves that accompany meiotic maturation, suggesting that it relates to mechanical trauma. We have expanded this paragraph and the legend of Fig. 3C to explain these injection experiments more fully in the text and to clarify these issues. Changes: Page 9, lines 16-29 - Page 32, lines 34-41 & Page 33, lines 1-11 - Supplementary Table 1.

Same paragraph: Lines 25-27 of page 8. Text reads, "These results suggest that PP2A inhibition is not sufficient to induce oocyte maturation in Clytia, although we cannot rule out that the quantity of OA or Gwl thiophosphorylated ARPP proteins delivered was insufficient to trigger GVBD.". Please provide evidence if higher concentrations of OA or Gwl were tested to state this conclusion.

As explained above, we could not increase the concentrations of ARPP19 protein beyond 4mg/ml. It is important to note that at the same concentration, both Clytia and Xenopus proteins induce activation of Cdk1 and GVBD in the Xenopus oocyte.

Concerning OA, it is well documented in many systems including Xenopus, starfish and mouse oocytes as well as mammalian cell cultures, that high concentrations lead to cell lysis/apoptosis as a result of a massive deregulation of protein phosphorylation (Goris et al, 1989; Rime & Ozon, 1990; Alexandre et al, 1991; Boe et al, 1991; Gehringer, 2004; Maton el al, 2005; Kleppe et al, 2015). Specific tests in Xenopus oocytes, have shown that injecting 50 nl of 1 or 2 mM OA specifically inhibits PP2A, while injecting 5 mM also targets PP1 and higher OA concentrations inhibit all phosphatases. For these reasons, we did not increase OA concentrations over 2 mM. When injected in Xenopus oocyte at 1 or 2 mM, OA induces Cdk1 activation, GVBD but then the cell dies because PP2A has multiple substrates essential for cell life. When injected at 2 mM in Clytia oocytes, OA does not induce Cdk1 activation nor GVBD but promotes cell lysis. This supports the conclusion that 2 mM OA is sufficient to inhibit PP2A (and possibly other phosphatases) but that PP2A inhibition is not sufficient to induce oocyte maturation in Clytia.

We have reworded the relevant text to make these points clearer. The previous statement that “we cannot rule out that the quantity of OA or Gwl thiophosphorylated ARPP proteins delivered was insufficient to trigger GVBD” has been removed because it was unnecessarily cautious in the context of the literature cited above, as now fully explained_._ Changes: Page 9, lines 31-35 - Page 32, lines 34-41 & Page 33, lines 1-11 - Supplementary Table 1.

References: Alexandre et al, 1991, doi: 10.1242/dev.112.4.971; Boe et al, 1991, doi: 10.1016/0014-4827(91)90523-w; Gehringer, 2004, doi: 10.1016/s0014-5793(03)01447-9; Goris et al, 1989, doi: 10.1016/0014-5793(89)80198-x; Kleppe et al, 2015, doi: 10.3390/md13106505; Maton el al, 2005, doi: 10.1242/jcs.02370; Rime & Ozon, 1990, doi: 10.1016/0012-1606(90)90106-s

Reviewer #2: Lines 12-13: the sentence "This in vitro assay thus places S81 as the sole residue in ClyARPP19 for phosphorylation by PKA." is overstated. As not all residues had been tested, please indicate that "it is likely that" or "among the residues tested", in contrast to "the sole residue in ClyARPP19".

We realise that we had not explained clearly enough how the thiophosphorylation assay works. In this assay, γ-S-ATP will be incorporated into any amino acid of ClyARPP19 phosphorylatable by PKA. The observed thiophosphorylation of the wild-type protein, demonstrates that one or more residues are phosphorylated by PKA. This thiophosphorylation was completely prevented by mutation of a single residue, S81. This experiment thus shows that S81 is entirely responsible for phosphorylation by PKA in this assay. We have rewritten this section more clearly. Changes: Page 10, lines 18-28.

____________V - Figures and text related to the figures

Figure 1A

Reviewer #2: Why is mouse not included in Figure 1A? Although it might be very similar to human, given that mouse is the species that is most commonly use as a mammalian model, I believe it could be included. However, this is optional upon decision by the authors.

We have replaced the human sequence in Figure 1A with the mouse sequence as suggested. The sequences of each of the mouse and human ENSA/ARPP19 proteins are indeed virtually identical across mammals. Changes: Fig. 1A.

Figure 1C

Reviewer #2: There should be a better explanation in the text of the results sections for the image included in in Fig1 C. Note that Clytia is not a commonly used species, therefore images should be properly explained for general readers. Please indicate in the text that ClyARPP19 mRNA is expressed in previtellogenic oocytes and not in vitellogenic, plus any additional information needed to understand the image. In addition, the detection of ARPP19 in the nerve rings is intriguing. This is mentioned in the discussion section, any idea of its function there? Please include some additional information or additional references, if they exist.

We have expanded the explanations of Fig. 1C in the text and in the figure legend. We have also added cartoons to the figure to help readers understand the organisation of the Clytia jellyfish and gonad. As now explained, ClyARPP19 mRNA is detected in oocytes at all stages, but the signal is much stronger in pre-vitellogenic oocytes because all cytoplasmic components including mRNAs are significantly diluted by high quantity of yolk proteins as the oocytes grow to full size. Changes: page 7, line 40 & page 8, lines 1-9 - Fig. 1C - Legend page 31, lines 19-31.

Nothing is known about the function of ARPP19 in the Clytia nervous system. The only data linking ARPP19 and the nervous system concerns mammalian ARPP16, an alternatively spliced variant of ARPP19. ARPP16 is highly expressed in medium spiny neurons of the striatum and likely mediates effects of the neurotransmitter dopamine acting on these cells (Andrade et al, 2017; Musante et al, 2017). This point is included in the Discussion in relation to the hypothesis that PKA phosphorylation of ARPP19 proteins in animals first arose in the nervous system and only later was coopted into oocyte maturation initiation. Changes: page 16, lines 12-13 & 17-20 - page 19, lines 6-9.

Figure 2A

Reviewer #1: Fig. 2A (and similar plots in subsequent figures): is it really necessary to cut the x axis? Would it be possible to indicate the number of oocytes for each experiment (maybe in the legend in brackets)?

As requested by reviewer #1, the x-axis is no longer cut. The number of oocytes for each experiment is now provided in the legend of Fig. 2A and in similar plots of Fig. 5A and 5D. Changes: Fig. 2A - Legends page 31, lines 37-38 (Fig. 2A), page 33, line 25 (Fig. 5A) - page 33, line 34 (Fig. 5D).

Figure 2D-E (as well as Figure 6C-D and Figure 8B-C)

Reviewer #1: Fig. 2D (and all similar plots below): I am lacking the discrete data points that were measured. Without these it is impossible to evaluate the fits. The half-times shown in 2E are somewhat redundant, and the information could be combined on a single plot.

We added all the data points to the concerned plots: 2D, 6C and 8B. As recommended by reviewer #1, we combined on a single plot the phosphorylation levels and the half-times. 2D-E => 2D, 6C-D => 6C and 8B-C => 8B. Changes: Figs 2D, 6C and 8B - Legends page 32, lines 9-14 (Fig. 2D), page 34, lines 24-30 (Fig. 6C) - page 35, lines 13-18 (Fig. 8B).

Figure 3A and 3B

Reviewer #1: Fig. 3: why is the blot for PKA substrates cut into 3 pieces? It would be clearer to show the entire membrane.

In western blot experiments using Clytia oocytes, the amount of material was limited so the membranes were cut into three parts. The central part was incubated sequentially in distinct antibodies. We finally incubated all three parts of the membrane with the anti-phospho-PKA substrate antibody to reveal the full spectrum of proteins recognized by this antibody. The 3 pieces in Fig. 3A therefore together make up the same original membrane. We had separated them on the figure to make it clear that the membrane had been cut. In the new presentation, the 3 pieces are shown next to each other, making it clear that all the membrane is present, with dotted lines indicating the cut zone as explained in the legend. Changes: Fig. 3A and 3B - Legend page 32, lines 22-25 (Fig. 3A), lines 30-33 (Fig. 3B) - Page 24, lines 3-6 (Methods).

Figure 3C

Reviewer #2: Fig. 3C needs a better explanation in the text. The way these graphs are presented is somehow confusing. The meaning of the dots is not self-explanted in the graph, and it seems that each experiment was done independently but then the complete set of results is presented. Legend says that "each dot represents one experiment" but this is difficult to read as in every analysis the figure also indicates the average and the total number of oocytes. If authors wish so, they can keep the figure as it is, but then please explain this graph better in the text, and please include statistical analysis. These results are very robust, but a comparison between the number of oocytes that go through spontaneous GVBD of lysis in the different conditions will benefit their understanding.

This figure is intended to provide an overview of all the Clytia oocyte injection experiments that we performed, for which full details are given in Supplementary Table 1. Since these experiments were not equivalent in terms of exact timing and types of observation (or films) made and oocyte sensitivity to injection -as ascertained by buffer injections-, it is not justified to make statistical comparisons between groups. We apologise that the presentation was misleading in this respect and hope that the new version is easier to understand. We removed from the figure the average percentage of maturation for each condition between experiments to avoid any misunderstanding of the nature of the data, and rather represent the values of each experiment independently. We also now explain the data included in the figure fully in the text and figure legend. Changes: Page 9, lines 16-39 - Fig. 3C and Supplementary Table 1 - Legend page 32, lines 34-41 & page 33, lines 1-11.

Reviewer #2: Also, please provide in the text a plausible explanation for the cause of oocyte lysis for all experimental conditions (Fig 3C). Given that in the control experiments with buffer this effect is also observed in some oocytes, please explain if this is caused by a mechanical disruption of the oocyte during the injection. In contrast, okadaic acid induces the lysis in all the 14/14 oocytes analyzed, is this due also to the mechanical approach? Or is there other reason more related to the PP2A inhibition? Please explain.

These points are treated above in the response to this reviewer concerning the Results section.

Figure 5

Reviewer #2: In Figure 5 D-F, cited in page 9 lines 35-35. Can you provide an explanation of why the time course of meiosis resumption was delayed?

The binding partners/effectors of XeARPP19-S109D that are involved in maintaining the prophase arrest have not yet been identified. The most probable explanation of the delay in meiotic maturation induced by ClyARPP19-S109D is that Clytia protein recognizes less efficiently these unknown ARPP19 effectors that mediate the prophase arrest. As a result, maturation would be delayed, but not blocked. This explanation was provided in the Discussion (page 17, lines 14-17) and is now mentioned in the Results section. Changes: page 11, lines 16-19.

____________VI - Discussion

Reviewer #2: Although it presents highly interesting suggestions, discussion may border on being overly speculative, especially from line 37 of page 15 till the end.

We agree and have reduced the speculation in this part of the discussion, in particular regrouping and reformulating ideas about evolutionary scenarios in a single paragraph. Changes: page 17, lines 37-41 - page 18, lines 1-41 - page 19, lines 1-18.

SUMMARY - Point by point responses to individual reviewers’ comments in their order of appearance.

Reviewer 1

• The figures and text could be slightly condensed down to about 6 figures.

We have reduced the number of figure panels but we prefer to maintain the number of figures, because the experimental data presented in them is essential to the interpretation of our results and the overall conclusions of the article. If the journal editor would like us to reduce the number of figures, we could do this by displacing Figure 4 and some panels of other figures (to then fuse some of them) to supplementary material, but this would be a pity.

• The exact mechanisms responsible for the reduced effect of PKA phosphorylation remain relatively vaguely defined. Indeed, in their Discussion the authors list a number of experimental approaches to address this - but I understand that these would all involve substantial efforts to address. In particular, testing chimeric constructs around the consensus PKA site and from multiple species could be very informative.

As the reviewer points out, unravelling these exact mechanisms will require a large amount of additional work and is beyond the scope of the current study.

• 2A (and similar plots in subsequent figures): is it really necessary to cut the x axis? Would it be possible to indicate the number of oocytes for each experiment (maybe in the legend in brackets)?

Fig. 2A has been changed in line with the reviewer's request (as well as similar plots in Fig. 5A and 5D). Changes: Fig. 2A - Legends page 31, lines 37-38 (Fig. 2A), page 33, line 25 (Fig. 5A) - page 33, line 34 (Fig. 5D).

• 2D (and all similar plots below): I am lacking the discrete data points that were measured. Without these it is impossible to evaluate the fits. The half-times shown in 2E are somewhat redundant, and the information could be combined on a single plot.

Fig. 2D has been changed in line with the reviewer's request (as well as similar plots in Figs 6C-D and 8B-C). Changes: Fig. 2D, 6C and 8B - Legends page 32, lines 9-14 (Fig. 2D), page 34, lines 24-30 (Fig. 6C) - page 35, lines 13-18 (Fig. 8B).

• 3: why is the blot for PKA substrates cut into 3 pieces? It would be clearer to show the entire membrane.

In western blot experiments using Clytia oocytes, the amount of material was limited so the membranes were cut into three parts. The central part was incubated sequentially in distinct antibodies. We finally incubated all three parts of the membrane with the anti-phospho-PKA substrate antibody to reveal the full spectrum of proteins recognized by this antibody. The 3 pieces in Fig. 3A therefore together make up the same original membrane. In the new presentation, the 3 pieces are shown next to each other, making it clear that all the membrane is present, with dotted lines indicating the cut zone as explained in the legend. Changes: Fig. 3A and 3B - Legend page 32, lines 22-25 (Fig. 3A), lines 30-33 (Fig. 3B) - Page 24, lines 3-6 (Methods).

Reviewer 2

• Abstract needs to be simplified if wants to reach a broader range of readers.

We have reworked the Abstract to make it more accessible to new readers. Changes: Page 2.

• It would be interesting to include some time-references when introducing the prophase arrest of Clytia and Xenopus oocytes. This should be indicated in the introduction with a short introduction of why, and not others, were these species chosen for this study.

We have expanded the Introduction to cover the issue of time-references. Fuller details are now included about the advantages of Clytia compared to other hydrozoan species. Changes: Page 3, lines 5-11, page 4, lines 28-35, page 5, lines 32-33, page 5, lines 21-32 & 37-39.

• The proteins MAPK is not introduced properly, as it is first mentioned in the results section.

The involvement of MAPK activation during Xenopus oocyte meiotic maturation is now introduced. Changes: Page 5, lines 1-5.

• Page 4 Lines 16-17 "... no role for cAMP has been detected in meiotic resumption, which is mediated by distinct signaling pathways" Which pathways?

We now give the example of the well-characterized pathway Gbg-PI3K pathway for oocyte maturation in starfish, also mentioning that in many species the pathways are still unknown. Changes: Page 4, lines 1-15.

• Page 4 line 34-39. Introduction indicates that the phosphorylation of ARPP19 on S67 by Gwl is a poorly understood molecular signaling cascade (line 34). However, the positive role of ARPP19 on Cdk1 activation, through the S67 phosphorylation by Gwl, appears to be widespread across all eukaryotic mitotic and meiotic divisions studied (lines 36-37). These two sentences seem a little contradictory.

The mechanisms of PP2A inhibition by Gwl-phosphorylated ARPP19 are very well studied. The part that remains mysterious concerns the upstream mechanisms. We have reworded the paragraph to make this point unambiguous. Changes: Page 5, lines 1-8.

• Why is mouse not included in Figure 1A?

We have replaced the human sequence in Figure 1A with the mouse sequence. Changes: Fig. 1A.

• 1C: There should be a better explanation in the text of the results sections for the image included in in Fig1 C. Please indicate in the text that ClyARPP19 mRNA is expressed in previtellogenic oocytes and not in vitellogenic.

We have expanded the explanations of Fig. 1C in the text. We have also added cartoons to the figure to help readers understand the organisation of the Clytia jellyfish and gonad. As now explained, ClyARPP19 mRNA is detected in oocytes at all stages, but the signal is much stronger in pre-vitellogenic oocytes because all cytoplasmic components are significantly diluted by high quantity of yolk proteins. Changes: page 7, line 40 & page 8, lines 1-9 - Fig. 1C - Legend page 31, lines 19-31.

• In addition, the detection of ARPP19 in the nerve rings is intriguing. Any idea of its function there?

The only data linking ARPP19 and the nervous system concerns a mammalian variant of ARPP19 that is highly expressed in the striatum. This point is included in the Discussion_. Changes: page 16, lines 12-13 & 17-20 - page 19, lines 6-9._

• Figure 3C. The way these graphs are presented is somehow confusing. If authors wish so, they can keep the figure as it is, but then Also, please provide in the text a plausible explanation for the cause of oocyte lysis for all experimental conditions. please explain this graph better in the text, and please include statistical analysis.

This figure is intended to provide an overview of all the Clytia oocyte injection experiments, for which full details are given in Supplementary Table 1. We have modified the figure and now clarified this fully in the text and figure legend. Clytia oocytes are relatively fragile. Sensitivity of oocytes to injection varies between batches, while in general increasing injection volumes or protein concentrations increases the levels of lysis observed. We do not know exactly what causes this but it probably relates to mechanical trauma. We now explain these injection experiments more fully in the text. Changes: Page 9, lines 16-39 - Fig. 3C and Supplementary Table 1 - Legend page 32, lines 34-41 & page 33, lines 1-11.

• In Figure 5 D-F, cited in page 9 lines 35-35. Can you provide an explanation of why the time course of meiosis resumption was delayed?

The most probable explanation is that Clytia protein recognizes less efficiently the unknown ARPP19 effectors that mediate the prophase arrest in Xenopus. This explanation is provided in the Results section. Changes: page 11, line 16-19.

• All the sections start with a long introductory paragraph. I believe this facilitates the contextualization of the experiments, but please try to summarize when possible.

As requested, we have shortened or removed the introductory passages of the Results section paragraphs, which were redundant with the information given in the introduction. Changes: Page 7, lines 3-4 & 14-16 & 36-37 - Page 8, lines 12-15 - Page 8, lines 37-40 & Page 9, lines 1-6.

• Page 7, Lines 14-19 present a general conclusion of the findings explained in lines 20-27. I think these results are important and they should be explained better, in my opinion they are slightly poorly described.

The explanation of the experiments and the results are now more detailed and the paragraph ends with a general conclusion which came too early in the previous version. Changes: Page 8, lines 22-24 & 32-34.

• Page 8, lines 16-17: "It was not possible to increase injection volumes or protein concentrations without inducing high levels of non-specific toxicity". What are the non-specific toxicity effects? How was this addressed? What fundaments this conclusion?

As explained above, increasing injection volumes or protein concentrations increases the levels of lysis observed due probably to mechanical trauma. But it is important to note that at the same concentration, both Clytia and Xenopus proteins induce activation of Cdk1 and GVBD in the Xenopus oocyte. Changes: Page 9, lines 16-29 - Page 32, lines 34-41 & Page 33, lines 1-11 - Supplementary Table 1.

• Lines 25-27 of page 8. "These results suggest that PP2A inhibition is not sufficient to induce oocyte maturation in Clytia, although we cannot rule out that the quantity of OA or Gwl thiophosphorylated ARPP proteins delivered was insufficient to trigger GVBD." Please provide evidence if higher concentrations of OA or Gwl were tested to state this conclusion.

High OA concentrations lead to cell lysis/apoptosis as a result of a massive deregulation of protein phosphorylation. For these reasons, we cannot increase OA concentrations over 2 µM. When injected in Xenopus oocyte at 1 or 2 µM, OA induces Cdk1 activation, but then the cell dies because PP2A has multiple substrates essential for cell life. When injected at 2 µM in Clytia oocytes, OA does not induce Cdk1 activation but promotes cell lysis. This supports the conclusion that 2 µM OA is sufficient to inhibit PP2A but that PP2A inhibition is not sufficient to induce oocyte maturation in Clytia. We have reworded the relevant text. Changes: Page 9, lines 31-35 - Page 32, lines 34-41 & Page 33, lines 1-11 - Supplementary Table 1.

• Lines 12-13: the sentence "This in vitro assay thus places S81 as the sole residue in ClyARPP19 for phosphorylation by PKA." is overstated. As not all residues had been tested, please indicate that "it is likely that" or "among the residues tested", in contrast to "the sole residue in ClyARPP19".

The observed thiophosphorylation of the wild-type protein demonstrates that one or more residues are phosphorylated by PKA. This thiophosphorylation was completely prevented by mutation of a single residue, S81. This experiment thus shows that S81 is entirely responsible for phosphorylation by PKA in this assay. We have rewritten this section more clearly. Changes: Page 10, lines 18-28.

• Some parts of the discussion are a bit speculative.

We have reduced the speculation in this part of the discussion, in particular regrouping and reformulating ideas about evolutionary scenarios into a single paragraph. Changes: page 17, lines 37-41 - page 18, lines 1-41 - page 19, lines 1-18.

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Referee #2

Evidence, reproducibility and clarity

Summary of the main findings of the study.

This work presents very interesting data about the maintenance and release of the prophase arrest of oocytes during sexual reproduction. Authors approach some of the remaining questions about oocyte maturation in animals by taking a comparative approach between two species (Clytia and Xenopus) that use opposing cAMP/PKA signaling pathways to trigger oocyte maturation. To do it they focused on phosphorylation characteristics and function of the regulatory protein ARPP19 from the amphibian Xenopus and its orthologue in the hydrozoan Clytia. Results suggest that the low capacity of Clytia ARPP19 to be phosphorylated by PKA. Moreover, Clytia ARPP19 is inherently a poorer PKA substrate than Xenopus ARPP109 both in vivo and in vitro, despite the presence of a functional PKA site. In addition, the absence of functional interactors mediating its negative effects on Cdk1 activation may provide a double security allowing induction of meiosis resumption in Clytia by elevated PKA activity despite the presence of ARPP19, while additional and yet unidentified mechanisms ensure the Clytia oocyte prophase arrest.

Minor comments: read detailed review below. Figure 1 and Figure 3 need a better explanation of the results. Abstract needs to be simplified if wants to reach a broader range of readers. Some parts of the discussion are a bit speculative.

Overall, this work used a robust set of molecular experiments that strongly support the conclusions of the study.

Significance

Strengths and limitations of this work:

The primary strength of this work lies in its innovative use of two distinct species and the integration of molecular experiments to extract conclusions from their different signaling pathways. The well-designed and executed experiments, particularly those of figures 5-9, contribute to an elaborated exploration of the topic, elucidating the underlying mechanisms with clarity. The explanation of each experiment in the results section further adds to the clarity and depth of the study.

The abstract requires improvement, particularly from lines 10 to 21, as it becomes fully understood only after reading the entire manuscript. To make the work more accessible to new readers, it would be good to present the abstract in a more approachable manner. Figures 1C and 3C need a better explanation in the text. Additionally, some sentences would benefit from citations or further clarification in the results or discussion section. Although is presents highly interesting suggestions, discussion may border on being overly speculative, especially from line 37 of page 15 till the end.

Detailed review

Introduction:<br /> I believe that it would be interesting to include some time-references when introducing the prophase arrest of Clytia and Xenopus oocytes. How long is prophase arrest in Xenopus compared to Clytia or other organisms? How can this affect the prophase arrest mechanisms? It seems that the prophase arrest in Xenopus oocytes is found to be significantly more prolonged compared to Clytia and various other organisms, and also meiotic maturation proceeds much more rapidly in Clytia than in Xenopus. This should be indicated in the introduction with a short introduction of why, and not others, were these species chosen for this study. A brief justification is included in lines 1-page 5 "..a laboratory model hydrozoan species well suited to oogenesis studies", but it does not explain why this and not other hydrozoan species like Hydra, that has also been used for meiosis studies.<br /> The proteins MAPK is not introduced properly, as it is first mentioned in the results section in line 12. Given the importance of the results provided with it, it should be presented in the introduction prior to the results section.

These sentences need a more elaborate explanation:<br /> Page 4 Lines 16-17 "... no role for cAMP has been detected in meiotic resumption, which is mediated by distinct signaling pathways" Which pathways?

Page 4 line 34-39. Introduction indicates that the phosphorylation of ARPP19 on S67 by Gwl is a poorly understood molecular signaling cascade (line 34). However, the positive role of ARPP19 on Cdk1 activation, through the S67 phosphorylation by Gwl, appears to be widespread across all eukaryotic mitotic and meiotic divisions studied (lines 36-37). These two sentences seem a little contradictory. If the general pathway has been identified but the signaling cascade is still not well described, please indicate that in a clearer way.

Results section: this review will first comment the figures, and then the text.<br /> Figure 1<br /> Why is mouse not included in Figure 1A? Although it might be very similar to human, given that mouse is the species that is most commonly use as a mammalian model, I believe it could be included. However, this is optional upon decision by the authors.<br /> There should be a better explanation in the text of the results sections for the image included in in Fig1 C. Note that Clytia is not a commonly used species, therefore images should be properly explained for general readers. Please indicate in the text that ClyARPP19 mRNA is expressed in previtellogenic oocytes and not in vitellogenic, plus any additional information needed to understand the image. In addition, the detection of ARPP19 in the nerve rings is intriguing. This is mentioned in the discussion section, any idea of its function there? Please include some additional information or additional references, if they exist.

Figure 3<br /> The way these graphs are presented is somehow confusing. The meaning of the dots is not self-explanted in the graph, and it seems that each experiment was done independently but then the complete set of results is presented. Legend says that "each dot represents one experiment" but this is difficult to read as in every analysis the figure also indicates the average and the total number of oocytes. If authors wish so, they can keep the figure as it is, but then please explain this graph better in the text, and please include statistical analysis. These results are very robust, but a comparison between the number of oocytes that go through spontaneous GVBD of lysis in the different conditions will benefit their understanding.

Also, please provide in the text a plausible explanation for the cause of oocyte lysis for all experimental conditions (Fig 3C). Given that in the control experiments with buffer this effect is also observed in some oocytes, please explain if this is caused by a mechanical disruption of the oocyte during the injection. In contrast, okadaic acid induces the lysis in all the 14/14 oocytes analyzed, is this due also to the mechanical approach? Or is there other reason more related to the PP2A inhibition? Please explain.

Figure 5<br /> In Figure 5 D-F, cited in page 9 lines 35-35. Can you provide an explanation of why the time course of meiosis resumption was delayed?

• The text of the results is generally well described; however, all the sections start with a long introductory paragraph. I believe this facilitates the contextualization of the experiments, but please try to summarize when possible. For example, in page 5 lines 12-25, or page 7 lines 30-37, are all introduction information.<br /> Page 7, Lines 14-19 present a general conclusion of the findings explained in lines 20-27. I think these results are important and they should be explained better, in my opinion they are slightly poorly described.

Page 8, lines 16-17: "It was not possible to increase injection volumes or protein concentrations without inducing high levels of non-specific toxicity". What are the non-specific toxicity effects? How was this addressed? What fundaments this conclusion?

Lines 25-27 of page 8. Text reads, "These results suggest that PP2A inhibition is not sufficient to induce oocyte maturation in Clytia, although we cannot rule out that the quantity of OA or Gwl thiophosphorylated ARPP proteins delivered was insufficient to trigger GVBD.". Please provide evidence if higher concentrations of OA or Gwl were tested to state this conclusion.

Lines 12-13: the sentence "This in vitro assay thus places S81 as the sole residue in ClyARPP19 for phosphorylation by PKA." is overstated. As not all residues had been tested, please indicate that "it is likely that" or "among the residues tested", in contrast to "the sole residue in ClyARPP19".

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Referee #1

Evidence, reproducibility and clarity

In their present manuscript Meneau and coworkers investigate the evolutionary conserved functions of ARPP19 in regulation of meiotic maturation of oocytes. During meiotic maturation, the maturation hormone induces a signaling cascade ultimately leading to the activation of the master regulator, cdk1-cyclin B. within this signaling network, the phosphatase PP2A prevents cdk1 activation in immature oocytes. Upon the action of the maturation hormone, ARPP19 is activated through phosphorylation by the kinase Gwl, and then functions as a potent inhibitor of PP2A, thereby contributing to cdk1 activation. Additionally, ARPP19 is subject to a second layer of regulation: a second site is phosphorylated by the kinase PKA. Interestingly, in vertebrates this cAMP/PKA pathway prevents maturation, while in many other species the same pathway has an opposite effect and cAMP/PKA is indeed sufficient to drive maturation -- referred to as the cAMP paradox.

The authors' major aim was to reveal the molecular basis of these diverse functions of ARPP19 in triggering meiotic maturation. Firstly, they show that the Gwl site is extremely well-conserved all across eukaryotes. They then functionally validate this by comparing the functions of Xenopus ARPP19 to its orthologue in the jellyfish Clytia hemisphaerica. They confirm that the jellyfish ARPP19 is phosphorylated on the conserved Gwl site in vitro and in frog and jellyfish oocytes, acting as a PP2A inhibitor and contributing to cdk1 activation. However, while this is sufficient to drive maturation in Xenopus, PP2A inhibition alone is not sufficient to trigger entry to meiosis in Clytia oocytes, indicating the existence of additional mechanisms. Secondly, they show that the PKA site exists and is phosphorylated both in Xenopus and Clytia. However, the Clytia protein appears to be a much worst substrate for PKA and other interactors, which explains why PKA-phosphorylated ARPP19 does not inhibit maturation either in jellyfish oocytes or when exogenously injected into Xenopus oocytes.

I find the manuscript well-written and easy to follow. The experiments are carefully performed, well-controlled and well-documented. The data shown on the figures fully supports the conclusions drawn -- although the figures and text could be slightly condensed down to about 6 figures. Overall, I would highly recommend the manuscript for publication.

My main criticism is unfortunately inherent to the approach: comparative studies are absolutely critical, but they can only provide a very sparse sampling of diversity. Fortunately, thanks to high-throughput sequencing, bioinformatic analyses can now be performed on a large number of species, but experimental validation is typically restricted to two or three species. The consequence of this for the present manuscript is that while the functional conservation of the Gwl site is convincingly shown, the exact mechanisms responsible for the reduced effect of PKA phosphorylation remain relatively vaguely defined. Indeed, in their Discussion the authors list a number of experimental approaches to address this - but I understand that these would all involve substantial efforts to address. In particular, testing chimeric constructs around the consensus PKA site and from multiple species could be very informative.

In addition, I would have a few small suggestions for improving the figures:

• Fig. 2A (and similar plots in subsequent figures): is it really necessary to cut the x axis? Would it be possible to indicate the number of oocytes for each experiment (maybe in the legend in brackets)?
• Fig. 2D (and all similar plots below): I am lacking the discrete data points that were measured. Without these it is impossible to evaluate the fits. The half-times shown in 2E are somewhat redundant, and the information could be combined on a single plot.
• Fig. 3: why is the blot for PKA substrates cut into 3 pieces? It would be clearer to show the entire membrane.

Significance

Overall, I find this study extremely important, because it is only possible to entangle the diversity of cellular mechanisms though such comparative studies. Oocyte maturation perfectly exemplifies this issue: without doubt, oocyte maturation is a fundamental process and its detailed understanding is critical. However, researchers are often discouraged by diversity across species, which indeed complicates and hinders progress, well-reflected by the name "cAMP paradox". Combined with careful bioinformatic analyses, comparative studies can elegantly resolve such "paradoxes" through resolving the evolutionary history of molecular mechanisms.

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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 this interesting paper Bideau et al. report an antero-posterior gradient in the plasticity of tail tissues during tail regeneration in the annelid worm Platynereis dumerilii. The experiments are well designed and thoroughly quantified, the figures are of high quality.

Major comments:

The microscopic images lack scale bars. These should be added to all figures.

The authors should provide the source data for all quantifications as txt files. They should also provide as supplement representative confocal stacks for the various stainings.

The authors use LatrunculinB treatment to investigate the role of cell migration in regeneration. However, since LatB inhibits f-actin, it could also interfere with cell proliferation and other processes. The authors should check if this is the case and provide control data.

Minor comments:

Sometimes the language is a bit quite cryptic. For example, the title of Figure 4 is "Cell proliferation and migration, as well as tissue maturity modulate the plasticity of posteriorized gut progenitors through regeneration"<br /> in short: 'cell migration modulates the plasticity of progenitors' - this is just to say that inhibiting cell migration reduces regeneration

The authors should attempt to simplify the language.

Language:

"is an tremendous and essential process in animals" - not clear what 'tremendous' means here - please revise

"Those regeneration processes have been studied from a long" - for a long time

"more EdU+ cells in S1 than in S6 or S7 regardless the EdU incubation time" - regardless of the

"It showed that the gut is composed of" - The stainings showed that

"Indeed, cell labelled with a rather short EdU" - cells labelled

"tissues plays a major role on the reformation" - in the formation

The paper will be of interest to animal developmental biologists and scientists working on the plasticity of tissues during regeneration.

Referees cross-commenting

I agree with the comments made by the other reviewers. The authors need to be more clear and careful in interpreting their data. I don't think that new data are needed (unless they would like to demonstrate a 'gradient' with more positions) and the comments could be addressed by substantially rewriting the text and revising the claims.

Significance

The paper will be of interest to animal developmental biologists and scientists working on the plasticity of tissues during regeneration.

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Referee #2

Evidence, reproducibility and clarity

Bideau et al. studied the origin, plasticity and fate of the cells participating in blastema formation during posterior regeneration in the annelid Platynereis dumerilii. To label and track the fate of proliferative cells, the authors applied EdU/BrDU incorporation coupled with mRNA in situ hybridization and fluorescent beads labelling, on a wide array of regeneration assays. They also performed drug treatments to assess the role of proliferation and cell migration during posterior regeneration. Interestingly, the Authors showed that some proliferative gut cells can participate in the formation of ectodermal and mesodermal tissues during regeneration, in case of two successive posterior regeneration events, suggesting that gut cycling cells residing in a regenerating segment are more plastic than those located in a non-regenerating segment. They also suggested the existence of two different cell populations - "slowly" and "quickly" cycling cells - acting during regeneration. Overall, the experiments are well presented, and methods clearly described. The Authors concluded that posterior regeneration in Platynereis relies on a gradient of cell plasticity and cell proliferation, along the antero-posterior axis of the animal.

Major comments

Two of the main conclusions of this study are, in my opinion, not supported by the data:

As indicated in the title of the manuscript, the Authors put forward a cellular model for posterior regeneration relying on gradients of cell proliferation, cell differentiation and cell plasticity along the the antero-posterior axis of the animal. I am not convinced that the Authors have provided strong enough evidence to prove any of these gradients. They showed that there are differences between the region directly adjacent the most posterior segment and a region located more anteriorly (6 or 7 segments from the posterior end). However, by comparing only two positions, they cannot distinguish between graded or clearly regionalized contexts. To prove the existence of a gradient along the animal's antero-posterior axis, the authors would need to compare cell proliferation, cell dynamics and cell differentiation between multiple regions at increasing anterior positions, and show that their responses are indeed graded. This would represent a quite substantial amount of work. Instead, I would suggest removing the reference to a gradient in the paper entirely.

Using "short" (5h) and "long" (48h) EdU pulses, the Authors claim they have established the existence of two cell populations, namely "slowly-cycling cells" and "quickly-cycling cells" (first paragraph of the result section - pages 5/6 "We exposed uninjured worms to EdU, either for 5 or 48h to discriminate quickly-cycling cells from cells harboring a slower replication rate"). I am not convinced that the Authors provide strong enough evidence to demonstrate the existence of two such cell populations. Given that about 20% of cells incorporated EdU after 5h of exposure, that almost all of them have done so after 48h, and that only a fraction of proliferative cells are in S-phase at any given time, it is well possible that a majority of cells stained after 5h and 48h are from the same cell cycling population. To show the existence of different populations of cells, cycling at different rates, the Authors would need to compare staining after an equal EdU exposure time, following a period of chase of different duration. Without this set of experiments, I would refrain from distinguishing between several slower and faster cell cycling populations.

Minor comments

Page 1. Please correct "is an tremendous" into "is a tremendous".

Page 7. "The huge majority of the EdU+ cells colocalize with FoxA". Please provide quantification.

Page 11 "Quickly-cycling gut progenitors.... cannot give rise to neural progenitors and probably not to stem cells from the ectodermal growth zone"; Page 12 "cannot regenerate neural tissues"; Page 20 "posterior gut progenitors cannot produce nervous system or putative posterior stem cells". What the authors show in their experiments, is that labeled gut cycling cells likely do not generate neural cells or stem cells, in the assessed context. However, the Authors do not show that those cells 'cannot' do so. Please rephrase.

Page 11. "migration, through actin polymerization (LatrunculinB or LatB) widely used inhibitors". Please add a reference to justify the use of LatB as a cell migration inhibitor.

Significance

This is a thorough, well executed and interesting study on a tractable annelid regeneration model. The experiments are neatly performed and the manuscript reads well. As stated in my major comments, two of the main conclusions of the study (gradient of cell proliferation/plasticity/differentiation; identification of two types of progenitors differing in their cell cycle rates) have not been demonstrated properly and would need to be either strengthened or deleted from the manuscript. Several other findings, notably the increased plasticity of cells that recently participated in posterior regeneration (notably gut cells) are well demonstrated and of interest. Overall, this manuscript significantly advances our understanding of the cellular mechanisms that occur during posterior regeneration in Platynereis. It will be of interest to anyone working on comparative regeneration, but may be of lesser interest to researchers working outside this field.

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Referee #1

Evidence, reproducibility and clarity

Bideau et al. describe posterior regeneration in the annelid Platynereis. The authors aimed to identify patterns of proliferative cells. Pulse-chase and double labeling by EdU/BrdU was used to track cells. Finally, they attempted to reveal the identity of cycling cells and their contribution to regeneration. Platynereis is a relatively new regeneration model. Understanding the cellular source of regeneration in this annelid would be of considerable interest.

The authors performed EdU labeling of intact worms to find a posterior-anterior decreasing gradient of S-phase cells. Histological sections showed that proliferative cells are located in all tissues in the posterior-most segment, but mostly restricted to the gut epithelium in more anterior segments. Using fluorescent beads that are taken up specifically by gut epithelial cells, they show that gut epithelial cells of the intact animal contribute only to gut regeneration, i.e., they are lineage restricted. The authors also performed immunostaining and mRNA in situ hybridization experiments to better understand the tissue identity of proliferative cells.

The following are my specific comments:

1. I am not sure I understand how the authors identify slow- or fast-cycling cells. EdU gets incorporated in S-phase; the longer the incubation time the more cells will be labeled until saturation is reached. The length of the cell cycle and the number of different populations cannot be directly derived from this experiment. I think it would be fair to conclude that there are more cycling cells in posterior segments and in the gut of anterior segments but the conclusion of two distinct populations is unsupported in my opinion.
2. The Results and Discussion sections will have to be revised to address the above issue. The two supported conclusions are (1) the gradient of proliferative cells (but w/o reference to the number of distinct populations); (2) the fate-restricted nature of gut epithelial cells. The plasticity gradient is unsupported because worms can regenerate if amputated at segment #5. This suggests the presence of either resident stem cells (with broad potential or lineage-specific), cells that can dedifferentiate, or a combination of both. The authors' experiments cannot discriminate between the alternatives.
3. The text would benefit from copy editing to improve the language and making it more accessible. In its current form, it is rather difficult to read, with descriptions of experiments that are not easy to follow.
4. The figures and their legends can be improved. Re the legends, one has to read the full text to understand what each panel shows. The figures are very complex. It would already be easier if usage of A', A', A' was avoided. The figures could also be improved by direct annotation. Finally, consider simplifying the main figures and moving some material to the supplement.
5. How do the authors know that proliferative cells in the gut are "gut progenitors"? They might simply be proliferative gut epithelial cells.
6. The conclusions drawn from the drug experiments are overstated.

Referees cross-commenting

The comments made by the two other reviewers are complementary to mine. Either the authors extensively revise the text to remove unsupported conclusions or they perform additional experiments.

Significance

Little is known about the cellular basis of Platynereis posterior regeneration.

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Reply to the reviewers

We thank the Reviewers for their helpful and constructive comments. In response to these suggestions we have performed new experiments and amended the manuscript, as we describe in our detailed response below.

Reviewer #1:

1. The Reviewer notes that while our analysis of centrosome size was comprehensive, we provided no analysis of centrosomal MTs, pointing out that while centrosome size declines as the embryos enter mitosis, the ability of centrosomes to organise MTs might not. This is a good point, and we now provide an analysis of centrosomal-MT behaviour (Figure 2). We find that there is a dramatic decline in centrosomal MT fluorescence at NEB, although the pattern of centrosomal MT recruitment prior to NEB is surprisingly complex.

2. The Reviewer questions how PCM client proteins can be recruited in different ways by the same Cdk/Cyclin oscillator. We apologise for not explaining this properly. It is widely accepted that Cdk/Cyclins drive cell cycle progression, in part, by phosphorylating different substrates at different activity thresholds (e.g. Coudreuse and Nurse, Nature, 2010; Swaffer et al., Cell, 2016). Moreover, it is also clear that Cdk/Cyclins can phosphorylate the same protein at different sites at different activity thresholds (e.g. Koivomagi et al., Nature, 2011; Asafa et al., Curr. Biol., 2022; Ord et al., Nat. Struct. Mol. Biol., 2019). Thus, we hypothesise that rising Cdk/Cyclin cell cycle oscillator (CCO) activity phosphorylates multiple proteins at different times and/or at different sites to generate the complicated kinetics of centrosome growth. We now explain this point more clearly throughout the manuscript.

3. The Reviewer is puzzled as to how we conclude that Cdk/Cyclins phosphorylate Spd-2 and Cnn at all the potential Cdk/Cyclin phosphorylation sites we mutate in our study. The Reviewer is right that we cannot make this conclusion, and we did not intend to make this claim. As we now clarify (p11, para.1), although it is unclear if Cdk/Cyclins phosphorylate Spd-2 or Cnn on all, some, or none of these sites, if either protein can be phosphorylated by Cdk/Cyclins, then these mutants should not be able to be phosphorylated in this way—allowing us to address the potential significance of any such phosphorylation. We now also note that several of these sites have been shown to be phosphorylated in embryos in Mass Spectroscopy screens (Figure S6).

4. The Reviewer highlights differences in how Spd-2 and Cnn help recruit γ-tubulin to centrosomes (Figure 6). They ask for a more detailed description, and are puzzled as to how this is compatible with direct regulation by a single oscillator. We now explain our thinking on this important point in much more detail. It appears that Spd-2 helps recruit γ-tubulin throughout S-phase, while Cnn has a more prominent role in late S-phase (Figure 6). This is consistent with our overall hypothesis of CCO regulation, as we postulate that low-level CCO activity promotes the Spd-2/γ-tubulin interaction in early S-phase, while higher CCO activity promotes the Cnn/γ-tubulin interaction in late-S-phase, potentially explaining the increase in the rate of γ-tubulin (but not γ-TuRC) recruitment we observe at this point (see minor comment #1, below, for an explanation of the various γ-tubulin complexes in flies). This is consistent with recent literature showing that CCO activity promotes γ-tubulin (but not γ-TuRC) recruitment by Cnn/SPD-5 in worms and flies (Ohta et al., 2021; Tovey et al., 2021).

5. The Reviewer was not convinced by our model (Figure 8, now Figure 9), raising two major concerns. First, they were unsure how a single oscillator could generate different patterns of protein recruitment. We addressed this in point #2 and #4, above, where we explain how different thresholds of CCO activity trigger different events, so there is no expectation that we should observe steady changes in recruitment over time as CCO activity rises. Second, they questioned how modest levels of Cdk/Cyclin activity can promote recruitment, while high levels of activity can inhibit recruitment. In point #1, above, we cite several examples where such positive and negative regulation by different Cdk/Cyclin activity levels have been described. We also now explain throughout the manuscript why this hypothesis provides a plausible explanation for our results: with moderate CCO activity promoting Spd-2-dependent PCM-client recruitment in early S-phase; higher CCO activity promoting a decrease in Spd-2 recruitment in mid-late-S-phase (so centrosomal Spd-2 levels decline); and even higher levels of CCO activity leading to a decrease in the interactions between the client proteins and the Spd-2/Cnn scaffold as the embryos enter mitosis (so the client proteins are rapidly released from the centrosome).

The Reviewer also raised the important point here that our model does not explain why the mutant forms of Spd-2 and Cnn accumulate to higher levels at the start of S-phase, and not just at the end of S-phase/entry into mitosis. We apologise for not explaining this properly. The accumulation of the mutant proteins (particularly Spd-2, Figure 5C) in early-S-phase occurs because the excess mutant protein that accumulates at centrosomes in _late-_S-phase/mitosis is not removed properly from centrosomes during mitosis (presumably because there is insufficient time). Thus, centrosomes still have too much mutant Spd-2 at the start of the next S-phase. We show this in Reviewer Figure 1 (attached to this letter), which tracks Spd-2 behaviour further into mitosis, and now explain this in more detail in the text (p12, para.1).

1. The Reviewer questions how the CCO can both induce centrosome growth and also switch it off, as it is unclear how an oscillator that only phosphorylates sites to decrease centrosome binding could also promote growth. They ask if we can identify and mutate any Cdk/Cyclin sites in centrosome proteins that promote centrosome recruitment. As we now clarify, we did not intend to claim that the CCO only phosphorylates sites that decrease the centrosome binding of proteins, although we do hypothesise that such phosphorylation is important for switching off centrosome growth in mitosis. In addition, we hypothesise that moderate levels of CCO initially promote centrosome growth, and our data suggests that the CCO does this, at least in part, by promoting Polo recruitment (Figure 8). We speculate that the CCO phosphorylates specific Polo-box-binding sites in Ana1 and Spd-2, the main proteins that recruit Polo to centrioles. We agree that identifying these sites is an important next step, but it is complicated as our studies indicate that multiple sites contribute in a complex manner. Importantly, it is well established that the CCO triggers centrosome growth as cells prepare to enter mitosis, so our hypothesis that moderate levels of CCO activity initiate centrosome growth is not new or controversial.

Minor Comments

1. The reviewer asks how we explain the different incorporation profiles we observe for the different subunits of the γ-tubulin ring complex. We apologise for not discussing this point. In flies there is a “core” γ-tubulin-small complex (γ-TuSC) and a larger γ-tubulin-ring complex (γ-TuRC) that contains the Grip71, Grip75 and Grip128 subunits we analyse here (Oegema et al., JCB, 1999). The γ-TuSC functions independently of the γ-TuRC so γ-tubulin and γ-TuRC components can behave differently.

2. The Reviewer questions why we claim an “inverse-linear” relationship between S-phase length and the centrosome growth rate when the relationship is not linear (Figure 3, now Figure S3). I was originally confused by this as well but, mathematically, a linear relationship means y is proportional to x, whereas an inverse-linear relationship means y is proportional to 1/x. Thus, an inverse-linear relationship between x and y does not plot as a straight line, but rather as the curves we show on the graphs. We now explain this in text (p9, para.2).

Reviewer #2:

This Reviewer found the manuscript hard to follow, so we are very grateful that they took the time to try to understand it. We agree that the subject matter is complicated, and that our presentation was not always helpful. The Reviewer’s comments have been very useful in helping us to identify (and hopefully improve) areas of particular difficulty.

Major points:

1. The Reviewer highlights that the two experimental approaches underpinning our main conclusions are problematic: (1) Experiments with mutants of Spd-2 and Cnn that theoretically cannot be phosphorylated by Cdk/Cyclins are hard to interpret as these mutations may have other effects; (2) It is unclear whether reducing Cyclin B levels reduces peak CDK activity or simply slows the time it takes to reach peak levels. They suggest a more direct test of our model would be to analyse PCM recruitment in embryos arrested in S-phase or mitosis. (1) We agree that the mutations designed to prevent Cdk/Cyclin phosphorylation could perturb function in other ways, but this is true for any such mutation, and there are many papers that infer a function for Cdk/Cyclin phosphorylation from such experiments. Importantly, the centrosomal accumulation of the phospho-null mutants actually slightly increases compared to WT (Figure 5C and I), and we now show that the centrosomal accumulation of a phosphomimicking Spd-2-Cdk20E mutant slightly decreases (Figure S8). We now acknowledge the potential caveat of a non-specific perturbation of protein function, but feel that the reciprocal behaviour of the phospho-null and phospho-mimicking mutants somewhat mitigates this concern (p12, para.2). (2) Fortunately, and as we now clarify, it has recently been shown that reducing Cyclin levels does not reduce peak Cdk activity, but rather slows the time it takes to reach peak activity (Figure 2A, Hayden et al., Curr. Biol., 2022). Thus, the cyclin half-dose experiments provide an excellent alternative test of our hypothesis as they show that the WT proteins can exhibit similar behaviour to the mutants if the rate of Cdk/Cyclin activation is slowed. We feel the evidence supporting our hypothesis is strong enough that it warrants serious consideration.

The suggestion to look at PCM recruitment in embryos arrested in either S-phase or M-phase is a good one, but these experiments produce complicated data. In M-phase arrested embryos, for example, Cnn levels continue to rise (see Figure 1G, Conduit et al., Dev. Cell, 2014), but the other PCM proteins do not (unpublished); in S-phase arrested embryos (arrested by mitotic cyclin depletion) centrosomes continue to duplicate, but now do so asynchronously, greatly complicating the analysis (McCleland and O’Farrell, Curr. Biol.., 2008; Aydogan et al., Cell, 2020). The centrosomes that don’t duplicate, however, reach a constant steady-state size (where the rate of centrosome protein addition is balanced by the rate of loss). These observations are consistent with our recent mathematical modelling of mitotic PCM assembly (Wong et al., 2022) if we additionally account for cell cycle regulation (which was not considered in our original model). We believe such analyses are beyond the scope of the current paper and we plan to publish a second paper incorporating our new hypothesis into our mathematical modelling.

1. The Reviewer questions whether our methods accurately measure centrosomal protein accumulation, pointing out that γ-tubulin and Grip128 occupy different centrosomal areas—which should not be possible if they are part of the same complex. They suspect that our use of different transgenes with different promotors could explain these differences. As we should have described (see point #1 in our response to the minor comments of Reviewer #1), γ-tubulin exists in two complexes in flies, only one of which contains Grip128, so γ-tubulin and Grip128 exhibit different localisations. Moreover, as we now show (Figure S2), using different promotors does not seem to make a difference to overall recruitment kinetics. Thus, we are confident that our methods measure centrosome protein recruitment dynamics accurately.

2. The Reviewer is concerned that our measurements of centrosome size based on fluorescence intensity (Figure 1) and centrosomal area (Figure S1) do not always match. They suggest a potential reason for this is that proteins are not uniformly distributed within centrosomes, and this may impact our ability to measure protein accumulation based on 2D projections (noting, for example, that Polo and Spd-2 are concentrated at centrioles and in the PCM, potentially explaining the different shape of their growth curves compared to the client proteins). When the centrosome-fluorescence-intensity and centrosome-area recruitment profiles of a protein do not match, the average “centrosome-density” of that protein must be changing over time. In some cases, we understand why density changes. Cnn, for example, stops flaring outwards on the centrosomal MTs during mitosis so its centrosomal area decreases even as its fluorescence intensity increases (leading to an increase in its centrosomal-density). We agree (and now discuss—p19, para.3) that the prominent accumulation of Spd-2 and Polo at centrioles could help to explain why Spd-2 and Polo accumulation dynamics differ from the client proteins.

Other points:

1. The Reviewer suggests it would be good to know how much Polo at the centrosome is active. We agree, but although commercial antibodies against PLK1 phosphorylated in its activation loop work in cultured fly cells, we cannot get them to work in embryos. Moreover, the recruitment of Polo/PLK1 to its site of action by its Polo-Box Domain is sufficient to partially activate the kinase independently of phosphorylation (Xu et al., NSMB, 2013). Thus, it seems likely that all the Polo/PLK1 recruited to centrosomes will be at least partially activated, even if it is not necessarily phosphorylated on its activation loop.

2. The Reviewer asks if it is clear that less Spd-2 and Cnn are recruited to centrosomes in the half gene-dosage embryos. We apologise for not mentioning that this is indeed the case. We showed this previously for Cnn (Conduit et al., Curr. Biol., 2010) and we now state that this is also the case for Spd-2. We do not show the Spd-2 data as we plan to publish a comprehensive dose-response curve of Spd-2 (and Cnn) recruitment in our next modelling paper.

3. Would it not be relevant to examine Polo ½ dosage embryos? We do have this data (Reviewer Figure 2), attached to this letter, but it is quite complicated to interpret (as we explain in the legend). We feel it would be more appropriate to include this in our next modelling paper where we can properly explain the behaviours we observe. Publishing this data here would distract from our main message without changing any of our conclusions.

4. The Reviewer asks why the non-phosphorylatable Spd-2 protein is also present at higher levels on centrosomes at the start of S-phase (not just the end of S-phase). This was also raised by Reviewer #1 (point #5), so please see the second paragraph of our response there.

Minor/Discussion Points:

1. We thank the Reviewer for highlighting that absolute and relative centrosome size control are different things and we have amended the manuscript accordingly.

2. The Reviewer questions whether it is accurate to describe Spd-2 and Polo as scaffold proteins, noting that only Cnn has been shown to have scaffolding properties. There is strong evidence that Spd-2 has Cnn-independent scaffolding properties in flies (e.g. Conduit et al., eLife, 2014), but this is a fair point for Polo. We think it is justified to separate Polo from other client proteins as Polo is essential for scaffold assembly, whereas other client proteins are not. We now define our scaffold/client terminology to avoid confusion (p4, para.3).

3. The Reviewer highlights several points related to differences in recruitment kinetics (also touched on in points #2 and #3, above), noting we don’t discuss properly the idea of two different modes of PCM recruitment. These are all good points, largely addressed in our response to points #2 and #3, above. We now discuss much more prominently the two different modes of client protein recruitment throughout the manuscript.

4. As we now clarify, in all our experiments we use centrosome separation and nuclear envelope breakdown (NEB) to define the start and end of S-phase, respectively.

5. The Reviewer quotes the landmark Woodruff paper (Cell, 2017) as showing that the ability to concentrate client proteins (including ZYG-9, the worm homologue of Msps) is an intrinsic property of the PCM scaffold, so how do we explain that Msps departs prior to NEB while Cnn continues to accumulate? It is indeed a striking observation of our study that all PCM client proteins (not just Msps) start to leave the centrosome prior to NEB, even as Cnn levels continue to accumulate. Our hypothesis is that this ‘leaving’ event is triggered by a threshold level of Cdk/Cyclin activity—explaining why these client proteins all start to leave the PCM at the same time (just prior to NEB) irrespective of nuclear cycle length. This is not incompatible with the Woodruff paper, which did not attempt to reconstitute any potential regulation by Cdk/Cyclins in their in vitro studies.

6. The Reviewer questions why Spd-2 that cannot be phosphorylated by Cdk/Cyclins (Spd-2-Cdk20A) accumulates abnormally at centrosomes in late S-phase, yet γ-tubulin (which is recruited by Spd-2) seems to leave centrosomes more slowly in the presence of the mutant protein. As we now explain more clearly, there is no contradiction here. Spd-2-Cdk20A accumulates to abnormally high levels in late-S-phase/early mitosis (Figure 5C), and this reduces the γ-tubulin dissociation rate, as we would predict (Figure 7B, right most graph). It does not “prevent” dissociation, however, (as the Reviewer seems to suggest it should?), but this is probably because these experiments have to be performed in the presence of large amounts of the WT Spd-2 (Figure 5A).

7. The referencing error has been corrected.

8. The Reviewer asks why in Figure 1 not all of the centrosome proteins could be followed for the full time period (as we mention in the legend, but do not explain). There are different reasons for different proteins: (1) Polo cannot be followed in mitosis as it binds to the kinetochores, making it impossible to accurately track centrosomes (so the data for mitosis is missing for Polo); (2) Cnn exhibits extensive flaring at the end of mitosis/early S-phase (Megraw et al., JCS, 1999), so we cannot track individual separating centrosomes labelled with NG-Cnn in early S-phase until they have moved sufficiently far-apart (so the early S-phase time-points are missing for Cnn); (3) In addition, several of the client proteins bind to the mitotic spindle, so although we can still track and measure the centrosomes in late mitosis in the graphs, we don’t show pictures of these late mitosis centrosomes in the montage in Figure 1A as the images look a bit odd. We now explain these reasons in the Materials and Methods.

9. We now indicate that nuclear cycle 12 (NC12) is being analysed in Figures 4-8.

10. The reviewer questions why we don’t show the decrease rate for γ-tubulin in Figure 6 (the Spd-2 and Cnn half-dose experiments), when we do show it in Figure 7 (the Spd-2 and Cnn Cdk-mutant experiments), suspecting that it is slowed in both cases. The reviewer is correct and we now show this data for both sets of experiments.

11. We have corrected the labelling error in Figure S1.

12. The Reviewer suggest moving some of the data from the main Figures, and the entirety of Figures 2 and 3 to the Supplemental Information. We understand this point, and agree that the amount of data presented in Figures 1-3 is somewhat overwhelming. We have played around with the Figures a lot—in particular trying to show a few examples of the data and moving the rest to Supplementary—but it is hard to pick a “typical” example, and the power of comparing the behaviour of so many different centrosome proteins is somewhat lost. We have tidied up several Figures and, as a compromise, we keep Figure 2 (now Figure 3) in the main text, but have moved Figure 3 to Supplementary (now Figure S5).

13. The Reviewer suggests that we should repeat the analysis of Spd-2, Polo and Cnn dynamics that we show here, as we already presented this data in a previous publication (Wong et al., EMBO. J, 2022). We understand this point, but feel this would be a less accurate comparison, as essentially all of the data shown in Figure 1 was obtained several years ago during a contiguous ~6month period. Since then, the lasers and software on our microscope system have been updated, so it would probably be less fair of a comparison to obtain new data for a subset of these proteins (and it seems overkill to perform the entire analysis again). We clearly state that this data has been presented previously, so we hope the Reviewer will agree that it is acceptable to present it again here so readers can more easily compare the data.

Reviewer #3:

This Reviewer is broadly supportive of the manuscript, but to publish in a prestigious journal they think additional experimental evidence will be required to support our hypothesis.

The Reviewer notes that our only evidence that Cdk/Cyclins directly phosphorylate Spd-2 comes from our analysis of the Spd-2-Cdk20A mutant, as the effect of reducing Cyclin B dosage on WT Spd-2 behaviour is very modest. They request that we analyse the behaviour of a Spd-2-Cdk20E phospho-mimicking mutant. The effect of halving the dose of Cyclin B on Spd-2 behaviour is modest, but this is what we would predict as all we are doing in this experiment is slowing S-phase by ~15%, so Spd-2 should accumulate at centrosomes for a slightly longer time and to a slightly higher level (as we observe, Figure 5E). A great advantage of the early fly embryo system is that we can compare the behaviour of many hundreds of centrosomes, so even subtle differences like this are usually meaningful. To illustrate this point, we have now repeated the Spd-2 analysis in WT and CycB1/2 embryos (but now using a CRISPR/Cas9 Spd-2-NG knock-in line) and we see the same subtle differences (Figure S9). In addition, as requested, we have now analysed the behaviour of a Spd-2Cdk20E mutant protein using an mRNA injection assay (as it would have taken too long to generate and test new transgenic lines). In this assay we injected embryos with mRNA encoding either WT Spd-2-GFP, Spd-2-Cdk20A-GFP or Spd-2-Cdk20E-GFP. The mRNA is quickly translated, and we computationally measured the fluorescence intensity of the centrosomes in mid-S-phase (i.e. at the Spd-2 peak) (Figure S8). This analysis confirms that Cdk20A accumulates to slightly higher levels, and reveals that Cdk20E accumulates to slightly lower levels, than the WT protein. Together, these new experiments strongly support our original conclusions.

The Reviewer notes that we propose that the CCO initially promotes centrosome growth by stimulating Polo recruitment to centrosomes, but states that we only provide indirect evidence for this by showing that centrosomal Polo levels are strongly reduced in Cyclin B half-dose embryos. They suggest we determine Spd-2 levels in Polo half-dose embryos, and/or the centrosome levels of mutant forms of Spd-2 that cannot be phosphorylated by Polo. We believe the Cyclin B half-dose experiment provide direct support for our hypothesis that Cdk/Cyclin activity influences Polo recruitment (Figure 8), although, clearly, we have not identified the mechanism. We do, however, suggest a plausible mechanism: Ana1 and Spd-2 are largely responsible for recruiting Polo to centrosomes, and we have previously shown that several of the potential phosphorylation sites in these proteins that help recruit Polo to centrosomes are Cdk/Cyclin or Polo phosphorylation sites (Alvarez-Rodrigo et al., eLife, 2020 and JCS, 2021; Wong et al., EMBO J., 2022). We are currently testing this hypothesis, but progress is slow as it is clear that multiple sites in both proteins can influence this process.

As the Reviewer requests, we have now also examined how Spd-2 and Cnn behave in Polo half-dose embryos (Reviewer Figure 2, attached to this letter). As we describe in the Figure legend, this data is informative, but is complicated. With relatively minor, but mechanistically important, tweaks to our previous mathematical modelling we can explain these behaviours, but introducing such a significant mathematical modelling element would be beyond the scope of this paper. As described above, these findings will form the basis of a follow-up paper that is more mathematically oriented.

It is a great idea to look at mutant forms of Spd-2 that cannot be phosphorylated by Polo, but the consensus Polo phosphorylation site (N/D/E-X-S, with the N/D/E at -2 and the S at 0 being preferences, rather than a strict rule) is less well-defined than the consensus Cdk/Cyclin phosphorylation site (where the Pro at -1 is essentially invariant). Thus, we cannot accurately predict which sites would need to be mutated to generate such a mutant.

The Reviewer requests that we analyse the behaviour of TACC in embryos expressing the Spd-2-Cdk20A and Cnn-Cdk6A (as we do in Figure 7 for γ-tubulin). This is a reasonable request, but we prefer not to show this data as we have recently identified an interesting interaction between TACC, Spd-2 and Aurora A that will be the subject of another paper we hope to submit shortly. This data is hard to interpret without explaining these interactions properly, which is beyond the scope of the current manuscript.

We hope the Reviewers will agree that these changes have improved the manuscript substantially, and that it is now suitable for publication. We would like to thank them again for taking the time to read this rather complicated paper so thoroughly.

We look forward to hearing from you.