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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.

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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.

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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.

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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.

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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.

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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.

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

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Referee #3

Evidence, reproducibility and clarity

Summary: 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.

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

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.

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

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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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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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.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors investigated growth control of PCM at the mitotic centrosomes in late stages of the Drosophila syncytial embryos. They observed that mitotic centrosomes reach to the correct sizes through 13 rounds of nuclear division by reciprocally slowing their growth rate and increasing their growth period. They assumed that the Cdk/Cyclin cell cycle oscillator (CCO) is a main controller, based on their previous works (Aydogan et al., 2018, 2020; 2022). They determined the recruitment dynamics of the key mitotic PCM scaffolding proteins (Spd-2, Polo and Cnn) and PCM-client proteins (γ-tubulin, Msps, TACC, GFP, Grip75, Grip128 and Aurora A) in living embryos, and proposed that moderate levels of the CCO activity promote centrosome growth by stimulating Polo recruitment to centrosomes, while higher levels of activity subsequently inhibit centrosome growth by phosphorylating centrosome proteins, such as Spd-2, to decrease their centrosome recruitment and/or maintenance as the embryos enter mitosis.

Experiments were cleverly designed and carefully executed. The results are nicely presented, the manuscript is clearly written, and their proposal draws a strong attention. However, in order to publish the manuscript in a prestigious journal, the authors may provide additional experimental evidence to support their proposal.

• It is very significant that the centrosome levels of Spd-2-Cdk20A-NG is stronger than Spd-2-NG throughout the cell cycle (Figure 5B,C). However, this is only an experimental evidence to support that Cdk/Cyclins directly phosphorylate Spd-2 in the run-up to mitosis to help reduce Spd-2's centrosome recruitment and/or maintenance. As the authors confessed, recruitment of Spd-2-NG to the centrosomes in CycB1/2 embryos (Figure 5D,E) may be moderate or not significant at least in this reviewer's eyes. It is worth to perform the same experiments with a phospho-mimetic Spd2-Cdk20E-NG mutant.
• The authors proposed that moderate levels of CCO activity promote centrosome growth by stimulating Polo recruitment to centrosomes. They provided an indirect evidence that centrosome levels of polo were strongly reduced in CycB1/2 embryos (Figure 4E,F). It is worth to determine the centrosome levels of Spd-2 in the Polo1/2 embryos and/or the centrosome levels of Polo phospho-resistant Spd-2 (Spd-2-Polo#A-NG).
• TACC may be an ideal PCM-client protein, apart from its importance in spindle formation in comparison to γ-tubulin (Figure 4C,D). Therefore, it is worth to perform the Figure 7 experiments with TACC.

Significance

Experiments were cleverly designed and carefully executed. The results are nicely presented, the manuscript is clearly written, and their proposal draws a strong attention. However, in order to publish the manuscript in a prestigious journal, the authors may provide additional experimental evidence to support their proposal.

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Referee #2

Evidence, reproducibility and clarity

Control of organelle size has been an active field of research for many years for a large variety of cellular structures and in a range of experimental models. Here, Jordan Raff and colleagues examine the mechanisms underlying centrosome (PCM) size control in Drosophila syncytial embryos, building on their previous work (Wong, EMBOJ 2022) to propose a role for CDK in both promoting (at intermediate levels) and inhibiting (at high levels) PCM expansion.

I found this a difficult manuscript to review, not only because the subject matter is complicated, but so is the writing. Having read and re-read the manuscript some clarity eventually emerges, but it shouldn't be that inaccessible. As for the authors' model I find it intriguing, but not fully supported by the data currently presented.

Major points

1. Central to the authors' model is the proposed dual function of Cdk (or CCO in the authors' terminology) in both promoting and inhibiting centrosomal protein accumulation. This the authors test by reducing the gene dosage of cyclin B and using putatively non-phosphorylatable versions of Spd-2 and Cnn. Both approaches to me appear quite problematic. The latter perturbation is hard to interpret given that whether these are indeed Cdk phosphosites that they have mutated is unknown and there are plenty of other possibilities how this might perturb protein function, as the authors' lack of success doing the same for gamma-tubulin illustrates. The former perturbation also lacks context. Does reducing cyclin B gene dosage reduce peak CDK activity or does it merely take longer to reach the same maximum, as appears to occur naturally as the cell cycle slows between embryonic cycles 11 and 13 (Edgar, Genes Dev 1994)? A more direct way to test their model would be to arrest the embryo in S phase (which in their model should lead to indefinite growth) or mitosis using suitable drugs/genetic perturbations. Is this not feasible in the fly system?
2. Similarly critical is that centrosomal protein accumulation is accurately measured. I am not entirely convinced that this is so. If one takes their estimations of centrosome size at face value, then the space occupied by gamma-tubulin (slightly over 1 µm2 peak area according to Fig. S3) is significantly smaller than that occupied by Grip128 (4µm2). How is this possible if these form part of the same gamma-tubulin complex? This likely reflects the fact that the dynamics of many proteins is being assessed using transgenic reporters under the control of heterologous regulatory sequences (not all of which are fully functional, eg Polo), which could result in wildly inappropriate centrosomal protein levels. It may then not be a coincidence that the centrosomal domain for Grip128 (endogenously tagged) is larger than that for gamma-tubulin (transgene).
3. Another concern is that centrosome size and integated signal intensity do not always match, as demonstrated by Grip71 (increasing as expected during centrosome maturation in cycle 13 based on fluorescence intensity but not area
4. compare Figs. 1B and S1). A potential reason for this is that proteins are not uniformly distributed within centrosomes. For example, Polo and Spd2 are highly concentrated at centrioles. This impacts the ability to accurately measure protein accumulation based on 2D projections. Such inaccuracies likely will not affect estimation of when peak protein accumulation occurs, but may explain apparent differences in the kinetics of recruitment/dissociation of different components. Thus, the differences in the shape of the PCM client growth curves compared to those of Polo and Spd-2 (p6) may simply reflect the centriole concentration of the latter.

Other points<br /> 4. In C. elegans much of Polo at centrosomes is apparently inactive, particularly in the vicinity of centrioles (Cabral, Dev Cell 2019). Knowing whether this is also the case in flies would seem like important information to have, particularly when comparing signal intensities across the cell cycle.<br /> 5. Is it clear that there is less Spd2/Cnn at centrosomes in Spd-2/Cnn 1/2 gene dosage embryos, as the authors assume?<br /> 6. Would it not be relevant to also examine Polo 1/2 dosage embryos?<br /> 7. Based on the authors model, Cdk phosphorylation first drives PCM accumulation, then at higher levels inhibits. Yet, their non-phosphorylatable Spd2 mutant exhibits not only a delayed decline in centrosomal levels, but also higher initial levels (Fig. 5B). If Cdk initially promotes Spd2 activity what is their explanation for this?

Minor/discussion points

1. p4 "In typical somatic cells the two mitotic centrosomes need to grow to approximately the same size, as mitotic centrosome size asymmetry can lead to asymmetric spindle assembly and so to defective chromosome segregation. How centrosome growth is regulated in somatic cells is unclear, but in early C. elegans embryos, mitotic centrosome size appears to be set by a limiting pool of the PCM-scaffolding protein SPD-2."<br /> The authors here conflate absolute and relative size. Relative size matters to avoid spindle asymmetries, and centriole involvement in PCM recruitment helps to prevent this (Zwicker et al., PNAS 2014). Absolute size, which is what the authors are concerned with in this manuscript, may be important for spindle scaling, but this is not the same thing.
2. p5 "The centrosomal levels of Polo, Spd-2 and Cnn all started to increase at the start of S-phase, but whereas Cnn levels continued to rise and/or plateau as the embryos entered mitosis, the centrosomal levels of Polo and Spd-2 started to decrease before the entry into mitosis (Wong et al, 2021) (Figure 1A,B). Thus, the components of the mitotic PCM scaffold exhibit different growth kinetics, making it hard to use these proteins to define centrosome "size" at any particular point in the cell cycle."<br /> It is misleading and confusing for the reader to describe Polo and Spd2 as scaffold proteins as opposed to regulators of scaffold assembly. Presently Cnn is the only PCM protein demonstrated to have self-assembly/scaffolding properties based on the authors' own work (conduit, Dev Cell 2014; Feng, Cell 2017). There is little evidence that Polo and Spd2 form anything other than a nucleus for PCM growth.
3. p7 "The centrosomal levels of Grip71, Grip75, Grip128, and Aurora A tended to increase steadily through most of NC13, whereas TACC, Msps and γ-tubulin exhibited a noticeable increase in their recruitment rate towards the end of S-phase, shortly before their recruitment levels peaked (compare NC13 graphs in Fig. 1B). This difference was also obvious if we used centrosome area as a measure of centrosome size (Fig. S1). We conclude that PCM client proteins can be recruited to centrosomes in at least two different ways."<br /> As discussed above apparent differences in kinetics may reflect limitations in the way protein accumulation is measured. It is hard to conceive of a reason why the Grips would display a different mode of protein accumulation from gamma-tubulin, nor is the idea of two different modes of protein accumulation picked up again later in the manuscript.
4. Since the authors mention that the duration of S phase increases between cycles 11 and 13 (p9), are there any measures for the timing of the beginning/end of S phase in each cycle?
5. One of the main findings in the landmark Woodruff paper from 2017 Cell paper was that PCM scaffold polymer could dynamically concentrate client proteins in the absence of any other factors, to an extent similar to that observed in vivo. This list did not include gamma-tubulin, which was later shown to require PLK1 phosphorylation of SPD-5 (Ohta, JCB 2021). However, it did include ZYG-9, the C. elegans ortholog of Msps. If client protein accumulation is an intrinsic property of the PCM scaffold, how do the authors explain that Msps departs prior to NEBD while Cnn continues to accumulate?
6. p13 "The expression of the mutant proteins did not appear to dramatically perturb the centrosomal recruitment of γ-tubulin-GFP, except that the rate at which γ-tubulin-GFP left the centrosome as the embryos entered mitosis was reduced in both mutants compared to WT (Figure 7). This phenotype was subtle, but it was statistically significant, and it seems likely that the presence of large amounts of WT Spd-2 and Cnn in the mutant embryos (Figure 5A,F) would help to mask the potential severity of this phenotype."<br /> This does not quite make sense. Fig. 5 shows that Spd2 dissociation is significantly slowed in the mutant condition. If Spd2 drives gamma-tubulin accumulation (as Fig 6 shows), then the continued presence of Spd2 should prevent dissociation. Yet it apparently does not. Why?

Other

1. p3 and following. The reference for the authors' prior work on PCM recruitment (Wong et al, 2021) should probably be for the final, published article in EMBO J, not the 2021 preprint.
2. Fig. 1. legend "Note that for technical reasons not all of the centrosome proteins could be followed for the full time period." Why not?
3. Figs 4-6. Which cycle is being assessed here?
4. Fig 6. Not plotted here is the rate of dissociation of gamma-tubulin, unlike eg in Fig 7. It is notable that both accumulation and dissociation appear to be slowed in the Spd2 1/2 gene dosage condition.
5. Fig S1B. Some of the graphs in this figure are not labeled (based on Fig.1 presumably gamma-tubulin and Msps).
6. Some of the data in the main figures, including the entirety of Figs. 2 and 3, could be moved to Supplemental to present a more crisp and accessible manuscript.
7. While I sympathize with the authors needing to repeat entire sets of experiments I am not entirely sure it is appropriate to recycle entire sets of data from a previous publication of theirs (Cnn, Spd-2 and Polo recruitment kinetics, reproduced from Wong et al., EMBOJ 2022), since this manuscript is largely concerned with apparent differences between the kinetics of those components and the PCM client proteins now being analysed.

Significance

Control of organelle size has been an active field of research for many years for a large variety of cellular structures and in a range of experimental models. Here, Jordan Raff and colleagues examine the mechanisms underlying centrosome (PCM) size control in Drosophila syncytial embryos, building on their previous work (Wong, EMBOJ 2022) to propose a role for CDK in both promoting (at intermediate levels) and inhibiting (at high levels) PCM expansion.

I found this a difficult manuscript to review, not only because the subject matter is complicated, but so is the writing. Having read and re-read the manuscript some clarity eventually emerges, but it shouldn't be that inaccessible. As for the authors' model I find it intriguing, but not fully supported by the data currently presented.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Wong et al. investigates how cells regulate the increase in the size of the centrosomes (more specifically the size of the pericentriolar material or PCM) that occurs during preparation for mitosis. They use the Drosophila syncytial embryo as a model, focusing on nuclear cycles 11-13, during which cell cycle progression gradually slows. The authors find that centrosomes grow to a consistent size at each cycle by adjusting to the slowed cell cycle, reducing the growth rate and increasing the growth period. This adjustment is proposed to be regulated by the Cdk/Cyclin cell cycle oscillator. Curiously, Cdk/Cyclin activity seems to both promote and inhibit the increase in centrosome size, depending on whether its activity is moderate or very high, respectively. Both effects are proposed to depend on the phosphorylation of centrosome proteins by Cdk/Cyclin.

1. While being comprehensive in the number and type of markers that are being analyzed, there is no analysis of the centrosome's MTOC activity. In my opinion this is missing since centrosome size alone is not necessarily indicative of its MTOC activity, but MTOC activity is what ultimately matters for its role during mitosis. For example, it was observed that centrosome size declines already before mitotic entry, but it is possible that centrosome MTOC activity does not (similar to differences in the timing of the decline of PCM scaffold vs PCM client proteins). While not strictly related to size control, centrosome activity is biologically more relevant than solely size. I would consider it optional, if the authors decide to talk only about centrosome size, but then it should be made clear that size here may not be the most relevant factor.
2. The authors say that during NC13 PCM client proteins can be recruited in "at least two different ways" (p. 7), including a way (rapid increase before peak) that does not resemble PCM scaffold recruitment (steady increase during NC13). How can these two different ways and kinetics be determined by the same Cdk/Cyclin oscillator?
3. I am puzzled by the conclusion that Cdk/Cyclin directly phosphorylates Spd-2 or Cnn at the sites used for mutagenesis. This cannot be concluded based on the presented data.
4. Fig. 6: Doesn't the data show that Cnn does not affect the initial rate of g-tub recruitment, but only the later rapid recruitment shortly before mitosis? In contrast Spd-2 seems to affect the initial phase. This should be described more precisely. Again, I am wondering how this is compatible with direct regulation by a single oscillator, as suggested by the authors (see also point 2 above.
5. I don't find the proposed model very convincing and not fully supported by the presented data.<br /> First, the recruitment kinetics of different centrosome proteins are not all the same, arguing against a simple relationship based on phosphorylation by Cdk/Cyclin. For example, kinases (or phosphatases) may be recruited (or displaced) by Cdk/Cylclin at the centrosome and then locally regulate binding or maintenance of certain centrosome proteins. This could explain profiles that do not display a steady change over time, as would be expected by direct regulation by Cdk/Cyclin.<br /> Second, it is not clear from the description in the text or from Fig. 8 how moderate Cdk/Cyclin activity can promote recruitment and high activity induce loss of proteins at centrosomes. In fact, the experiments with Spd-2 and Cnn phospho-mutants suggest that phosphorylations at the mutated sites also reduce centrosome binding during S phase (at moderate activity) and not only shortly before mitosis (at high activity), since alanine mutants of both Spd-2 and Cnn are increased at centrosomes also during S phase. The model seems to ignore this observation. If these sites are already phosphorylated to decrease centrosome binding in S phase, then what triggers the rapid decrease shortly before mitosis?
6. Can the authors identify and mutate CdK/Cyclin dependent phospho-sites in centrosome proteins that promote centrosome recruitment at moderate Cdk/Cyclin activity? As an alternative to the "protein availability" model for regulation of centrosome size, the proposed model needs to explain how a steadily increasing activity (Cdk/Cyclin) can first induce growth and then turn growth off, when the desired size is reached. This is obvious in the "protein availability" model, where the available protein steadily decreases as centrosomes grow, but this is not at all obvious for an oscillator that behaves in the opposite way during the same period and that can only phosphorylate sites that decrease centrosome binding.

Minor:

1. The authors observe differences in the intensity profiles for different subunits of the gamma-tubulin complex. How do they explain this? Are they not in the same complex? The authors should mention and comment on this.
2. The authors refer at various points in the manuscript to an "inverse-linear" relationship between S phase length and centrosome growth rate, but according to the graphs the rate does not change linearly.

Significance

This is an interesting manuscript that reaches somewhat different conclusions regarding centrosome size control when compared to previous studies in other organisms. In particular, work in C. elegans has proposed that centrosome growth regulation is controlled by the limited cytoplasmic availability of PCM building blocks, whereas the current study proposes a different model based on the activity of a cell cycle oscillator. The model system and approaches are well presented and the data is of good quality. The authors monitor a large number of centrosome markers, each with detailed quantifications of intensity and distribution over time during the different cycles. They also employ two different ways of quantifying centrosome size with similar results, making their quantifications more robust. While the authors include phospho-mutants in their analyses that presumably cannot be phosphorylated by Cdk/Cyclin, the study is largely descriptive. Still, the authors present interesting observations and propose the "oscillator model" an alternative to the "limited availability model" for the regulation of centrosome size, and perhaps that of other organelles. Assuming the authors can clarify inconsistencies and/or provide additional data to support the proposed model, this could be an important finding that expands cell biologists' understanding of organellar size control.

I have expertise in centrosome biology and the role of centrosomes as MTOCs, as well as more general expertise regarding the function of the microtubule cytoskeleton in cell division and differentiation.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

In their manuscript „Live-cell super-resolution nanoscopy reveals modulation of cristae<br /> dynamics in bioenergetically compromised mitochondria", Golombek et al. tested the effects of different mitochondrial toxins on cristae dynamics. The main focus of their work lies on live STED imaging, which they use to visualize cristae merging and splitting. They found swelling of mitochondria and reduced cristae density in response to most toxins, but cristae dynamics remained largely unaffected. Depletion of the membrane potential by administration of CCCP increased cyristae dynamics, while inhibition of ANT had a negative effect on cristae dynamics at least in a subset of mitochondria.

1. The authors state that the used concentrations of mitochondrial toxins commonly result in a change in oxygen consumption. While this is believable, it is not guaranteed that the specific chemicals used for the experiments were working properly (freeze/thawing or simply incorrect storage or aliquotation may have an effect on the compounds). This is even more important in the case of results where no significant change after the administration of the toxins is seen. In Figure 5, the authors report no change in membrane potential after oligomycin administration, this is unexpected. I therefore suggest to include a supplementary figure, in which the functionality of the compounds is verified. This could be done by respiratory measurements (e.g. Seahorse). A Mito Stress Test was performed for Figure 6, but this was done using the Seahorse kit chemicals, which were probably different from the chemicals used in the microscopy experiments.

Response: We appreciate the valid concerns of the reviewer in this point.

A) In order to show the functionality of compounds which were used for performing our experiments including STED imaging, we now performed respiratory measurements employing the concentrations of mitochondrial toxins (Oligomycin A, CCCP, rotenone/antimycin A) which were used during imaging conditions as well as commercially available mitochondrial toxins (Oligomycin A, FCCP, rotenone/antimycin A) with respective concentrations used as a standard for the Mito stress Kit. The new figures are included in Fig S1A & B. HeLa cells treated with seahorse compounds or those used during imaging conditions showed similar results including basal, maximal and spare respiratory capacity. Further, in order to overcome the inefficiency of mitochondrial toxins employed, due to freeze/thaw cycles, we used fresh aliquots (stored at -20°C) as a general strategy. This is clearly observed by a drastic reduction of ΔΨm upon treating HeLa cells with CCCP, antimycin A as well as rotenone (Fig S6A & B). A reduction of mitochondrial ATP levels was also observed upon employing rotenone, antimycin A and oligomycin A confirming that active mitochondrial toxins were used. These experiments demonstrate that the mitochondrial toxins employed throughout our manuscript are functional as expected.

New Figure S1A & B

B) The Fig 6 (now Fig 5 due to Reviewer # 2, Point 7) respirometry experiments which initially employed seahorse compounds and BKA has now been replaced with new experiments where we used mitochondrial toxins similar to STED imaging. Needless, to say, the results are similar to what were observed with seahorse compounds. The new figures are replaced in Fig 5A & 5B.

New Figure 5A & B

C) Oligomycin A inhibits ATP synthase which results in decreased ATP synthesis as observed (Fig 4A & B). Further, oligomycin A is expected to hyperpolarise mitochondria (2). In Fig S6, despite some cells having more ΔΨm, there was no overall significant change when compared to untreated cells. Previous publications also show that there is no significant difference in ΔΨm upon treatment with oligomycin (1) demonstrating that the ΔΨm depends on the concentration of oligomycin, treatment time and cell type.

1. Figure 1 would benefit from a more detailed description of merging/splitting events. Maybe a cartoon plus a zoomed in image of an exemplary event?

Response: Thank you for the suggestion. In order to clearly explain/simplify the understanding of cristae merging and splitting events, we added a cartoon in Fig 1B. The green and magenta arrows show sites of imminent merging and splitting with the green and magenta asterisks representing them respectively in the subsequent frames. The zoomed in images in Fig1A (leftmost panel) are shown to the right as time-lapse images.

New Figure 1B

1. Could the reduced cristae density be an effect of mitochondrial swelling? It is curious that all toxins appear to have the same effect on mitochondrial architecture. What is the fait of an enlarged mitochondrion over time? Mitophagy? And does the percentage of enlarged mitochondria change with increasing treatment time?

Response: Thank you for the comment.

A) We agree that the reduced cristae density is due to mitochondrial swelling. We added the relevant text in the results section ‘Cristae structure is altered in a subset of mammalian cells treated with mitochondrial toxins’. Treatment of HeLa cells, with all the mitochondrial toxins mentioned, uniformly result around 50 % of mitochondria undergoing enlargement (Fig 2B). In enlarged mitochondria where the mitochondrial width is ≥ 650 nm, there is no change in cristae area occupied per mitochondria (Fig S3C & D) and as a result reduced cristae density (Fig 2H). Therefore, it indicates that reduced cristae density occurs due to mitochondrial enlargement.

Figure 2B-F

Figure S3C and D

B) In order to address the fate of mitochondria with increasing time upon treatment with various mitochondrial toxins, we treated the HeLa cells for 4 hrs with mitochondrial toxins. Untreated cells maintained normal mitochondrial morphology while cells treated with various mitochondrial toxins displayed fragmented and swollen mitochondrial morphology. The new Fig S5 is included in the supplementary. Cristae morphology was abnormal displaying interconnected cristae in swollen mitochondria. Since mitochondrial fragmentation is already observed at 4 hours and accompanied by interconnected cristae, the number of cristae merging and splitting were severely reduced.

Our imaging performed within 30 mins of addition of respective toxins overcomes the additional aberrancy of mitochondrial fragmentation which would not allow a reliable analysis of cristae dynamics as too few cristae would be visible within one mitochondrion.

New Figure S5

1. Figure 4C: How was the mitochondrial width determined in the LSM images? Especially in the perinuclear area it will be difficult to determine this parameter without the super-resolution provided by STED. Was this parameter determined manually for selected mitochondria? In the methods part it says that only a maximum of two mitochondria per cell were analyzed. How were these chosen? Was the process blinded?

Response: Thank you for the comment. We could imagine the reason for the ambiguity in understanding.

A) For LSM confocal images involving FRET-based microscopy to determine the ATP levels, we calculated the cell population as belonging to either normal or enlarged category. The confocal images of HeLa cells displayed clear separation of mitochondria even in the perinuclear area (representative images are shown in Fig 4A) and thus it was possible to measure the width of individual mitochondria. The methods section ‘FRET-based microscopy to measure ATP levels’ describes that ‘the cut off for swollen mitochondria was set to 650 nm in congruence with STED SR nanoscopy. If 85% of the mitochondrial population featured enlarged mitochondria, the cells were designated as swollen. Similarly, if 85% of the mitochondrial population featured mitochondria whose width was less than 650 nm, the cell was considered as having normal mitochondria’.

Figure 4A

B) The cristae morphology of various mitochondria is fairly uniform in individual cells. Thus, the mitochondria are representative of the individual cells. Therefore, in order to increase the coverage of various cells, we considered a maximum of two mitochondria from each cell which were randomly chosen. This part is modified in the methods section ‘Quantification of various parameters related to cristae morphology’ to make it clear. Thus, while the quantification of various parameters including dynamics involved individual mitochondria, various cells were classified as belonging to normal or enlarged category while measuring ATP levels.

1. What is the average size of all mitochondria per cell? Is this addressed in Figure 2B or are only analyzed mitochondria included? Please carify. Were the mitochondria chosen for analysis representative for the respective cell?

Response: The data obtained by super-resolution imaging of mitochondria is used for quantifying cristae dynamics which is a very challenging and time-consuming method done in a blind-manner. As mentioned in response 4B, the cristae morphology is fairly uniform in individual cells, therefore, we only included the mitochondria which were analysed for various cristae parameters in our analysis which are really huge data-sets already. Thus, the average size of individual mitochondria per cell are not represented while analysing images obtained with STED SR imaging. Please also check response 4B.

1. explain the mt-Go-AT team2, what is GFP (green fluorescent protein) and OTP (?)

Response: GFP is Green Fluorescent Protein and OFP is Orange Fluorescent protein and included in the revised text.

1. the graphs show in principle, e.g. Fig.1B, 3B-E show events/mitochondrion as far as I understand, not per cristae.

Response: Thank you for pointing this out. It is actually the average number of events per cristae per mitochondria. We have changed the Y-axis to events/cristae/mito in Fig 1C (previous 1B), Fig 3B-E and wherever applicable for other figures throughout the manuscript.

Figure 1C

Figure 3B-E

1. I would recommend changing the legend of the x-axis of Fig.2B-F to mito-width (y-axis could be probability density function, PDF).

Response: We have now changed the X-Axis to mito width (originally width) in Fig 2B-F. The Y-axis are still retained as percentage mitochondria where cells treated with few mitochondrial toxins do not show a gaussian distribution of mitochondrial width.

Figure 2B-F

Referees cross-commenting

both expert opinions address similar concerns and therefore a revision should be requested

Reviewer #1 (Significance):

The study is thorough and the experiments and results are well described. Overall, however, it remains a descriptive study and does not provide mechanisms. There is also no discussion of how MMP-dependent proteins, such as Opa1, which was previously studied by the Reichert group, might be affected. For swelling mechanisms, the opening of the mitochondrial permeability transition pore was discussed. This could be tested using inhibitors, but perhaps not within the scope of this publication. Nevertheless, the information provided by the study is of interest to the bioenergetics community and should be made available.

Response: Thank you for the overall inputs.

We tested the processing of OPA1 forms and found that after 30 mins, only CCCP treatment led to the processing of long isoforms to short forms (Fig S6C). We now included in the discussion that it is possible that short OPA1-forms are correlative to increased cristae merging as well as splitting events upon treatment with CCCP.

New Figure S6C

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:<br /> The authors investigated cristae merging and splitting events using ultra-resolution STED. The goal was to test if cristae membrane remodeling is dependent on OXPHOS complexes, mitochondrial membrane potential (ΔΨm), and the ADP/ATP nucleotide translocator. To do this the authors utilized several mitochondrial toxins with known mechanisms of action. Interestingly, many changed overall cristae density but did not change the cristae remodeling events. Inhibition of ANT did change cristae morphology and cristae dynamics.

Major Concerns

1. Many conclusions and concepts need more clarification. For example, a major take home from the abstract is that various ETC inhibitors and protonophores reduce cristae density but not did not change cristae remodeling events. If cristae density is reduced, how can this occur without cristae remodeling events? Remodeling events need to be clearly defined in the introduction and abstract.

Response: Thank you for pointing out this lack of sharpness in our terminology which indeed can cause a misunderstanding. To avoid this, we have now included ‘changes in cristae morphology’ as well as ‘dynamic merging and splitting events of cristae’ under the broader term cristae remodelling. Thus, we had changed the wording ‘cristae remodeling’ to cristae dynamics in the abstract and wherever appropriate in the manuscript text.

The cristae morphology analysis showed no change in cristae area (Fig S3C) which was accompanied by mitochondrial enlargement. Therefore, cristae density was reduced. For the purpose of clarity, we added a sentence in the introduction section while giving a peek into our results that ‘cristae dynamic events are ongoing despite reduced cristae density’. In addition, we have now included in the results section the following statement: ‘Cristae membrane remodeling has been used to describe cristae dynamic events (i.e. cristae merging and splitting) as well as overall changes in cristae morphology within a single mitochondrion in this manuscript’.

Figure S3C and D

1. Other interpretations are also unclear such as how ETC inhibitors which reduce ATP levels did not impact cristate remodeling events, yet inhibiting ATP/ADP exchange did greatly impact this phenomenon. It seems likely that the inhibition of ANT has nothing to do with ATP/ADP exchange since most of the ETC inhibitors no doubt greatly impact overall ATP/ADP exchange. This interpretation needs clarification.

Response: We agree that further clarification is needed, in particular to explain why ATP/ADP exchange is actually ongoing even when OXPHOS inhibitors are applied and to explain why reduced ATP levels do not mean that there is no ATP/ADP exchange occuring. Treatment of HeLa cells with various mitochondrial toxins inhibiting the function of OXPHOS complexes leads to decreased ATP levels due to ongoing ATP consumption within the cell (Fig 4). One should also consider that two things can and do happen when most of these toxins are applied regarding ATP exchange. First, the ATPase can act in reverse mode which is a (partial) compensatory mechanism to restore ΔΨm and which will further decrease ATP levels (Note: not in the presence of oligomycin). Second, under these conditions ADP/ATP exchange is still ongoing in order to transport ATP derived from glycolysis in the cytosol to the mitochondrial matrix which also causes an (partial) compensatory increase in membrane potential. After ATP import ATP is hydrolysed to ADP for reverse proton pumping via the F1FO-ATPase or alternatively by the F1-part alone without proton pumping. In all these cases it is essential and possible to exchange ADP with ATP constantly. Therefore, the overall exchange of ADP and ATP is not necessarily grossly expected to be different when compared to untreated cells (due to compensatory glycolysis and subsequent ATP import and hydrolysis in the matrix). On the other hand, BKA treatment which clearly impairs the exchange of ADP and ATP will lead to a completely different situation compared to only treating with OXPHOS inhibitors. With BKA the mitochondrial matrix cannot anymore be resupplemented with ATP derived from glycolysis and metabolite flux is grossly hampered. Consistent with this a strong reduction in ΔΨm and oxygen consumption is accompanied with BKA treatment (Fig. 5AB & SFig 7F). Thus, w.r.t cristae dynamic events, in the time-frame we used for imaging, a reduction of ATP levels does not impede occurrence of cristae merging and splitting events while BKA treatment does (Fig S7). We discuss this indeed interesting and unexpected finding in the discussion section. We propose that rather ongoing metabolite flux (ATP/ADP exchange) is critical for maintaining cristae dynamics and blocking it is detrimental for it. We adapted the discussion in this direction to make it more clear.

Figure S7A, B and D

1. Why did the authors wait 30 min to image after the addition of mitochondrial toxins? I would have guessed there is a more rapid change in response to these inhibitors. Is there is a chance he authors missed the most dramatic events?

Response: Since we were inclined to observe early responses, cells were imaged within the first 30 mins after addition of the respective mitochondrial toxins (Please see methods ‘cell culture transfection and mitochondrial toxin treatment’). Thus, to answer this question we want to emphasize that we did not wait 30 minutes but we restricted our time frame of analysis to 30 min. Therefore, we think that we did not miss out on any rapid changes occurring early on. Regarding this point, Reviewer #1 (Query 3) asked for responses at a later time-point. Please read the Reviewer #1, response 3B.

1. How do these mitochondrial toxins that are known to cause mitochondrial swelling not induce changes in cristate density?

Response: Thank you for the question. Probably, there is a misunderstanding. In Fig S3E, we clearly show that as the mitochondrial width increases in cells after treatment with mitochondrial toxins, there is a clear decrease in cristae density. In fact, the reduced cristae density is observed exclusively in enlarged mitochondria. Figure S3E-I

5. It's interesting that inhibition of the ANT translocator by BKA treatment led to increased percentage of mitochondria with abnormal cristae morphology. It's accepted that inhibition of ANT profoundly reduces mitochondrial swelling. Do the authors have any data suggesting that abnormal cristae morphology actually is a mechanism for reducing cell death events such as permeability transition? Did the authors utilize cyclosporin A concomitantly with any of the mitochondrial toxins?

Response: This is a very interesting question! As the reviewer might be aware, there is evidence connecting cristae remodelling to induction of apoptosis (3). Cristae transitioned to a highly interconnected state after tBID treatment within minutes. However, it is unclear what is the contribution of cristae dynamics in this regard. Within 30 mins, there were no visual signs of cell death in our experiments as observed under a microscope. Hence, we did not use cyclosporin A in our experiments. In our opinion, this question will form part of a very interesting future study and is currently beyond the scope of this manuscript.

1. Are the authors confident in the data given many of the experiments utilized quantification of 10-20 mitochondria? How are you sure this sampling is sufficient for phenomenon being studied?

Response: Please see Reviewer 1, Response 4B. As pointed in the response to reviewer #1, the cristae morphology is fairly uniform in individual cells. Therefore, in order to maximise the cell population covered, we randomly used a maximum of two mitochondria from each cell. In addition, we included cristae analysis from at least three biological replicates in order to observe the reproducibility of the data. Taking these factors into consideration, we are confident that our results reflect a sufficient sample size. Further, we would like to point out while our group performs STED super-resolution imaging routinely, the quantification of cristae merging and splitting events done in a blind yet manual manner is a really laborious and time-consuming process. In the future, we are also looking to optimise this at least in a semi-automated manner.

1. Figure 4 and 5 merely confirm current dogma and don't really contribute to the overall conclusions and can be moved to supplemental data.

Response: We agree that Fig 5 is confirming to the current dogma. Therefore, we moved it to Fig S6. Regarding Fig 4, we would like to highlight that there is a decrease of ATP levels before mitochondria enlarge. Thus, we would like to retain it as part of the main figure.

1. It's interesting that BKA dose dependently decreased ATP-linked respiration and all doses limited maximal respiratory capacity. It would be interesting to know if the BKA normal vs. abnormal mitochondria have differential membrane potential?

Response: Thank you for the interesting question. Overall, BKA treatment leads to a significant decrease of ΔΨm in the whole cell population (Fig S7). Further, the abnormal cristae morphology is only seen in one-third of the population of mitochondria (Fig shown in Response 2). Thus, a drop in ΔΨm seems to be a very early response upon exposure to BKA and independent of cristae morphology. An ideal experiment to address this question would be to image cristae dynamics and ΔΨm using super-resolution imaging which is challenging according to the state-of-art and available chemicals.

Figure S7E and F

1. Overall, this is an interesting study and seems appropriately performed but the results and conclusions are unclear. More discussion should include physiological relevance and impact and how this data influences previous work. Some physiological perturbations beyond the mitochondrial toxins and or utilization of genetic models would strengthen the interpretation and overall impact.

Response: Thank you. We added an OPA1 blot showing the different L-OPA1 and S-OPA1. (Reviewer #1, response in significance section) where we observed that S-OPA1cleavage is selectively enhanced in CCCP-treated cells which could be correlated with enhanced cristae dynamics. We also included these results in the main text.

New Figure S6C

Referees cross-commenting

Yes, I conclude that given the significant overlap in reviwer comments and general need for clarification of concepts and data that a revision is in order.

Reviewer #2 (Significance):

Overall, a highly specialized study with audience limited to mitochondriacs. Although, I'll note tis is a hot area of study and there is high interest in the field. Some of the data interpretation is difficult to understand and overall more context is needed to explain the results, impact and relevance. Defining exactly what a cristae remodeling event is and how this differs from cristae density and how the two aren't directly connected is unclear.

Review by a mitochondrial biologist specializing in mitochondrial signaling and connection to physiology.

References:

1. Baker MJ, Lampe PA, Stojanovski D, Korwitz A, Anand R, et al. 2014. Stress-induced OMA1 activation and autocatalytic turnover regulate OPA1-dependent mitochondrial dynamics. EMBO J 33: 578-93
2. Farkas DL, Wei MD, Febbroriello P, Carson JH, Loew LM. 1989. Simultaneous imaging of cell and mitochondrial membrane potentials. Biophys J 56: 1053-69
3. Scorrano L, Ashiya M, Buttle K, Weiler S, Oakes SA, et al. 2002. A distinct pathway remodels mitochondrial cristae and mobilizes cytochrome c during apoptosis. Dev Cell 2: 55-67

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors investigated cristae merging and splitting events using ultra-resolution STED. The goal was to test if cristae membrane remodeling is dependent on OXPHOS complexes, mitochondrial membrane potential (ΔΨm), and the ADP/ATP nucleotide translocator. To do this the authors utilized several mitochondrial toxins with known mechanisms of action. Interestingly, many changed overall cristae density but did not change the cristae remodeling events. Inhibition of ANT did change cristae morphology and cristae dynamics.

Major Concerns

1. Many conclusions and concepts need more clarification. For example, a major take home from the abstract is that various ETC inhibitors and protonophores reduce cristae density but not did not change cristae remodeling events. If cristae density is reduced, how can this occur without cristae remodeling events? Remodeling events need to be clearly defined in the introduction and abstract.
2. Other interpretations are also unclear such as how ETC inhibitors which reduce ATP levels did not impact cristate remodeling events, yet inhibiting ATP/ADP exchange did greatly impact this phenomenon. It seems likely that the inhibition of ANT has nothing to do with ATP/ADP exchange since most of the ETC inhibitors no doubt greatly impact overall ATP/ADP exchange. This interpretation needs clarification.
3. Why did the authors wait 30 min to image after the addition of mitochondrial toxins? I would have guessed there is a more rapid change in response to these inhibitors. Is there is a chance he authors missed the most dramatic events?
4. How do these mitochondrial toxins that are known to cause mitochondrial swelling not induce changes in cristate density?
5. It's interesting that inhibition of the ANT translocator by BKA treatment led to increased percentage of mitochondria with abnormal cristae morphology. It's accepted that inhibition of ANT profoundly reduces mitochondrial swelling. Do the authors have any data suggesting that abnormal cristae morphology actually is a mechanism for reducing cell death events such as permeability transition? Did the authors utilize cyclosporin A concomitantly with any of the mitochondrial toxins?
6. Are the authors confident in the data given many of the experiments utilized quantification of 10-20 mitochondria? How are you sure this sampling is sufficient for phenomenon being studied?
7. Figure 4 and 5 merely confirm current dogma and don't really contribute to the overall conclusions and can be moved to supplemental data.
8. It's interesting that BKA dose dependently decreased ATP-linked respiration and all doses limited maximal respiratory capacity. It would be interesting to know if the BKA normal vs. abnormal mitochondria have differential membrane potential?
9. Overall, this is an interesting study and seems appropriately performed but the results and conclusions are unclear. More discussion should include physiological relevance and impact and how this data influences previous work. Some physiological perturbations beyond the mitochondrial toxins and or utilization of genetic models would strengthen the interpretation and overall impact.

Referees cross-commenting

Yes, I conclude that given the significant overlap in reviewer comments and general need for clarification of concepts and data that a revision is in order.

Significance

Overall, a highly specialized study with audience limited to mitochondriacs. Although, I'll note tis is a hot area of study and there is high interest in the field. Some of the data interpretation is difficult to understand and overall more context is needed to explain the results, impact and relevance. Defining exactly what a cristae remodeling event is and how this differs from cristae density and how the two aren't directly connected is unclear.

Review by a mitochondrial biologist specializing in mitochondrial signaling and connection to physiology.

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

Learn more at Review Commons

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Referee #1

Evidence, reproducibility and clarity

In their manuscript „Live-cell super-resolution nanoscopy reveals modulation of cristae<br /> dynamics in bioenergetically compromised mitochondria", Golombek et al. tested the effects of different mitochondrial toxins on cristae dynamics. The main focus of their work lies on live STED imaging, which they use to visualize cristae merging and splitting. They found swelling of mitochondria and reduced cristae density in response to most toxins, but cristae dynamics remained largely unaffected. Depletion of the membrane potential by administration of CCCP increased cyristae dynamics, while inhibition of ANT had a negative effect on cristae dynamics at least in a subset of mitochondria.

Major comments

• The authors state that the used concentrations of mitochondrial toxins commonly result in a change in oxygen consumption. While this is believable, it is not guaranteed that the specific chemicals used for the experiments were working properly (freeze/thawing or simply incorrect storage or aliquotation may have an effect on the compounds). This is even more important in the case of results where no significant change after the administration of the toxins is seen. In Figure 5, the authors report no change in membrane potential after oligomycin administration, this is unexpected. I therefore suggest to include a supplementary figure, in which the functionality of the compounds is verified. This could be done by respiratory measurements (e.g. Seahorse). A Mito Stress Test was performed for Figure 6, but this was done using the Seahorse kit chemicals, which were probably different from the chemicals used in the microscopy experiments.
• Figure 1 would benefit from a more detailed description of merging/splitting events. Maybe a cartoon plus a zoomed in image of an exemplary event?
• Could the reduced cristae density be an effect of mitochondrial swelling? It is curious that all toxins appear to have the same effect on mitochondrial architecture. What is the fait of an enlarged mitochondrion over time? Mitophagy? And does the percentage of enlarged mitochondria change with increasing treatment time?
• Figure 4C: How was the mitochondrial width determined in the LSM images? Especially in the perinuclear area it will be difficult to determine this parameter without the super-resolution provided by STED. Was this parameter determined manually for selected mitochondria? In the methods part it says that only a maximum of two mitochondria per cell were analyzed. How were these chosen? Was the process blinded?
• What is the average size of all mitochondria per cell? Is this addressed in Figure 2B or are only analyzed mitochondria included? Please carify. Were the mitochondria chosen for analysis representative for the respective cell?

Minor comments

1. explain the mt-Go-AT team2, what is GFP (green fluorescent protein) and OTP (?)
2. the graphs show in principle, e.g. Fig.1B, 3B-E show events/mitochondrion as far as I understand, not per cristae.
3. I would recommend changing the legend of the x-axis of Fig.2B-F to mito-width (y-axis could be probability density function, PDF).

Referees cross-commenting

both expert opinions address similar concerns and therefore a revision should be requested

Significance

The study is thorough and the experiments and results are well described. Overall, however, it remains a descriptive study and does not provide mechanisms. There is also no discussion of how MMP-dependent proteins, such as Opa1, which was previously studied by the Reichert group, might be affected. For swelling mechanisms, the opening of the mitochondrial permeability transition pore was discussed. This could be tested using inhibitors, but perhaps not within the scope of this publication. Nevertheless, the information provided by the study is of interest to the bioenergetics community and should be made available.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Major comments<br /> In the paper "Microtubules under mechanical pressure can breach dense actin networks", the authors showed clear evidence that pressure plays an important role in microtubule breaching into dense actin networks using elegant in vitro reconstitution assays. They have argued that the pressure results from polymerization force of microtubules, which builds up when microtubules are immobilized in the opposite end of breaching, by the means of actin microtubule crosslinking factor Tau.

Authors answer:

We thank the reviewer for his/her positive comments on our manuscript.

It would definitely be interesting to see lack of breaching in the presence of crosslinking deficient Tau construct in order to rule out the off -target effect of Tau on microtubule and actin architecture which may possibly facilitate breaching.

Authors answer:

This is an interesting suggestion. Unfortunately, we do not have in hand such crosslinking deficient Tau construct. However, please note that we showed two independent ways to demonstrate the role of pressure. One is indeed by crosslinking microtubule to actin bundle with Tau, but the other is by blocking the two opposite ends of microtubules with two dense actin networks. So, we think our conclusion about the role of pressure is solid.

The authors have also observed microtubule breaching into dense actin networks in living cells. However, in Figure 1C, better cell/ image processing might have been chosen to increase the visibility of actin structures that microtubules encounter on their way to breaching. In Figure S1D, for example, the similar actin structures in lamellipodia are very nicely visible.

Authors answer:

We apologize but we don’t understand reviewer’s comment. In figure 1C images of actin networks are shown in black and white and are more visible than in figure S1D where they are shown in magenta and overlaid with microtubules. In any case, we increased the contrast of images to make fine actin structures at the cell edge clearer.

It is also interesting that on Figure 6A, actin bundles look different than the rest of the figures on the paper. It almost looks like actin bundles become branched, whereas in the other Figures actin bundles are either singular or two-three bundles joined together at the point very close to the edge of micropatterned lipid bilayer.

Authors answer:

This is correct. In this experiment several bundles co-aligned. As mentioned by the reviewer this could also be visible in other conditions without Tau (such as in Figure 4E), and, as shown below, this structure of bundle was not visible in all fields we looked at. So we don’t think this structure is responsible for the changes we measured in the ability of microtubules to penetrate the actin network in the presence of Tau.

Minor comments<br /> In the legend of Figure 4E, it should be written "white arrow" instead of "yellow arrow".<br /> In the Results section "crosslinking between microtubules and actin bundles increase piercing frequency", in the sentence number 7, it should be written "backwards" instead of "reaward".

Authors answer: We modified the text and legend according to the reviewer suggestions.

Reviewer #1 (Significance):

The experimental setup of the paper is quite significant in the field, given the difficulty of observing dynamics of dense cytoskeletal structures in living cells. Moreover, the paper gives insight into how microtubule behavior can vary depending on different morphological states of actin network.

Authors answer: We thank the reviewer for his/her overall very positive feedback on our manuscript.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors developed a novel in vitro system to investigate the interaction of dynamic microtubules with the F-actin network. While this system does produce some interesting results, it is unclear how exactly this replicates or explains what might happen near a cell's leading edge. There is a limited characterization of the produced F-actin networks. For example, it is unclear to what extent the F-actin networks are similar or different to cell lamellipodial networks. What is the density / expected mesh size of these networks and could that be varied / manipulated? The bottomline observation that microtubules can grow into F-actin networks if they have nowhere else to go does not seem particularly ground-breaking, and the discussion is very shallow. Overall writing could be improved; there are lots of typos and grammatical inconsistencies. The second paragraph of the introduction is a bit convoluted.

Authors answer:

We thank the reviewer for his/her comments. Figure 1 was used to illustrate the behavior of microtubules encountering actin networks in cells and the fact that they struggle to penetrate actin network. This is only a way to argue that the penetration of actin network is a relevant question, that cannot be easily addressed in cells. However, it is correct that our in vitro systems, as it is the case for all in vitro reconstituted systems, cannot tend exactly to reproduce a lamellipodial cellular network. But it offers a better way to modulate actin network architecture. We have used in vitro systems to characterize the different behavior of microtubules when they encounter dense actin networks in different conditions, guided or not by actin bundles, constraint or not at the two ends.

The observation that microtubule can penetrate actin network when pressurized might not be “ground breaking”, still it contradicts previous works showing that microtubule under pressure tend to depolymerize (Janson et al, J Cell Biol, 2003), which would obviously prevent them from penetrating actin networks. So, our conclusion was somehow unexpected.

We found important to discuss the fact that although the microtubule polymerizing forces is sufficient to breach dense actin network, it must be counteracted by another mechanism immobilizing microtubules. This means that in cells, expression level of actin-microtubule crosslinker modulate the penetration of microtubule into the lamellipodium.

However, we agree that the second paragraph of the introduction is not absolutely necessary and removed it.

Specific comments:

Fig. 1 seems a bit anecdotal. The authors revisit an observation that has been made before. I can see how it is used as rationale for the in vitro system, but not sure that this adds much to the overall story. Clearly different cell types are different, but without some sort of quantification this remains meaningless. It should also be noted in the discussion maybe that there are large differences between cells in 2D and 3D. Microtubules much more frequently grow to the cell edge compared with 2D (see Akhmanova SLAIN2 paper from some years ago).

Authors answer:

We agree with these comments. Indeed, Figure 1 is used only as an illustration of the behavior of microtubules encountering actin network in cells. As the reviewer said, microtubule penetration and actin architectures will both vary a lot from one cell type to another. So we believe that quantification for these particular cases will not extend the illustrative purpose of this figure where it is already clear that some microtubules can penetrate and other can’t.

Fig. 2: While Arp2/3 certainly promotes branched F-actin networks, from the data provided it is not clear to me to what extent the produced F-actin networks replicate F-actin organization at the cell edge. If this a the point the authors are trying to make, the ultrastructure of their in vitro networks needs some additional characterization. As far as it is possible to discern from the data provided, the F-actin meshwork on the stripes in E looks pretty much identical in both panels (and not really like a dendritic network that in a cell also would have a certain polarity with barbed ends facing out), and the bundles on the left don't look like anything that normally occurs in a cell.

Authors answer:

We also agree with these comments. The networks we assembled are not lamellipodial-like networks, there are branched network of various densities, with or without bundles. It is true that bundles of filaments do not grow out of lamellipodial network in cells. However, bundles of aligned and linear filaments exist in cells, in the form of radial fibers or transverse arcs, along which microtubule tend to align. And these structures might guide microtubules toward cell protrusions, as it is the case in growth cone for example.

Fig. 4 It is unclear what is going on here. Given that without F-actin bundles, polymerizing microtubules are freely moving around, it does not come as a surprise that they would never penetrate the F-actin network because as the authors correctly state the growing end will push back from the barrier. So, then why do they sometimes penetrate when bundles are present? In 4A it appears that microtubule growth into f-actin only happens once the microtubule minus ends gets stuck between F-actin bundles on the other side. 4D is the same as 4A; so that makes me think this really does not occur that often. Does the microtubule plus end only penetrate the F-actin meshwork when the minus end gets stuck on the other side? This seems important and also means microtubule penetration may not have anything to do with the F-actin network architecture at the plus end. This needs to be quantified.

Authors answer:

This is perfectly correct. In figure 4 the two actin networks are distant, and the microtubules only rarely penetrate them because they are rarely in contact with them at both ends. This occurs only when bundles orient microtubules perpendicular to the edges of the actin network, since in this configuration the distance between the two actin networks is shorter. Hence our motivation to bring actin networks closer to each other in figure 5.

Fig. 5 I guess that sort of solves my confusion with Fig. 4. The quantification graphs in 5B and 5C are flipped with respect to the figure legend (?).

Authors answer:

Indeed, in this figure we distinguished the role of pressure (when both microtubule ends are in contact with actin networks) and the role of alignment with actin bundles. And found that the presence of bundles is useless and that only pressure matters.

I understand the rationale for not considering microtubules that grow at a shallow angle, but there does not seem to be that much of a difference between 5B and 5D. Wouldn't a better quantification simply compare microtubules that contact F-actin at both ends compared with microtubules were the minus end is free. In this case, I would expect a very large difference in penetration.

Authors answer:

This is also correct. The difference is so important that when one end is free the microtubule never penetrate. We mention it in the text but did not plot these data. This is why we measured only microtubule with both ends contacting an actin network and did not consider the one at shallow angles.

We added the illustration of the condition with short distance and actin bundles (shown below) to make this more clear in the figure.

The small difference between 5B and 5D shows that by eliminating those microtubules there is no more difference between the conditions with or without bundles. And thus that their contribution in favoring microtubule penetration was to favor optimal orientation to get pressurized at the two ends rather than offering a sort of favorable network organization at their base. However, we agree with the reviewer that the absence of difference between the two populations, with or without actin bundle, when considering only microtubule interacting with actin at angles higher than 30° is not quite striking. We tested all angles (see below) and found that actually the absence of difference is more obvious when considering microtubules interacting with more than 60°. And the analysis of angle distribution, now reported in Figure 5D, showed that in both conditions most microtubules interact with more than 60°, so we only exclude few outliers by considering those that interact with more than 60°. So we changed the presentation of our data in Figure 5C by changing the threshold from 30 to 60°.

Do microtubules under pressure ever bend/buckle in this in vitro situation. As the authors state, in cells, that happens frequently. This difference is interesting. Why?

In vitro microtubules buckle homogeneously between their two ends. These long buckling wavelengths are not very spectacular. In cells, microtubules are crosslinked to actin filaments or other structures over shorter distances (see quantification below). This leads to buckling with shorter wavelength, which is more striking.

It is customary to refer to polymerized actin as F-actin.

The supplementary videos are not referenced in the manuscript.

Authors answer:

We apologize and have now referenced the supplementary video in the manuscript.

Reviewer #2 (Significance):

The manuscript describes results from a novel assay to study interactions between F-actin networks and dynamic microtubules in vitro. While of interest to a specialized audience, the overall finding that microtubules can grow into an F-actin meshwork is somewhat incremental especially because of the limited characterization of the F-actin networks used. It remains unclear to what extent this is relevant to a physiological context in cells.

My field of expertise is related to cytoskeleton dynamics and quantitative microscopy in live cells.

Authors answer:

Although intuitive, the demonstration that the density of actin network can prevent microtubule penetration is novel. More importantly, the demonstration that anchoring of microtubule is sufficient to increase the pressure to such a point that microtubule can then penetrate those networks is also novel and significant to appreciate when and how they do so in cells.

Reviewer #3 (Evidence, reproducibility and clarity):

In this paper, the authors present an in vitro assay designed to explore the dynamic interaction between growing microtubules and pre-existing actin networks. Notably, the presence of linear actin bundles facilitated the movement of polymerizing microtubules along actin filaments. When microtubules were immobilized to two spatially separated actin networks, they exhibited the ability to breach and penetrate dense actin meshworks. This penetration was attributed to the mechanical pressure generated by microtubule polymerization. The authors tested tau as a microtubule-actin crosslinking protein in this process and found that tau promoted microtubule penetration into dense actin meshwork. Although the findings in this paper are potentially significant, the work is still in its preliminary stage and the scope is limited.

Authors answer:

We thank the reviewer to summarize properly the main findings of our manuscript.

1. The authors observed that the inclusion of tau, a microtubule-associated protein known for its role in promoting microtubule polymerization, significantly facilitated microtubule penetration into dense actin meshworks. This enhancement is likely attributed to tau's ability to promote microtubule polymerization, generating stronger forces within the microtubules that enable them to breach the actin meshworks. To validate the involvement of the crosslinking function in the process, the authors should explore the effects of other microtubule-actin crosslinking proteins in their assay.

Authors answer:

We thank the reviewer for this interesting suggestion regarding the role of Tau in our experiments. To address this comment, we have analyzed the rate of growth in our experiments in presence and absence of Tau (see quantification below). We found that the construction of Tau we used reduced microtubule growth rate. Therefore, we believe that microtubule growth was not responsible for the improved penetration of microtubule in dense actin networks in our assay, and that it was rather the crosslinking ability of Tau that played a significant role.

1. The paper highlights the importance of anchoring both ends of microtubules to two adjacent actin networks for successful penetration into the actin meshworks. However, the precise mechanisms by which these microtubule ends are anchored to actin filaments are not elaborated upon. Providing detailed insights into this anchoring process would enhance the readers' comprehension of the experimental setup and its relevance to the observed results.

Authors answer:

We apologize for this lack of clarity. We don’t think that microtubule ends are “anchored” to the actin network. They are simply embedded into it. This embedding prevents them from moving rearward and thus lead to pressure increase as they polymerize.

1. Additional information on the experimental methods is warranted to improve the reproducibility and clarity of the study. Specifically, the authors should elucidate the process through which nucleation-promoting factors were grafted onto lipid bilayers. This detail is crucial for researchers seeking to replicate or build upon the study's findings.

Authors answer:

We apologize for this lack of clarity. There was indeed an error in our description of SUV preparation with lipid-biotin. We have now revised our material and method section. In particular we have described more accurately the various steps we used to micropattern WA-streptavidin onto lipid-biotin.

1. In Fig. 5D, the authors observed no significant difference in the breaching probability between microtubules that contacted the actin meshwork at an angle higher than 30°, with or without actin bundles. To ensure a better comparison, it is advisable to focus on quantifying the microtubules that are contacting two actin meshworks at both ends (the immobilized microtubules), as they would have similar probabilities of being pressurized by their growth. Moreover, further justification is required to explain the choice of 30° as the threshold angle and its significance in the context of microtubule behavior.

Authors answer:

We thank the reviewer for this comment. We apologize for the confusion. The quantification we made is precisely the one described by the reviewer. We made this more clear by adding further illustration of the two conditions and the measurement made.

1. Fig. 5C appears to depict the "Distribution of the angle of the interaction of microtubules in the presence (10nM of Arp2/3 complex) or absence (100 nM of Arp2/3 complex) of actin bundles" instead of the "proportion of microtubules piercing the branched actin network." The alphabet labels in the figure should be updated accordingly. Additionally, the authors should clarify whether a comparison was conducted between the means of the angles in the two conditions and whether any observed differences were statistically significant.

Authors answer:

We apologize for this confusion. We updated the figure legend in which 5C and 5D were inverted.

1. Investigating the potential significant difference in the mean interaction angles between the absence and presence of actin bundles would be intriguing. The presence of actin bundles might indeed influence the interaction angle or contact position, potentially increasing penetration frequency. This insight would further enrich the findings and provide valuable context for understanding the interplay between microtubules and actin networks.

Authors answer:

We apologize for this confusion. We now report the statistical difference. And indeed, it accounts for the difference it the penetration frequency, as shown by the absence of difference when we consider only microtubules that are more or less perpendicular to the network. This is indeed one of the most significant conclusion of our work. We added some schematics to make this clearer.

1. More comprehensive information about the statistical analyses should be provided. This'd be important for the validity and reliability of the study's conclusions.

Authors answer:

We apologize for this lack of clarity. The statistical analysis we performed were not described in the Materials and Methods section but in each figure legend.

Reviewer #3 (Significance):

The work represents an advance in understanding the mechanism by which microtubules navigate dense actin meshworks.

Authors answer:

We thank the reviewer for this positive evaluation of our work.

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Referee #3

Evidence, reproducibility and clarity

In this paper, the authors present an in vitro assay designed to explore the dynamic interaction between growing microtubules and pre-existing actin networks. Notably, the presence of linear actin bundles facilitated the movement of polymerizing microtubules along actin filaments. When microtubules were immobilized to two spatially separated actin networks, they exhibited the ability to breach and penetrate dense actin meshworks. This penetration was attributed to the mechanical pressure generated by microtubule polymerization. The authors tested tau as a microtubule-actin crosslinking protein in this process and found that tau promoted microtubule penetration into dense actin meshwork. Although the findings in this paper are potentially significant, the work is still in its preliminary stage and the scope is limited.

1. The authors observed that the inclusion of tau, a microtubule-associated protein known for its role in promoting microtubule polymerization, significantly facilitated microtubule penetration into dense actin meshworks. This enhancement is likely attributed to tau's ability to promote microtubule polymerization, generating stronger forces within the microtubules that enable them to breach the actin meshworks. To validate the involvement of the crosslinking function in the process, the authors should explore the effects of other microtubule-actin crosslinking proteins in their assay.
2. The paper highlights the importance of anchoring both ends of microtubules to two adjacent actin networks for successful penetration into the actin meshworks. However, the precise mechanisms by which these microtubule ends are anchored to actin filaments are not elaborated upon. Providing detailed insights into this anchoring process would enhance the readers' comprehension of the experimental setup and its relevance to the observed results.
3. Additional information on the experimental methods is warranted to improve the reproducibility and clarity of the study. Specifically, the authors should elucidate the process through which nucleation-promoting factors were grafted onto lipid bilayers. This detail is crucial for researchers seeking to replicate or build upon the study's findings.
4. In Fig. 5D, the authors observed no significant difference in the breaching probability between microtubules that contacted the actin meshwork at an angle higher than 30{degree sign}, with or without actin bundles. To ensure a better comparison, it is advisable to focus on quantifying the microtubules that are contacting two actin meshworks at both ends (the immobilized microtubules), as they would have similar probabilities of being pressurized by their growth. Moreover, further justification is required to explain the choice of 30{degree sign} as the threshold angle and its significance in the context of microtubule behavior.
5. Fig. 5C appears to depict the "Distribution of the angle of the interaction of microtubules in the presence (10nM of Arp2/3 complex) or absence (100 nM of Arp2/3 complex) of actin bundles" instead of the "proportion of microtubules piercing the branched actin network." The alphabet labels in the figure should be updated accordingly. Additionally, the authors should clarify whether a comparison was conducted between the means of the angles in the two conditions and whether any observed differences were statistically significant.
6. Investigating the potential significant difference in the mean interaction angles between the absence and presence of actin bundles would be intriguing. The presence of actin bundles might indeed influence the interaction angle or contact position, potentially increasing penetration frequency. This insight would further enrich the findings and provide valuable context for understanding the interplay between microtubules and actin networks.
7. More comprehensive information about the statistical analyses should be provided. This'd be important for the validity and reliability of the study's conclusions.

Significance

The work represents an advance in understanding the mechanism by which microtubules navigate dense actin meshworks.

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Referee #2

Evidence, reproducibility and clarity

The authors developed a novel in vitro system to investigate the interaction of dynamic microtubules with the F-actin network. While this system does produce some interesting results, it is unclear how exactly this replicates or explains what might happen near a cell's leading edge. There is a limited characterization of the produced F-actin networks. For example, it is unclear to what extent the F-actin networks are similar or different to cell lamellipodial networks. What is the density / expected mesh size of these networks and could that be varied / manipulated? The bottomline observation that microtubules can grow into F-actin networks if they have nowhere else to go does not seem particularly ground-breaking, and the discussion is very shallow. Overall writing could be improved; there are lots of typos and grammatical inconsistencies. The second paragraph of the introduction is a bit convoluted.

Specific comments:

Fig. 1 seems a bit anecdotal. The authors revisit an observation that has been made before. I can see how it is used as rationale for the in vitro system, but not sure that this adds much to the overall story. Clearly different cell types are different, but without some sort of quantification this remains meaningless. It should also be noted in the discussion maybe that there are large differences between cells in 2D and 3D. Microtubules much more frequently grow to the cell edge compared with 2D (see Akhmanova SLAIN2 paper from some years ago).

Fig. 2: While Arp2/3 certainly promotes branched F-actin networks, from the data provided it is not clear to me to what extent the produced F-actin networks replicate F-actin organization at the cell edge. If this a the point the authors are trying to make, the ultrastructure of their in vitro networks needs some additional characterization. As far as it is possible to discern from the data provided, the F-actin meshwork on the stripes in E looks pretty much identical in both panels (and not really like a dendritic network that in a cell also would have a certain polarity with barbed ends facing out), and the bundles on the left don't look like anything that normally occurs in a cell.

Fig. 4 It is unclear what is going on here. Given that without F-actin bundles, polymerizing microtubules are freely moving around, it does not come as a surprise that they would never penetrate the F-actin network because as the authors correctly state the growing end will push back from the barrier. So, then why do they sometimes penetrate when bundles are present? In 4A it appears that microtubule growth into f-actin only happens once the microtubule minus ends gets stuck between F-actin bundles on the other side. 4D is the same as 4A; so that makes me think this really does not occur that often. Does the microtubule plus end only penetrate the F-actin meshwork when the minus end gets stuck on the other side? This seems important and also means microtubule penetration may not have anything to do with the F-actin network architecture at the plus end. This needs to be quantified.

Fig. 5 I guess that sort of solves my confusion with Fig. 4. The quantification graphs in 5B and 5C are flipped with respect to the figure legend (?). I understand the rationale for not considering microtubules that grow at a shallow angle, but there does not seem to be that much of a difference between 5B and 5D. Wouldn't a better quantification simply compare microtubules that contact F-actin at both ends compared with microtubules were the minus end is free. In this case, I would expect a very large difference in penetration. Do microtubules under pressure ever bend/buckle in this in vitro situation. As the authors state, in cells, that happens frequently. This difference is interesting. Why?<br /> It is customary to refer to polymerized actin as F-actin.<br /> The supplementary videos are not referenced in the manuscript.

Significance

The manuscript describes results from a novel assay to study interactions between F-actin networks and dynamic microtubules in vitro. While of interest to a specialized audience, the overall finding that microtubules can grow into an F-actin meshwork is somewhat incremental especially because of the limited characterization of the F-actin networks used. It remains unclear to what extent this is relevant to a physiological context in cells.

My field of expertise is related to cytoskeleton dynamics and quantitative microscopy in live cells.

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Referee #1

Evidence, reproducibility and clarity

Major comments

In the paper "Microtubules under mechanical pressure can<br /> breach dense actin networks", the authors showed clear evidence that pressure plays an important role in microtubule breaching into dense actin networks using elegant in vitro reconstitution assays. They have argued that the pressure results from polymerization force of microtubules, which builds up when microtubules are immobilized in the opposite end of breaching, by the means of actin microtubule crosslinking factor Tau.<br /> It would definitely be interesting to see lack of breaching in the presence of crosslinking deficient Tau construct in order to rule out the off -target effect of Tau on microtubule and actin architecture which may possibly facilitate breaching.

The authors have also observed microtubule breaching into dense actin networks in living cells. However, in Figure 1C, better cell/ image processing might have been chosen to increase the visibility of actin structures that microtubules encounter on their way to breaching. In Figure S1D, for example, the similar actin structures in lamellipodia are very nicely visible.

It is also interesting that on Figure 6A, actin bundles look different than the rest of the figures on the paper. It almost looks like actin bundles become branched, whereas in the other Figures actin bundles are either singular or two-three bundles joined together at the point very close to the edge of micropatterned lipid bilayer.

Minor comments

In the legend of Figure 4E, it should be written "white arrow" instead of "yellow arrow".<br /> In the Results section "crosslinking between microtubules and actin bundles increase piercing frequency", in the sentence number 7, it should be written "backwards" instead of "reaward".

Significance

The experimental setup of the paper is quite significant in the field, given the difficulty of observing dynamics of dense cytoskeletal structures in living cells. Moreover, the paper gives insight into how microtubule behavior can vary depending on different morphological states of actin network.

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Reply to the reviewers

General Statements

We are happy to resubmit our manuscript “The protective function of an immunity protein against the cis-toxic effects of a Xanothomonas Type IV Secretion System Effector” by Gabriel Oka et al. This paper shows that the cohort of immunity proteins associated with the cocktail of toxic effectors secreted by the Xanthomonas citri T4SS are not required to protect against toxins injected by neighboring cells but rather provide protection against endogenous toxins of the cell in which they were produced. To our knowledge, this the first description of an antibacterial secretion system in which the immunity proteins are dedicated to protecting cells against cis-intoxication, a point we emphasize in the revised introduction.

We thank the reviewers for their thorough revision of the manuscript. Two of the three reviewers clearly expressed the opinion that the manuscript would be of general interest and should be published. We have carried out a number of new experiments and data analyses to respond to most of the suggestions of all three reviewers and believe that the manuscript is significantly improved as a result.

Reviewer #1 (Evidence, reproducibility and clarity):

The manuscript by Oka et al. shows that one effector of X. citri is likely translocated into the periplasm where it cleaves PG unless inhibited by its cognate immunity protein. Interestingly, this effector is required for killing of target cells like E. coli in T4SS-dependent manner but it does not seem to be delivered into X. citri cells by T4SS. Authors show using various assays that cells lacking the immunity protein have various phenotypes including lysis and defect in biofilm formation, however, despite "cis-intoxication" the ability to kill other bacteria or infect plants remains unaffected. The manuscript is well written and in general all the experiments have proper controls and thus the conclusions seem solid. The results described here are novel and interesting as they are unexpected.

Major issues that should be addressed:

- Test various deletion variants of the toxin to identify which part of the protein is responsible for its translocation into the periplasm. This may help to identify the possible mechanism of translocation of the toxin into the periplasm. Alternatively, the authors may attempt to select for non-toxic point mutants of the toxin. This could be done by a random PCR mutagenesis of the toxin and a selection of the surviving mutants in the absence of the immunity protein.

Thank you for your insightful experimental suggestions using PCR mutagenesis to investigate the molecular mechanisms of the alternative translocation of X-Tfes to the periplasm. However, I regret to inform you that the first five authors of this manuscript are no longer a member of my lab. Therefore, please consider accepting the results shown in Figure 5A where we observe that the N-terminal domain of X-TfeXAC2609 that lacks the XVIPCD domain still abolishes biofilm formation in the absence of X-TfiXAC2610. Also, note that the E48A point mutation in the active site of the GH19 domain that abolishes the in vitro activity of X-TfeXAC2609 (Souza et al. 2015), also abolishes X-TFEXAC2609 toxicity in vivo in the absence of X-TfiXAC2610(Figure 5). Furthermore, in the predicted structure of the X-TfiXAC2610(54-267)-X-TfeXAC2609(1-194) complex (Figure 6), A tyrosine side chain in the conserved loop in X-TfiXAC2610 interacts directly with Glu48 in the X-TfeXAC2609 active site. One possibility for further investigation is the remaining region of X-TfeXAC2609(195-306) as a putative translocation domain. Sequence analysis of this region indicates that it encodes a canonical peptidoglycan binding domain. Another possibility is the existing intrinsic leakage of cytoplasmic proteins to the periplasm. As we understand it, the leakage of cytoplasmic proteins to the periplasm is not a well-documented phenomenon, although there is some evidence that suggests it may occur (PMID: 28808000, PMC3016450 references cited in the revised manuscript). This poorly characterized T4SS-independent pathway of translocation as indicated in Figure 1B (pathway 2).

- Test if localization of the immunity protein to the cytoplasm blocks its activity. An immunity protein mutant that lacks its secretion signal should not protect against cis-intoxication.

To address the question, we conducted new assays on colony opacity, as shown in Figure S2C. The X. citri ∆X-TfiXAC2610 strain was transformed with a plasmid expressing a cytoplasmic version of X-TfiXAC2610 that lacks the signal peptide and lipobox (X-TfiXAC2610(His-22-267)). Figure S2C shows that this cytosolic version of X-TfiXAC2610 protects X. citri from the toxic effects of X-TfeXAC2609 in the ∆X-TfiXAC2610 background. This suggests that X-TfiXAC2610(His-22-267) may directly interact with X-TfeXAC2609 in the cytoplasm, leading to the inhibition of X-TfeXAC2609 hydrolase activity and/or inhibition of its translocation into the periplasm. This is now mentioned in the results section of the revised manuscript

While many experiments support the conclusion that the toxin is responsible for "cis-intoxication, the test of "trans-intoxication" should be done again but with the same setup as was used for testing of killing of E. coli. The CPRG based assay is far more sensitive than counting survival by plating to count CFUs. This test should be done at a relatively high initial OD so that there is an immediate contact between the "killer" and the "prey" bacteria (lacking immunity/effector). If needed, LacZ should be over-expressed in X. citri to make use of the CPRG based assay. In addition, such assay could be used also for "cis-intoxication" to supplement the potentially hard to quantify biofilm experiments shown in Fig. 4 (e.g. test all the T4SS mutants for "cis-intoxication").

We are confident that the X-Tfis do not play a role in protecting against T4SS-mediated trans-intoxication since we continue to observe X-TfeXAC2609-dependent intoxication even in the absence of a functional XT4SS (see experiments using strains lacking X-T4SS subunits in Figures 2, S2, 3, 4 and 5. This is not to say that trans-intoxication does not occur. In fact, it does, and there is an independent mechanism that protects against it. We will provide details of the mechanism that protects against trans-intoxication in a forthcoming manuscript. In the present manuscript, we are addressing the phenomenon of cis-intoxication. To support our conclusion that the immunity proteins are not involved in the prevention of trans-intoxication does not occur in X. citri, we have included one additional supplementary video: Movie S7 shows that wild-type Xanthomonas citri does not kill and X. citri Δ8Δ2609-GFP. The absence of killing events in these experiments indicates that the X-T4SS-associated X-Tfi immunity proteins are not required for protection against X-T4SS-mediated sibling attack.

In addition, such assay could be used also for "cis-intoxication" to supplement the potentially hard to quantify biofilm experiments shown in Fig. 4 (e.g. test all the T4SS mutants for "cis-intoxication").

- Fig. 2A needs a positive control. For example, test killing of E. coli under the same conditions.

Figure 2A of the revised manuscript now shows a CPRG assay competition assay that clearly demonstrates X-T4SS-dependent killing of E.coli MG by X. citri. We have now included the results of CFU experiments of X. citri vs E. coli competitions in a new Supplementary Figure (Figure S1) that are consistent with the CPRG assays. We note that our group has published similar results in the past (Souza et al. 2015; Oliveira et al. 2016; Oka et al. 2022). CFU measurements of X. citri vs E. coli competition assays are performed under slightly different conditions from the X. citri vs X. citri assays shown in Fig 2B. This is because E. coli grows at a significantly faster rate than X. citri so the initial cell ratios in these experiments have to be modified.

- Authors should look at the paper by Ho et al. PNAS 2017, which describes trafficking of VgrG of V. cholerae into the periplasm of E. coli without an obvious secretion signal. The effector of X. citri may behave similarly.

We thank the reviewer for this observation and now mention the paper by Ho et al. in the Discussion of the revised manuscript. Using a number of different algorithms (TatP, SignalP 6.0) we do not find any evidence of putative signal sequences. In the Discussion, we also mention the manuscript by Dong et al., 2013 that showed that the immunity protein TsiV3 that neutralizes VgrG3 is critical to prevent trans-intoxication.

- Provide some form of quantification of the phenotypes (cell rounding and cell death) observed using live-cell imaging.

As suggested by the reviewer, we performed a quantitative analysis of the propidium iodide (PI) permeability by calculating the percentage of PI permeable cells observed in movies S1-S5. This data is now presented in Figure 3 and Table S4 of the revised manuscript.

- Provide quantification of biofilm related phenotypes as well as of the citrus canker development assay

As suggested by the reviewer, we have carried out experiments to quantify the amount of biofilm using a crystal violet assay (absorbance at 570 nm). The results are presented in Figure S5 of the revised manuscript.

Reviewer #1 (Significance):

The study provides an interesting insight into immunity proteins against anti-bacterial toxins. It points to a need to protect against "cis-intoxication". This is novel and interesting to a wide audience of microbiologists interested in bacterial competition as this could be true also for other toxins.

We thank the reviewer for his/her positive recommendation.

It would be however important to identify how is the toxin translocating to the periplasm of the producing bacterium. Some insight into the mechanism would vastly improve the study. My expertise is in understanding bacterial interactions and competition but I lack a direct experience with assays specific for X. citri.

We agree that an understanding of the mechanism of translocation into the periplasm would be interesting but is beyond the scope of the present manuscript. However, we do point out that this has been observed previously by other groups in the fourth paragraph of the Discussion of the revised manuscript: “... In the case of X-TfeXAC2609, the toxin somehow makes its way into the cell periplasm where, in the absence of X-TfiXAC2610, it degrades the peptidoglycan layer. Analysis of the X-TfeXAC2609 sequence by the SignalP 6.0 (Teufel et al., 2022) and other algorithms failed to detect any putative N-terminal signal peptide. Although the mechanism responsible for X-TfeXAC2609 transfer into the periplasm is at the moment unknown, we have shown that it is independent of a functional X-T4SS and of the XVIPCD secretion signal. Other bacterial proteins have been shown to transfer into the periplasm without any obvious secretion signal, for example VgrG3 from Vibrio cholerae (Ho et al. 2017) and recombinant forms of HdeA and chymotrypsin inhibitor 2 (Banes and Pielak, 2011).”

Reviewer #2 (Evidence, reproducibility and clarity):

This manuscript explores the role of an immunity protein of the Xanthomonas type IV secretion system (X-T4SS). In contrast to most T4SSs that conjugate plasmids or transfer effectors into host cells, this system is able to kill other bacteria similar to the role of T6SSs. Here, the authors tested whether the immunity protein XAC2610 functions to prevent cis-intoxication (by self) and/or trans-intoxication (by sister cells). They provide data that the XAC2610 immunity protein functions to protect cis intoxication, but not trans-intoxication, by the T4SS effector XAC2609 (which functions as a peptidoglycan hydrolase). Based on AlphaFold modeling, they went on to identify a residue in XAC2610 that is critical for inhibiting the activity of the XAC2609 toxin. Overall the data is fairly solid and generally support the conclusions the authors made.

Major comments:

One of the major conclusions of the manuscript is that XAC2610 does not prevent trans-intoxication and the data in the manuscript support this conclusion. However, I wonder if this is an oversimplification. Notably, the authors observed that wild type Xantho was unable to kill a target cell lacking 8 different toxin/immunity systems (Fig. 1A). One could conclude that none of these immunity proteins function in preventing trans-intoxication ... or ... perhaps it appears that none perform this role because wild-type Xantho never attacks its siblings? For example, it is conceivable that Xantho uses a general mechanism, perhaps somewhat similar to phage exclusion or plasmid incompatibility, to prevent sibling attack? To me this seems more likely than none of the eight immunity proteins play a role in preventing trans-intoxication. Moreover, the phenotype observed for the ∆2610 mutant in preventing cis-intoxication is somewhat subtle, likely because the toxin and the immunity protein are topologically restricted to the cytoplasm and the periplasm, respectively. This would make sense if this were not the primary role for 2610.

Ideally the authors will be able to test this theory by demonstrating that a wild-type Xantho strain can attack (but likely not kill) its siblings. Alternatively, could the authors test if related, but not identical, Xantho strains that express 2609/2610 are able to kill their ∆2610 mutant, i.e. do "cousins" attack each other? Not sure about the semantics but this could be described as preventing trans-intoxication. If they are unable to do either experiment, that is ok but they should at least describe this concept in their discussion (assuming they agree).

We thank the reviewer for his insightful comments. Indeed, this manuscript is focussed solely on the role of X-Tfi immunity proteins which we show to be principally involved in avoiding cis-intoxication (self-intoxication). The question of trans-intoxication will be left to an upcoming manuscript by our group. In fact we have identified a key factor (not an X-Tfi) that is responsible for inhibiting trans-intoxication. As suggested by the reviewer, we have now added the following text to the end of the third paragraph of the Discussion: “Nevertheless, the fact that wild-type X. citri is unable to kill strains lacking immunity proteins is intriguing. That cells in some way avoid trans-intoxication is revealed by the fact that X. citri wild-type cells carrying an X-T4SS and full cohort of X-Tfes do not kill the X. citri Δ8Δ2609-GFP, the X. citri ∆X-TfeXAC2609∆X-TfiXAC2610, or any other X-T4SS-deficient strain tested points to a still-to-be-characterized mechanism of protection against trans-intoxication (fratricide) that will be addressed in future studies by our group.”

Minor comments:

1. Figure 1 is a bit confusing in terms of the layout. It would be beneficial if the authors separated parts A and B by a few spaces.

As suggested, we have modified the layout of Figure 1 to more clearly distinguish between the two mechanisms tested.

1. Figure 2A should start off by showing that the Xantho T4SS can kill other bacteria (e.g. Fig S4A). This would set up the paper better.

As suggested, old Figure S4A has now been transferred to Figure 2A in the revised manuscript.

1. Fig. 2A should include p values.

As suggested, p values have been provided in the legend of Figure 2B (old Figure 2A).

1. Fig. 2B is really hard to see and should be removed from the manuscript (although I do appreciate the novelty of the technique using Marilyn Monroe).

We have transferred the old Fig. 2B to the Supplementary Material (Fig S2) of the revised manuscript. We agree that the effect is subtle, but we want to maintain the figure since the transparency of the ΔXAC2610 X. citri colonies over time were the first observations that led us to investigate this phenomenon. Additionally, to reduce potential human bias and to enhance the objectivity of the assay, we employed a Convolutional Neural Network (CNN) to analyze all the colonies presented in Fig S2. This method provides a confidence tendency index for opacity and transparency variations. A detailed description of this new methodology is in the "Materials and Methods" section (Convolutional Neural Network (CNN) analysis).

1. Instead all of the data in Fig. 2B should be shown in a new version of Fig. 2C. Fig. 2C should include additional controls including:
2. A wild type strain containing 2609 and 2610 mutants
3. A complete virB operon deletion in combination with 2609 and 2610 mutants
4. ∆8 strain
5. 2609 lacking its T4SS signal sequence
6. 2609 targeted to the periplasm with a sec signal sequence
7. etc.

We sincerely value the comprehensive suggestions for improving what was previously presented as Fig. 2D. (Current version of Figure 2B is the Fig S2 as mentioned in the previous observation). We encounter a practical challenge here: the primary authors responsible for these experiments, especially the first five, have since departed from our lab. This situation limits our immediate capacity to execute the extensive set of experiments you've proposed.

Recognizing the significance of the controls you've outlined for a quantitative analysis of the colony phenotypes (Fig. 2C (current version)) we have instead supplemented our study with a rigorous quantitative analysis of the microscopy assays referenced in Movies S1-S5, Figure 3, Table S4. These analyses further emphasize our observations concerning colony transparency (Fig S2).

1. Figure 2C. The VirB7 western band looks like in the 2610 complemented strain.

Thank you for pointing out the discrepancy in our previous manuscript at line 366, which pertains to the description of the mutants in old Fig. 2. The double mutant, ΔX-TfiXAC2610ΔvirB7 strain, was actually complemented with X-TfiXAC2610 (as stated in the current version (Fig S2B), and not with VirB7. Additionally, we have corrected the legend of the figure (line 684 previous version) from (∆X-TfiXAC2610∆VirB7c) to (∆X-TfiXAC2610c∆VirB7). We apologize for the mix-up in our earlier description and are grateful for your meticulous review and feedback in this matter. Furthermore, we agree that, in this particular experiment, the VirB7 band seems weaker but it is clearly visible in the 2610 complemented strain.

1. Figure 3C should include a comparison of exponential vs. stationary phase cells. In addition, the results for the ∆2610 mutant and the ∆2610 ∆B7 double mutant appear to be different(?). P values should be provided. If it is statistically significant, then this should be explained in the manuscript. It was not clear how the % damaged cells were calculated? # of cells? Stats?

The statistical analysis that the reviewer suggested has been provided in the new version of the Figure 4C and its legend. In addition, we have also included a supplementary Table S5 that presents the total number of cells analyzed in these experiments.

1. The majority of Figure 4 should be replaced by assaying the effect of a virB operon deletion rather than showing the individual mutants.

We believe that retaining old Figure 4 (Figure 5 of the revised manuscript) is important. By showcasing results from this specific set of single mutants, we are able to rule out the possibility that X-TfeXAC2609 translocation into the periplasm is mediated by a distinct X-T4SS subunit or subcomplex. We've expanded on this rationale at the start of the paragraph to provide a more comprehensive justification for our approach.

1. Discussion:
2. The last one to two paragraphs of the results belong in the Discussion.
3. A more detailed description of cis-intoxication would be useful.

As suggested, the last two paragraphs the Results section of the original manuscript have now been moved to the end of the Discussion.

As suggested by the reviewer, third paragraph of the Discussion describes cis-intoxication in more detail.

Reviewer #2 (Significance):

This work provides a conceptual advance in understanding the protective function of a T4SS immunity protein, X-Tfe XAC2610, against the cis-toxic effects of the T4SS effector, X-Tfi XAC2610. It will likely be of interest to scientists interested in T4SSs & T6SSs and interbacterial competition. Overall this is a thought-provoking manuscript and should be published in a respectable journal.

We sincerely thank Reviewer #2 for the thoughtful appraisal and positive feedback regarding our work. We are gratified to hear that the reviewer recognizes the conceptual advance our research brings to the understanding of T4SS immunity proteins and are encouraged by the acknowledgment that this manuscript will be of interest to our peers. We truly appreciate the endorsement for publication in a reputable journal.

Reviewer #3 (Evidence, reproducibility and clarity):

In this study, the authors suggest that TfeXAC2609-TfiXAC2610 represent a novel deviation from the established paradigm in contact-dependent interbacterial secretion systems. X. citri strains lacking the predicted immunity protein, TfiXAC2610, do not suffer a competitive disadvantage when grown in T4SS-inducing conditions against a wild-type strain. Furthermore, cells lacking the immunity develop aberrant morphology and auto-lyse. The mechanism for self-intoxication by TfeXAC2609 is independent of a functional T4SS, and intoxication is exacerbated when the toxin's T4SS-signal sequence is removed.

Major Points

1. The authors of the study do not provide sufficient evidence that TfeXAC2609 contributes to T4SS mediated killing. Does the toxin behave in a synergistic way, rather than mediate killing independently? Does removing the toxin and immunity change the competitive advantage of X. citri?

We have shown in a previous publication that X-TfeXAC2609 does contribute to X-T4SS mediated killing (Oka et al, 2022). In that published paper we show that even in the absence of seven other toxin/antitoxin pairs, X-T4SS mediated transfer of only one effector (X-TfeXAC2609 or X-TfeXAC3634) can kill E. coli cells.

Removing only X-TfeXAC2609 and X-TfiXAC2610 does not significantly reduce the ability of X. citri cells to kill E. coli (Fig. 2A of the revised manuscript). This is expected since this double mutant still retains seven other toxin/immunity pairs.

Suggested Experiments: Competing, against E. coli, both WT X. citri and X. citri ΔXAC2609 ΔXAC2610, and determining whether there is a change in relative competitive advantage, or expressing TfeXAC2609 in a heterologous system and marking any observed toxic phenotype.

The results of the experiment suggested by the reviewer have now been included in part A of the revised version of Figure 2. The effect of deleting only one toxin such as X-TfeXAC2609 results in no detectable difference in killing efficiency, most likely due to the presence of the eight other X-Tfes, three of which have been shown (XAC3634) or are predicted (XAC0466 and XAC1918) to have pedptidoglycan hydrolase activity (Oka et al, 2022, Souza, 2015, Sgro et al, 2019).

1. Authors should directly answer where the toxin is active and localized in the cell.

Suggested Experiments: Western blot subcellular fractionation (cytoplasm, periplasm, etc) to determine the localization of each protein.

In response to the query about the toxin's activity and localization within the cell, we acknowledge the importance of such experiments to shed light on these aspects. However, I would like to highlight that the five first authors of this work are no longer affiliated with our lab. Consequently, we are facing constraints in terms of manpower and expertise to undertake comprehensive experiments such as the suggested subcellular fractionation.

Also, our earlier work demonstrated the importance of the XVIPCD for secretion via X-T4SS (Souza, 2015) and in vivo activity of X-TfeXAC2609 (Oka et al., 2022). Moreover, using heterologous proteins expressed in E. coli (Souza, 2015) and our current observation that the absence of X-TfiXAC2610 induces spheroplast formation (Fig 4A-B, Movie S6) strongly suggest that the peptidoglycan glycohydrolase activity of the N-terminal domain of X-TfeXAC2609 acts in the periplasm.

1. There is no evidence that TfeXAC2609 plays any role in inter-bacterial killing besides that is predicted from its genetic arrangement and in vitro assays from a previous publication.

Suggested Experiments: Again, with the available antibodies, detecting whether TfeXAC2609 is being secreted, either in competition settings against X. citri or E. coli; given that there is no killing observed in Fig. 2B, it may also be a suitable control for this experiment.

We have published in vivo evidence in the past:

Souza et al, 2015 showed that X-TfeXAC2609 is secreted when in contact with E. coli cells.

Oka et al, 2022 showed that an X. citri strain expressing X-TfeXAC2609/X-TfiXAC2610 but lacking seven other toxin/antitoxin pairs can still kill E. coli.

1. The structural and co-evolutionary analysis seems to miss an essential point - that the lack of fratricide protection is not due to a novel protein-protein interaction.

We do not understand this comment. As we point out in the manuscript, X-TfiXAC2610 does not protect against fratricide (trans-intoxication) but instead does protect against suicide (cis-intoxication). This protection requires a X-TfeXAC2609-X-TfiXAC2610 protein-protein interaction supported by the structural and co-evolutionary analysis as well as the experimental data using the X-TfiXAC2610 Y170A mutant (Fig. 6D of the revised manuscript). Moreover, we believe that the structural and sequence analysis significant expand the knowledge of the broader family of immunity proteins to which X-TfiXAC2610 belongs (Fig. S10 and Fig. S11 of the revised manuscript).

1. The role of the immunity in biofilm formation is confusing. Cells lacking the immunity die within 96 hours (the auto-lysis phenotype). Given that the immunity is required for viability in this time frame, wouldn't it also be required for viability after five days?

Suggested Amendments: Remove or de-emphasize.

In the manuscript we use several different techniques to show that cells lacking the X-TfiXAC2610 immunity protein are less viable than the wild-type strain under certain conditions (growth on LB agar plates, biofilm formation) but perhaps not under others (ie in direct short-term competition experiments against E. coli and in long-term (2 week) in planta citrus canker assays). This is consistent with the fact that ultrastructural analysis by transmission electron microscopy shows that when grown in liquid media, only around 2% of X. citri cells lacking X-TfiXAC2610 present significant damage to their cell envelope (only 0.1% of wild-type cells show damage).

1. Why does cell permeability increase with the loss of the T4SS signal sequence? Without there being greater evidence to support that an alternative secretion system is secreting or transporting the toxin into the periplasm, which may compete with the T4SS, additional hypotheses should be experimentally probed.

The reviewer is comparing the propidium iodide permeability results observed for the ΔX-TfiXAC2610 mutant (carrying an empty pBRA plasmid) that expresses full-length X-TfeXAC2609 from its chromossomal gene with the ΔX-TfeXAC2609/ΔX-TfiXAC2610 double mutant carrying the pBRA-X-TfeXAC2609NT plasmid that expresses the X-TfeXAC2609 protein lacking the T4SS signal sequence from a very strong inducible promoter. Therefore, it can be expected that the levels of the truncated effector could be significantly greater than that of the full-length effector, leading to more damage.

Note that, in the absence of X-TfiXAC2610, cell permeability increases only if X-TfeXAC2609 is present, with or without its XVIPCD T4SS signal sequence. This is consistent with a cis-intoxication mechanism which is independent of the X-T4SS-mediated transfer of the toxin from one cell to another. As we mention in the revised manuscript, and as pointed out by reviewer 1, Ho et al have also observed that when a lysozyme-containing domain of the T6SS effector VgrG3 is expressed in E. coli or in Vibrio cholerae, it can be detected in the periplasm in spite of the lack of a detectable signal sequence and in the absence of a functional T6SS. Ho et al attributed this observation to a “cryptic” secretion mechanism.

1. Unclear if the the loss of cell envelope integrity is a direct effect of TfeXAC2609 activity and not an artifact of cell death. The microscopy also does not show a consistent change in morphology amongst intoxicated cells as there are healthy cells adjacent to lysed cells. This needs to be investigated in much more mechanistic detail.

We observed that the X-TfeXAC2609 toxicity is dependent on its lysozyme domain since a point mutation in the active site residue (E48A) abolishes the toxicity-related phenotype in the biofilm assay (Figure 5).

1. The role for immunity proteins in cis-intoxication is not novel as proposed by the authors. For example, see PMID:22511866 and PMID:26456113 where the authors used an inducible degradation system to show that in a T6SS null strain, cis-intoxication occurs when immunity is depleted.

We thank the reviewer for pointing out these observations which are now mentioned and cited in the Introduction and in the Discussion of the revised manuscript.

Minor Revisions

1. Inconsistent use of the term "self-killing"; either refers to the killing of kin cells, or self (interchangeably used to refer to trans and cis killing).

The term “self-killing” no longer appears in the manuscript.

1. Terms trans-intoxication and cis-intoxication are convoluted and not constructive to the points being communicated. Self-killing vs kin-killing seem more intuitive and clearer. We prefer to maintain the use of the terms cis-intoxication and trans-intoxication which we defined in the Introduction, at the beginning of the Results section and in the Discussion as well as in Figure 1.
2. Readability would be improved by the removal of double negatives.

We have tried to avoid these whenever possible.

1. Bacterial competition assay in methods only refers to the E. coli competition, not the one between the different genotypes of X. citri.

Both methods were described in the same paragraph in the original manuscript. For clarity, this has now been divided into two sections in the revised manuscript: “X. citri vs E. coli competition assays” and “X. citri vs X. citri competition assays”.

1. Strain naming scheme presented on pg. 16 doesn't conform to traditional, and clearer, nomenclature typically used.

We have checked the manuscript to make sure that strain naming was consistent throughout the manuscript.

1. On Pg 25, there is a typo "X-TfiXAC2609" as opposed to X-TfeXAC2609

Thank you for the observation. This has now been corrected.

1. Line 619 - "or several other immunity proteins in competition assays"... where was this data shown? No immediate connection to any figures from this paper nor are there any references.

This is shown in Figure 2B and in Movie S7 which is now cited directly in the revised manuscript.

Reviewer #3 (Significance):

Overall it is difficult to take paradigm-conflicting conclusions at face-value when they are not presented alongside concrete experimental evidence. Without directly showing that the toxin localizes to the periplasm, the explanation that "the toxin somehow makes its way into the cell periplasm [independent of the T4SS] where it degrades the peptidoglycan layer" hinders the other conclusions presented by the authors. Consequently, my enthusiasm for this work is minimal.

We deeply appreciate the insightful feedback from Reviewer #3, particularly regarding the concerns about paradigm-conflicting conclusions. We are steadfast in our commitment to ensuring that our findings are both rigorous and scientifically relevant.

Evidence for Toxin Localization: We understand the criticality of concrete experimental evidence for toxin localization to the periplasm. While our data suggest an yet to be discovered translocation pathway of X-TfeXAC2609 from the cytoplasm to the periplasm, we recognize the importance of providing direct evidence. We are actively working on methodologies to understand this phenomenon. However, we do not believe that answering this question is absolutely necessary to understand the main conclusions of the present manuscript.

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 study, the authors suggest that TfeXAC2609-TfiXAC2610 represent a novel deviation from the established paradigm in contact-dependent interbacterial secretion systems. X. citri strains lacking the predicted immunity protein, TfiXAC2610, do not suffer a competitive disadvantage when grown in T4SS-inducing conditions against a wild-type strain. Furthermore, cells lacking the immunity develop aberrant morphology and auto-lyse. The mechanism for self-intoxication by TfeXAC2609 is independent of a functional T4SS, and intoxication is exacerbated when the toxin's T4SS-signal sequence is removed.

Major Points

1. The authors of the study do not provide sufficient evidence that TfeXAC2609 contributes to T4SS mediated killing. Does the toxin behave in a synergistic way, rather than mediate killing independently? Does removing the toxin and immunity change the competitive advantage of X. citri?<br /> Suggested Experiments: Competing, against E. coli, both WT X. citri and X. citri ΔXAC2609 ΔXAC2610, and determining whether there is a change in relative competitive advantage, or expressing TfeXAC2609 in a heterologous system and marking any observed toxic phenotype.
2. Authors should directly answer where the toxin is active and localized in the cell.<br /> Suggested Experiments: Western blot subcellular fractionation (cytoplasm, periplasm, etc) to determine the localization of each protein.
3. There is no evidence that TfeXAC2609 plays any role in inter-bacterial killing besides that is predicted from its genetic arrangement and in vitro assays from a previous publication.<br /> Suggested Experiments: Again, with the available antibodies, detecting whether TfeXAC2609 is being secreted, either in competition settings against X. citri or E. coli; given that there is no killing observed in Fig. 2B, it may also be a suitable control for this experiment.
4. The structural and co-evolutionary analysis seems to miss an essential point - that the lack of fratricide protection is not due to a novel protein-protein interaction.
5. The role of the immunity in biofilm formation is confusing. Cells lacking the immunity die within 96 hours (the auto-lysis phenotype). Given that the immunity is required for viability in this time frame, wouldn't it also be required for viability after five days?<br /> Suggested Amendments: Remove or de-emphasize.
6. Why does cell permeability increase with the loss of the T4SS signal sequence? Without there being greater evidence to support that an alternative secretion system is secreting or transporting the toxin into the periplasm, which may compete with the T4SS, additional hypotheses should be experimentally probed.
7. Unclear if the the loss of cell envelope integrity is a direct effect of TfeXAC2609 activity and not an artifact of cell death. The microscopy also does not show a consistent change in morphology amongst intoxicated cells as there are healthy cells adjacent to lysed cells. This needs to be investigated in much more mechanistic detail.
8. The role for immunity proteins in cis-intoxication is not novel as proposed by the authors. For example, see PMID:22511866 and PMID:26456113 where the authors used an inducible degradation system to show that in a T6SS null strain, cis-intoxication occurs when immunity is depleted.

Minor Revisions

1. Inconsistent use of the term "self-killing"; either refers to the killing of kin cells, or self (interchangeably used to refer to trans and cis killing).
2. Terms trans-intoxication and cis-intoxication are convoluted and not constructive to the points being communicated. Self-killing vs kin-killing seem more intuitive and clearer
3. Readability would be improved by the removal of double negatives.
4. Bacterial competition assay in methods only refers to the E. coli competition, not the one between the different genotypes of X. citri.
5. Strain naming scheme presented on pg. 16 doesn't conform to traditional, and clearer, nomenclature typically used.
6. On Pg 25, there is a typo "X-TfiXAC2609" as opposed to X-TfeXAC2609
7. Line 619 - "or several other immunity proteins in competition assays"... where was this data shown? No immediate connection to any figures from this paper nor are there any references.

Significance

Overall it is difficult to take paradigm-conflicting conclusions at face-value when they are not presented alongside concrete experimental evidence. Without directly showing that the toxin localizes to the periplasm, the explanation that "the toxin somehow makes its way into the cell periplasm [independent of the T4SS] where it degrades the peptidoglycan layer" hinders the other conclusions presented by the authors. Consequently, my enthusiasm for this work is minimal.

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

This manuscript explores the role of an immunity protein of the Xanthomonas type IV secretion system (X-T4SS). In contrast to most T4SSs that conjugate plasmids or transfer effectors into host cells, this system is able to kill other bacteria similar to the role of T6SSs. Here, the authors tested whether the immunity protein XAC2610 functions to prevent cis-intoxication (by self) and/or trans-intoxication (by sister cells). They provide data that the XAC2610 immunity protein functions to protect cis intoxication, but not trans-intoxication, by the T4SS effector XAC2609 (which functions as a peptidoglycan hydrolase). Based on AlphaFold modeling, they went on to identify a residue in XAC2610 that is critical for inhibiting the activity of the XAC2609 toxin. Overall the data is fairly solid and generally support the conclusions the authors made.

Major comments:

One of the major conclusions of the manuscript is that XAC2610 does not prevent trans-intoxication and the data in the manuscript support this conclusion. However, I wonder if this is an oversimplification. Notably, the authors observed that wild type Xantho was unable to kill a target cell lacking 8 different toxin/immunity systems (Fig. 1A). One could conclude that none of these immunity proteins function in preventing trans-intoxication ... or ... perhaps it appears that none perform this role because wild-type Xantho never attacks its siblings? For example, it is conceivable that Xantho uses a general mechanism, perhaps somewhat similar to phage exclusion or plasmid incompatibility, to prevent sibling attack? To me this seems more likely than none of the eight immunity proteins play a role in preventing trans-intoxication. Moreover, the phenotype observed for the ∆2610 mutant in preventing cis-intoxication is somewhat subtle, likely because the toxin and the immunity protein are topologically restricted to the cytoplasm and the periplasm, respectively. This would make sense if this were not the primary role for 2610.

Ideally the authors will be able to test this theory by demonstrating that a wild-type Xantho strain can attack (but likely not kill) its siblings. Alternatively, could the authors test if related, but not identical, Xantho strains that express 2609/2610 are able to kill their ∆2610 mutant, i.e. do "cousins" attack each other? Not sure about the semantics but this could be described as preventing trans-intoxication. If they are unable to do either experiment, that is ok but they should at least describe this concept in their discussion (assuming they agree).

Since the cis-intoxication phenotype of the ∆2610 mutant is subtle, it would strengthen the authors' conclusions on cis-intoxication if they artificially targeted XAC2609 to the periplasm with a sec signal sequence. If the authors are correct, this should be a lethal event in the absence of the 2610 immunity protein. This might be useful in terms of figuring out how the 2609 toxin normally gets into the periplasm, a major unanswered question in this manuscript.

Minor comments:

1. Figure 1 is a bit confusing in terms of the layout. It would be beneficial if the authors separated parts A and B by a few spaces.
2. Figure 2A should start off by showing that the Xantho T4SS can kill other bacteria (e.g. Fig S4A). This would set up the paper better.
3. Fig. 2A should include p values.
4. Fig. 2B is really hard to see and should be removed from the manuscript (although I do appreciate the novelty of the technique using Marilyn Monroe).
5. Instead all of the data in Fig. 2B should be shown in a new version of Fig. 2C. Fig. 2C should include additional controls including:
6. a. A wild type strain containing 2609 and 2610 mutants
7. b. A complete virB operon deletion in combination with 2609 and 2610 mutants
8. c. ∆8 strain
9. d. 2609 lacking its T4SS signal sequence
10. e. 2609 targeted to the periplasm with a sec signal sequence
11. f. etc.
12. Figure 2C. The VirB7 western band looks like in the 2610 complemented strain.
13. Figure 3C should include a comparison of exponential vs. stationary phase cells. In addition, the results for the ∆2610 mutant and the ∆2610 ∆B7 double mutant appear to be different(?). P values should be provided. If it is statistically significant, then this should be explained in the manuscript. It was not clear how the % damaged cells were calculated? # of cells? Stats?
14. The majority of Figure 4 should be replaced by assaying the effect of a virB operon deletion rather than showing the individual mutants.
15. Discussion:
16. a. The last one to two paragraphs of the results belong in the Discussion.
17. b. A more detailed description of cis-intoxication would be useful.

Significance

This work provides a conceptual advance in understanding the protective function of a T4SS immunity protein, X-Tfe XAC2610, against the cis-toxic effects of the T4SS effector, X-Tfi XAC2610. It will likely be of interest to scientists interested in T4SSs & T6SSs and interbacterial competition. Overall this is a thought-provoking manuscript and should be published in a respectable journal.

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

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Oka et al. shows that one effector of X. citri is likely translocated into the periplasm where it cleaves PG unless inhibited by its cognate immunity protein. Interestingly, this effector is required for killing of target cells like E. coli in T4SS-dependent manner but it does not seem to be delivered into X. citri cells by T4SS. Authors show using various assays that cells lacking the immunity protein have various phenotypes including lysis and defect in biofilm formation, however, despite "cis-intoxication" the ability to kill other bacteria or infect plants remains unaffected. The manuscript is well written and in general all the experiments have proper controls and thus the conclusions seem solid. The results described here are novel and interesting as they as unexpected.

Major issues that should be addressed:

• Test various deletion variants of the toxin to identify which part of the protein is responsible for its translocation into the periplasm. This may help to identify the possible mechanism of translocation of the toxin into the periplasm. Alternatively, the authors may attempt to select for non-toxic point mutants of the toxin. This could be done by a random PCR mutagenesis of the toxin and a selection of the surviving mutants in the absence of the immunity protein.
• Test if localization of the immunity protein to the cytoplasm blocks its activity. An immunity protein mutant that lacks its secretion signal should not protect against cis-intoxication.
• While many experiments support the conclusion that the toxin is responsible for "cis-intoxication, the test of "trans-intoxication" should be done again but with the same setup as was used for testing of killing of E. coli. The CPRG based assay is far more sensitive than counting survival by plating to count CFUs. This test should be done at a relatively high initial OD so that there is an immediate contact between the "killer" and the "prey" bacteria (lacking immunity/effector). If needed, LacZ should be over-expressed in X. citri to make use of the CPRG based assay. In addition, such assay could be used also for "cis-intoxication" to supplement the potentially hard to quantify biofilm experiments shown in Fig. 4 (e.g. test all the T4SS mutants for "cis-intoxication").
• Fig. 2A needs a positive control. For example, test killing of E. coli under the same conditions.
• Authors should look at the paper by Ho et al. PNAS 2017, which describes trafficking of VgrG of V. cholerae into the periplasm of E. coli without an obvious secretion signal. The effector of X. citri may behave similarly.
• Provide some form of quantification of the phenotypes (cell rounding and cell death) observed using live-cell imaging.
• Provide quantification of biofilm related phenotypes as well as of the citrus canker development assay.

Significance

The study provides an interesting insight into immunity proteins against anti-bacterial toxins. It points to a need to protect against "cis-intoxication". This is novel and interesting to a wide audience of microbiologists interested in bacterial competition as this could be true also for other toxins. It would be however important to identify how is the toxin translocating to the periplasm of the producing bacterium. Some insight into the mechanism would vastly improve the study. My expertise is in understanding bacterial interactions and competition but I lack a direct experience with assays specific for X. citri.

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Reply to the reviewers

We have addressed all the queries and suggestions put forth by the reviewers. Major changes include:

1. Expansion of PILOT Functionality and Analysis: We have substantially extended the functionality and analysis capabilities of PILOT, particularly in relation to sample clustering. This enhancement now encompasses the incorporation of statistical tests aimed at identifying cell types and genes associated with distinct patient groups. We applied this expanded feature in an exploratory analysis of sub-clusters within pancreas ductal adenocarcinoma data (PDAC).
2. Clarification of Benchmarking Methods: We have provided clear elucidations of the methods employed for benchmarking PILOT alongside competing methodologies. Our benchmarking approach is notably comprehensive, encompassing twelve different datasets and evaluating four to five competing methods through statistical assessment across three problem domains: clustering, distance measurement, and trajectory estimation. The outcomes of these evaluations consistently demonstrate the superior performance of PILOT's Wasserstein metric across all three problem domains. It is noteworthy that previous studies have often limited their analyses to exploratory evaluations on individual datasets, lacking the level of comprehensive benchmarking undertaken in this study.
3. Examination of Experimental Factors: We have conducted a thorough investigation into the impacts of batch correction, cluster/cell type resolution, and parameter choices used within the PILOT framework.
4. Enhancement of Text Description: We have enhanced the textual descriptions to provide a high-level overview of the PILOT methodology, along with justifications for the methodological decisions made.
5. Improvement of Code and GitHub Repository: To enhance accessibility and promote reproducibility, we have made improvements to the codebase and the associated GitHub repository.

In summary, PILOT stands as a distinctive and all-encompassing framework. It holds the unique distinction of being the sole method offering comprehensive tools for both clustering and trajectory analysis of samples within multiscale single-cell and pathomics data. Moreover, it incorporates statistical methodologies for the interpretation of results. The effectiveness of these tools has been thoroughly validated through the most extensive benchmarking study performed to date on sample-level analysis. The versatility of PILOT is demonstrated through its successful application in exploratory analyses of three distinct datasets: elucidating trajectories in myocardial infarction single-cell RNA-seq data, uncovering trajectories within pathomics data from kidney IgNA patients, and facilitating the clustering of pancreas adenocarcinoma samples. We firmly believe that these contributions hold significant value for the fields of bioinformatics, single-cell genomics, and pathology.

Reviewer #1 (Evidence, reproducibility and clarity):

The paper describes a computational method, PILOT, that uses optimal transport to compute the Wasserstein distance between two individual single-cell samples. It uses PILOT to detect sample (patient) level trajectories and clusters associated with diseases. The method was applied separately to single-cell genomics data and to digital pathology data. The method was applied to several datasets and compared against other tools.

Major comments:

The paper is not easy to follow and should be improved considerably to make it readable and reproducible. Consequently, I was not convinced that the PILOT method is much better than other methods.

We extend our appreciation to the reviewer for their valuable suggestion. We have further refined the manuscript by incorporating a comprehensive and high-level description of our method. This expansion encompasses methodological justifications and clarifications to enhance the overall clarity. Additionally, we wish to emphasize that, to the best of our knowledge, our benchmarking analysis stands as the most comprehensive within the current literature. The results of this analysis unequivocally demonstrate that PILOT surpasses all competing methods in at least one of the various computational analysis tasks, namely clustering, trajectory estimation, and distance evaluation.

Furthermore, we have undertaken significant enhancements in the codebase of PILOT, coupled with a reorganization of the associated GitHub repository. This effort includes the development of in-depth and improved tutorials that faithfully replicate the analyses conducted on datasets related to myocardial infarction, pancreas adenocarcinoma, and pancreas pathomics (https://pilot.readthedocs.io/en/latest/). This changes guarantee the reproducibility of the PILOT framework.

See below for specific changes and additional clarifications.

At first read of the title and abstract, I got the impression that the method analyzes single cell and pathomics data concurrently rather than separately. This should be fixed.

We have changed the text of the abstract and introduction to make clear that PILOT is either applied to single cell or pathomics data independently.

The usage of Wasserstein distance to compute distance between single-cell samples is elegant and is the main strength of this study. Given that PILOT is the main achievement, it should be described more carefully and in a detailed manner.

For example, in the first Results paragraph, "The test indicates for features explaining the predicted pseudotime by fitting either linear or quadratic models" - I could not understand this sentence. Also, which test do the authors refer to? A few sentences down, there is a reference to a Wald test, is that it?

PILOT has three major parts: (1) a method for measuring distance of samples with optimal transport; (2) an patient level unsupervised analysis part (clustering or trajectory analysis) and (3) a part for explaining predicted trajectories/clustering. The sentence mentioned before, refers to the interpretation approach after trajectory analysis. Here, we fit linear, quadratic or linear quadratic models to find association of predicted sample pseudo-time with data features (gene expression values in scRNA or morphological features in pathomics data). This fit can be done for all cells in the data or only for cells from a specific type. In the case of a cell specific fit, we use a Wald test to check if the cell type fit differs from all other cell types in the data, i.e. the gene is associated with the trajectory and the expression changes are specific to the cluster at hand.

While these details were found in the method section, we agree with the referee that they can be better introduced in the main manuscript. We have therefore improved the first subsection of the results and Figure 1 to reflect this.

One of the key aspects of the Wasserstein distance is the cost metric. The determination of the cost metric should be detailed as part of the Results. Have the authors considered and estimated other ways to define the distance?

This is an interesting question. Currently, PILOT uses the Cosine metric. In our revision, we evaluate other metrics (Euclidean, Manhattan, and Chebyshev). This benchmarking indicates that the Cosine and Manhattan performed best regarding the clustering problem (ARI), while Cosine was better than all metrics for the Silhouette statistic; and Cosine and Euclidean performed best regarding AUPR. Therefore, we adopt the Cosine metric in the paper. We include these results in the revised manuscript and in Sup. Fig. 5F-H.

Figure 1 provides a schematic view of PILOT. However, there is no explanation of the notation, which makes it confusing rather than helpful. Also, what is the relationship between J and j, if any?

We understand that the figure 1 was problematic, as it did not introduce the formulation. We have now improved the first sub-section of the results page and figure 1 to improve this.

The motivation and usage of adjusted Rand index (ARI) and Friedman-Nemenyi tests should be provided. Currently, they are not clear, including why those tests are suitable in the cases shown.

The adjusted Rand index is a well known metric to evaluate clustering results when labels are known. Among others this metric has many interesting features as it does not require an association of clusters with class labels. Moreover, it has a correction for random clustering solutions, therefore values lower than zero indicate poor solutions and values of 1 a perfect solution.

The Friedman-Nemenyi test allows us to compare the performance of several algorithms whenever evaluated in the same data sets. Here, the null hypothesis is that all algorithms have the same performance (same ARI statistic). The test is nonparametric and is based on the rank of the algorithm at each data set. This is important, as ARI values (or any other evaluation statistic) are data set specific, e.g. some clustering problems are more difficult than others. By evaluating the rank, the test indicates which methods perform relatively better than others. Moreover, it follows a rigorous statistical framework including correction for multiple testing. This test has an increasing adoption in the machine learning community (Demsar et al., JMLR, https://jmlr.org/papers/v7/demsar06a.html).

We have added phrases with these justifications in the main text (subsection Evaluation of patient-level clustering and trajectory analysis) and included a new section in the materials and methods with more information in the experimental design of the benchmarking analysis.

Fig. 2 the use of method colors should be constant across panels.

We have changed the colors of panels in figure 2A-C (and equivalent panels everywhere else) to avoid confusions.

The proportions method works at least as well as PILOT in 2B and 2C (silhouette and AUPR). Explain why PILOT is better.

The benchmarking analysis shows that PILOT has the highest ARI value (clustering performance) at absolute and ranking levels (Fig. 2A). Moreover the Friedman-Neymeni test indicates this PILOT has significantly higher ranking than all evaluated methods. Regarding Silhouette (distance evaluation) and AUPR (trajectory evaluation) both proportion and PILOT have similar absolute values (Fig. 2B and 2C; panel left), while PILOT has a superior ranking in both cases (Fig. 2B and 2C panel right). Friedman-Neymeni test indicates higher ranking of PILOT than PhEMD for Silhouette and higher ranking of PILOT than PhEMD and pseudo-Bulk regarding trajectory evaluation. The difference in the results on absolute and ranking values can be understood by looking at the statistics in table Table S1. PILOT has highest AUPR in 8 out 12 data sets; proportion has highest values in 5 (including 4 ties with PILOT); proportion-PHATE had 3 best results (including 3 ties with both PILOT and proportions), while PhEMD is best in one data set and Pseudo-bulk in 3 (including 1 tie with PILOT). Altogether, PILOT obtained a higher or equal AUCPR in 9 out of the 12 data sets. We have also changed Fig.2A, 2B and 2C to include all data points and to show the mean, as this provides a better visualization of the previously reported results.

Altogether, these results indicate that PILOT outperforms all competing methods in at least one of the evaluated problems (clustering, trajectory and distance estimation) and ranks favorably in all evaluated scenarios. We have changed the manuscript text to reflect these results.

Likewise, Figure 2C,D and Figures S1 and S2 don't show a clear and consistent advantage for PILOT over other methods. Explain what advantage of PILOT do the fraction panels highlight in Fig. 2E and Fig. S3. Fig. 2C is not mentioned in the text.

Figure 2D, 2E, and now figures S2 and S3 represent visualizations of the results, which were statistically evaluated in panels of Fig.2A-2C. As discussed in the previous point, PILOT does perform better than all methods for the clustering problem and performs better or as good as the proportion test on 9 of the 12 evaluated data sets in the trajectory problem. We also have improved the text to include references to all figures in the main text.

I assume Kidney IgAN (text) and Kidney IgA (fig. 2) are the same.

The correct name is IgAN and this has been corrected in Figure 2.

Fig. 3B fix the p-value notation (what is p=1.05E?) and R2 (R square?). Nrte tha both this problem also occurs in other figs. Fig. 3B shows the major cellular changes.

We now adopt the term “R-squared” in the figures. Also, the previous version did not display p-values properly. We apologize for this. This has been fixed now.

Are these changes consistent with known ones? Explain and provide references. Are there cell types that were expected to show a change and did not? Same questions for Fig. 3C wrt genes. Is this an exploratory analysis highlighting interesting candidate genes? If so, it should be described as such.

Cardiac remodeling after myocardial infarction is characterized by loss of cardiomyocytes, infiltration by immune cells (myeloid and lymphocytes) and increase in myofibroblast populations (doi.org/10.1038/s41392-022-00925-z;doi.org/10.3389/fcvm.2019.00026). PILOT indicates these populations, with the exception of lymphocytes, are most relevant at both clustering levels (see Sup. Fig, 6). Particularly important are results from the low granularity analysis, as this indicates particular macrophage/fibroblast sub-populations (SPP1+ Mac. and Myofibroblast) with increase in disease. PILOT could not detect changes in lymphocyte cells, but this is explained by the poor coverage of these cells in the data set (>3%). We have updated the main manuscript to reflect this.

We also explicitly mention that the analysis of genes and cells are exploratory analysis.

The point of Fig. S6 and its major findings should be mentioned in the text (or it can be removed).

We now make the reference to the gene ontology analysis presented in the new Figure S7 more explicit in the text.

Fig. 4B legend - eGFR not GFR. What do the high-low values of Fig. 2B refer to?

We have fixed these points.Hhigh and low values of panel 4B refer to the eGFR.

Fig. S12 is out of order in supp file.

This has been fixed.

AUCPR - explain.

The AUCPR stands for area under the curve of the precision recall (AUCPR) curve. We have now improved the explanation of the evaluation metric in the main text and methods section.

The github looks like work in progress with many internal comments (eg, add ,edit, etc). I could not find the tutorials.

We have removed all the comments, improved the repository organization and code. The tutorials are explicitly mentioned in the main github page (https://github.com/CostaLab/PILOT/) and in readthedocs webpage (https://pilot.readthedocs.io/). It include tutorials replicating analysis with trajectory inference and clustering problems, which are discussed in the manuscript.

In the process of code review, we have noticed that while we could replicate all the analysis, the procedure for selection of healthy cardiomyocyte genes was distinct (gene were ranked by regression model fit p-value) than the analysis of the myofibroblast genes (genes were ranked by the Wald test p-value). As explained before, the Wald test, which compares the expression of the regression model fits across samples, is a more appropriate criteria, as it finds cluster and trajectory specific genes. We have changed the analysis of the cardiomyocyte to make the gene selection to be based on the Wald-test p-value. New results recover other sarcomere related genes (MYBPC3 and MYOM1) as being dysregulated during disease progression. These findings are in accordance with observations made in the original study presenting the data (Kuppe et al. 2022). We have updated Fig.3 and respective genes accordingly.

Minor comments:

Introduction: "Alternatively, trajectory analysis can be performed to uncover disease progression allowing the characterization of early disease events." Citations should be added (some appear later in the text).

We included a reference to PhEMD.

"Currently, there are no analytical methods to compare two single cell experiments from the same tissue from two distinct individuals." There have been several comparisons among data from patients, (e.g. Cain et al, 2023), so the authors should be more careful/accurate in their statements.

We assume that the referee mentions https://www.nature.com/articles/s41593-023-01356-x. Indeed, we were not aware of this recently published study. The manuscript focuses on comparing cell proportion changes (estimated by deconvolution) between distinct phenotypes and does not provide any approach for sample level analysis of single cell data. This is in our view a different problem than the one addressed by PILOT or PhEMD. We refer to it in our manuscript, as its cell community based analysis is an interesting approach for the interpretation of PILOT results.

"Except for PhEMD, all related methods9, 11, 12 require labels of patients for their analysis and cannot be used in the unsupervised analysis " - this sentence comes immediately after describing ref 13, which can be used in unsupervised analysis and accordingly is not cited in this sentence. The authors did well in describing ref 13 (a bioRxiv paper), and its description should come after this sentence.

We changed the text to reflect this.

"These can be clusters", clustered?

Done.

" acquire an injury cell states" remove an.

Done.

"As for scRNA-seq, there is no analytical method which is able to compare two or more histological slides based on morphometric properties of their structures." The sentence seems to refer to pathomics, not to sc data as suggested in "As for scRNA-seq"

This has been rephrased.

"Thus PILOT represents the first approach to detect unknown patient trajectories and clusters" patient clusters were also observed by others (eg ref 13, Cain et al).

This has been rephrased.

Equation 7 - Cosine(Mi,Mi) should be Cosine(Mi,Mj)

Done.

In the beginning of the Results, PILOT is not referred to as a package but as a researcher ("PILOT explores").

This has been rephrased.

Reviewer #1 (Significance):

In general, the paper is a Methods paper. Hence, likely audience includes computational biologists interested in methodologies, not to biologists interested in the actual findings.

Although I am among the likely audience, I was not convinced by the merits of the method, potentially due to the way the paper was written.

I do not have sufficient expertise to check the math.

In this revision, we have significantly enhanced the text to incorporate high-level descriptions of methods tailored for non-computational experts. Additionally, we have refined the description of the benchmarking process, which, as far as our knowledge extends, stands as the most comprehensive in the literature. This comprehensive analysis strongly underscores the statistical superiority of PILOT when compared to other methods. Lastly, PILOT presents an unique framework, encompassing methods for trajectory analysis, clustering, and interpretation of sample-level analyses within the realm of multiscale single-cell genomics and pathomics data.

Reviewer #2 (Evidence, reproducibility and clarity):

Joodaki et al. propose PILOT, a computational method for analysing single-cell genomics and pathomics data. PILOT is a method that enable clustering, trajectory analysis, and feature detection at a patient level using scRNA-seq data. This is an important task and represent the growing application of scRNA-seq to understand diseases and other perturbations to other biological systems. In particular, PILOT enables unsupervised analysis which alleviate the need of patient labels required by many alternative methods. We have the following comments for the authors' consideration.

1. A key consideration in dealing with scRNA-seq data at a patient level is the batch effect in the data. Typically, each patient sample may be treated as a "batch" especially when they are processed separately to obtain a scRNA-seq dataset that are subsequently combined with scRNA-seq datasets from other patients to form a single dataset. Analysing these data without batch correction may lead to the identification of "cell types" and "states" that are driven by batch effect. In Figure 1. PILOT takes a clustered and integrated scRNA-seq data as input for analysis. I wonder how PILOT would behave if there is a strong batch effect in the data and how would the authors propose to handle them?

This is an interesting question. Currently, PILOT is using the batch procedure used in the paper proposing the original data. We evaluate now the impact of batch correction methods implemented in scanpy (Harmony, bknn and Scanorama). We focus here on single cell data, which we have access to the original count matrix (Lupus, COVID, and Diabetes). We observe no impact of the batch correction algorithm in these data sets (see Sup. Fig. 5C-E). These results are now included in the manuscript.

We have noticed however that strong batch effects in the lung cell atlas or the kidney cell atlas.For the lung cell atlas, we observed that single cell data measured from distinct techniques (Seq-well, Drop-seq, 10x 5’ and 10x 3’) or distinct tissue sampling approaches confounded results for all evaluated approaches. Therefore, we restricted the analysis to the technology with more samples (10x genomics 3’) and to lung tissues. This sample selection was previously described in the material and methods. Of note, the use of samples from distinct 10x genomic version kits (v1, v2 or v3) did not impact results. For the kidney cell atlas, we also observed a strong batch between single nuclei and single cell protocols. Here, we opted to focus on the largest cohort of single cell RNA experiments (see Review Fig. 1). Altogether, PILOT and other evaluated methods do require samples to be analyzed with an uniform technique and sampling approaches. We now include a brief discussion about this open point in the “Discussion” section. This is an important topic of future research.

Review Fig. 1. - Data of the Kidney Precision Medicine Project was measured using either single cell or single nucleus protocols. All evaluated methods were affected by the differences in these technologies and could not separate disease status in this data.

1. It appears that the Wasserstein distance (W) matrix of the samples was used for patient clustering and also trajectory analysis. However, most of the figures presented in the manuscript are for trajectory analysis. Since the patient clustering were performed prior to trajectory analysis, could the authors visualize the patient data based on the W before performing disease trajectory estimation?

Indeed, despite the clustering-based analysis (ARI statistics; Fig. 2A) the current manuscript focuses on results of the trajectory analysis. We now include additional features for clustering analysis. This includes heatmap visualizations of the OT distance matrices together with Leiden clustering (Sup. Fig. 1). See points 4 and 5 below for further changes regarding clustering analysis.

1. In trajectory analysis in figure 2D and E, why not use Multi-scale PHATE which appears to be specifically designed for trajectory analysis? The authors also mentioned SCANCell. While these methods require labels of patients for their analysis, it would be interesting to know how well they perform in comparison to PILOT if such information is available.

This is an interesting point. Multiscale-PHATE is based on doing a multi-resolution clustering of the cells. It then applies PHATE (instead of diffusion map) to find a non-linear embedding on the cell proportions across samples and resolutions. While this analysis is presented at Multiscale-PHATE manuscript (Fig. 5), we could not find any code or functionality in their github to replicate this (https://github.com/KrishnaswamyLab/Multiscale_PHATE). Moreover, we were not able to find a function to find the cluster/resolution associations of cells to reimplement the above mentioned analysis following the descriptions of the manuscript. We also contacted authors, but obtained no reply. It is also important to state that Multi-PHATE used a supervised filter to select cell types for further analysis.

Alternatively, we now include an evaluation of the use of cell proportions followed by a PHATE embedding in the trajectory based evaluation, which is close to the method proposed in Multiscale-PHATE. Our benchmarking indicates that Multiscale-PHATE is the third best ranked method being overpassed by proportion and PILOT. Regarding SCANCell, it focuses on the interpretation of cell communities and it uses embedding/distances by exploring PhEMD. Therefore, its performance in the trajectory or clustering performance problem is the same as PhEMD. We refer to these points in the text now.

1. The current design of PILOT appears to assume that there is always a "smooth" trajectory in the data. Is this going to be the case in reality? What if we have a well separated and distinct groupings of the patients and controls data? In the latter case, imposing a trajectory seems artificial. I am also not sure how meaningful the trajectory analysis would be if, biologically, such a smooth transition is not present in the data.

The EMD based distance can be used both for clustering or trajectory analysis. Also, PILOT performed quite well in the clustering problem benchmarking (Fig. 2A). The choice of application lies on the problem at hand. In our view, both the kidney pathomics and the myocardial infarction data (explored in Fig. 3 and Fig. 4) represent medical data with potential disease trajectories. We now expand the PILOT framework to include new visualizations and statistical methods to improve the interpretation of the clusterings (see point 2; Fig. S1; and point 5 and new Fig. 5).

1. The feature analysis is also built on trajectory analysis using regression models. Again, how would this work out if there isn't a smooth trajectory/transition in the data (e.g. the data are obtained from a discrete case-control study)?

We expanded the PILOT framework to also include statistical tests for accessing changes in cell populations and markers for the clustering problem. First, we use a Welch’s t-test to evaluate cell proportion changes associated with detected clusters. Next, we use a differential analysis test from limma to find genes within a cluster, whose gene expression is changing between the two groups of samples for a given cluster of cells. While these are standard approaches in the literature, this further improves the functionality of PILOT as a general framework for patient level analysis. This is now described in PILOT manuscript (Results subsection “Patient level distance with Optimal Transport” and methods).

We also include in the manuscript an explorative analysis of a sub-cluster found in the PDAC data. This analysis could find a population of PDAC patients displaying higher levels of malignant cells and marked by both increase in hypoxia and fibrosis pathways. This example highlights how PILOT can be used to find potentially interesting groups of samples. These are implemented in the main manuscript (Fig. 5). We also include a new tutorial of PILOT with this analysis (see https://pilot.readthedocs.io/).

1. It is not clear from the formulation of PILOT (and also Figure 1) if the cell type labels is required/used or the cluster id of a clustering algorithm was used instead. The author also mentioned that the clustering output does not have much impact on the downstream analysis. I wonder why and if so can we group the data in any way we want for downstream analysis? This can be useful when one would like to focus on certain grouping of cells.

Clustering at the cells (or structure level) is required. For the benchmarking analysis, we have used the cell annotation reported in the original paper, which were derived via clustering analysis. The use of annotated clusters is crucial for interpretation. We also included in the original manuscript an analysis on the impact of the clustering resolution of the Leiden algorithm. This indicates that the change in resolution did not have a high impact in the clustering (ARI) of the samples (Sup. Fig. 5A-B). However, this analysis could not consider any interpretation of results, as cluster labels were not present.

We believe, however, that the granularity of the clustering will impact the interpretation of the sample analysis. To investigate this, we evaluate how using higher level annotation/clustering of the heart myocardial infarction (also reported in Kuppe et al. 2022) impacts our ability to find cell specific changes. We observe similar changes whenever using low resolution clustering (decrease of cardiomyocytes, increase in fibroblasts and myeloid cells). However, this analysis loses a lot of important nuances found in the high resolution clustering (see Sup. Fig. 6). For example, it does not recover the fact that damaged cardiomyocyte populations have a slower decay than healthy myocytes. Or the fact that myofibroblasts has an increase in the latter disease trajectory stage, while progenitor fibroblast cells (Fibro_Scara5) have an increase previous to myofibroblasts. These results show how low resolution clustering can lead to loss of interesting information contained in cellular sub-states or cell sub-populations. This is now discussed in the results subsection ‘PILOT trajectories detect events associated with cardiac remodeling in myocardial infarction’.

Reviewer #2 (Significance):

PILOT is designed for analyzing scRNA-seq data at a patient level. There is a growing application of scRNA-seq to diseases and the development of computational tools for analyzing such data at phenotype level is critical. The key aspect of PILOT compared to other currently available tools is that it enables unsupervised analysis which alleviate the need of patient labels required by many alternative methods.

Thanks for this very positive feedback and constructive comments.

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

Joodaki et al. propose PILOT, a computational method for analysing single-cell genomics and pathomics data. PILOT is a method that enable clustering, trajectory analysis, and feature detection at a patient level using scRNA-seq data. This is an important task and represent the growing application of scRNA-seq to understand diseases and other perturbations to other biological systems. In particular, PILOT enables unsupervised analysis which alleviate the need of patient labels required by many alternative methods. We have the following comments for the authors' consideration.

1. A key consideration in dealing with scRNA-seq data at a patient level is the batch effect in the data. Typically, each patient sample may be treated as a "batch" especially when they are processed separately to obtain a scRNA-seq dataset that are subsequently combined with scRNA-seq datasets from other patients to form a single dataset. Analysing these data without batch correction may lead to the identification of "cell types" and "states" that are driven by batch effect. In Figure 1. PILOT takes a clustered and integrated scRNA-seq data as input for analysis. I wonder how PILOT would behave if there is a strong batch effect in the data and how would the authors propose to handle them?
2. It appears that the Wasserstein distance (W) matrix of the samples was used for patient clustering and also trajectory analysis. However, most of the figures presented in the manuscript are for trajectory analysis. Since the patient clustering were performed prior to trajectory analysis, could the authors visualize the patient data based on the W before performing disease trajectory estimation?
3. In trajectory analysis in figure 2D and E, why not use Multi-scale PHATE which appears to be specifically designed for trajectory analysis? The authors also mentioned SCANCell. While these methods require labels of patients for their analysis, it would be interesting to know how well they perform in comparison to PILOT if such information is available.
4. The current design of PILOT appears to assume that there is always a "smooth" trajectory in the data. Is this going to be the case in reality? What if we have a well separated and distinct groupings of the patients and controls data? In the latter case, imposing a trajectory seems artificial. I am also not sure how meaningful the trajectory analysis would be if, biologically, such a smooth transition is not present in the data.
5. The feature analysis is also built on trajectory analysis using regression models. Again, how would this work out if there isn't a smooth trajectory/transition in the data (e.g. the data are obtained from a discrete case-control study)?
6. It is not clear from the formulation of PILOT (and also Figure 1) if the cell type labels is required/used or the cluster id of a clustering algorithm was used instead. The author also mentioned that the clustering output does not have much impact on the downstream analysis. I wonder why and if so can we group the data in any way we want for downstream analysis? This can be useful when one would like to focus on certain grouping of cells.

Significance

PILOT is designed for analysing scRNA-seq data at a patient level. There is a growing application of scRNA-seq to diseases and the development of computational tools for analysing such data at phenotype level is critical. The key aspect of PILOT compared to other currently available tools is that it enables unsupervised analysis which alleviate the need of patient labels required by many alternative methods.

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 paper describes a computational method, PILOT, that uses optimal transport to compute the Wasserstein distance between two individual single-cell samples. It uses PILOT to detect sample (patient) level trajectories and clusters associated with diseases. The method was applied separately to single-cell genomics data and to digital pathology data. The method was applied to several datasets and compared against other tools.

Major comments:

The paper is not easy to follow and should be improved considerably to make it readable and reproducible. Consequently, I was not convinced that the PILOT method is much better than other methods.

At first read of the title and abstract, I got the impression that the method analyzes single cell and pathomics data concurrently rather than separately. This should be fixed.

The usage of Wasserstein distance to compute distance between single-cell samples is elegant and is the main strength of this study. Given that PILOT is the main achievement, it should be described more carefully and in a detailed manner.

For example, in the first Results paragraph, "The test indicates for features explaining the predicted pseudotime by fitting either linear or quadratic models" - I could not understand this sentence. Also, which test do the authors refer to? A few sentences down, there is a reference to a Wald test, is that it?<br /> One of the key aspects of the Wasserstein distance is the cost metric. The determination of the cost metric should be detailed as part of the Results. Have the authors considered and estimated other ways to define the distance?

Figure 1 provides a schematic view of PILOT. However, there is no explanation of the notation, which makes it confusing rather than helpful. Also, what is the relationship between J and j, if any?

The motivation and usage of adjusted Rand index (ARI) and Friedman-Nemenyi tests should be provided. Currently, they are not clear, including why those tests are suitable in the cases shown.

Fig. 2 the use of method colors should be constant across panels. The proportions method works at least as well as PILOT in 2B and 2C (silhouette and AUPR). Explain why PILOT is better. Likewise, Figure 2C,D and Figures S1 and S2 don't show a clear and consistent advantage for PILOT over other methods. Explain what advantage of PILOT do the fraction panels highlight in Fig. 2E and Fig. S3. Fig. 2C is not mentioned in the text.

I assume Kidney IgAN (text) and Kidney IgA (fig. 2) are the same.

Fig. 3B fix the p-value notation (what is p=1.05E?) and R2 (R square?). Norte tha both this problem also occurs in other figs. Fig. 3B shows the major cellular changes. Are these changes consistent with known ones? Explain and provide references. Are there cell types that were expected to show a change and did not?<br /> Same questions for Fig. 3C wrt genes. Is this an exploratory analysis highlighting interesting candidate genes? If so, it should be described as such.<br /> The point of Fig. S6 and its major findings should be mentioned in the text (or it can be removed).

Fig. 4B legend - eGFR not GFR. What do the high-low values of Fig. 2B refer to?<br /> Fig. S12 is out of order in supp file.

AUCPR - explain.

The github looks like work in progress with many internal comments (eg, add ,edit, etc). I could not find the tutorials.

Minor comments:

Introduction: "Alternatively, trajectory analysis can be performed to uncover disease progression allowing the characterization of early disease events." Citations should be added (some appear later in the text).<br /> "Currently, there are no analytical methods to compare two single cell experiments from the same tissue from two distinct individuals." There have been several comparisons among data from patients, (e.g. Cain et al, 2023), so the authors should be more careful/accurate in their statements.<br /> "Except for PhEMD, all related methods9, 11, 12 require labels of patients for their analysis and cannot be used in the unsupervised analysis " - this sentence comes immediately after describing ref 13, which can be used in unsupervised analysis and accordingly is not cited in this sentence. The authors did well in describing ref 13 (a bioRxiv paper), and its description should come after this sentence.

"These can be clusters", clustered?

" acquire an injury cell states" remove an.

"As for scRNA-seq, there is no analytical method which is able to compare two or more histological slides based on morphometric properties of their structures." The sentence seems to refer to pathomics, not to sc data as suggested in "As for scRNA-seq"

"Thus PILOT represents the first approach to detect unknown patient trajectories and clusters" patient clusters were also observed by others (eg ref 13, Cain et al).

Equation 7 - Cosine(Mi,Mi) should be Cosine(Mi,Mj)

In the beginning of the Results, PILOT is not referred to as a package but as a researcher ("PILOT explores").

Significance

In general, the paper is a Methods paper. Hence, likely audience includes computational biologists interested in methodologies, not to biologists interested in the actual findings.

Although I am among the likely audience, I was not convinced by the merits of the method, potentially due to the way the paper was written.

I do not have sufficient expertise to check the math.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:<br /> In this study, the authors delineate the association of paralog dispensability with the frequency of homozygous deletions (HDs) and thereby show that paralog dispensability can play a significant role in shaping tumor genomes. The authors analyzed the strength of negative selection on the paralogs relative to the singletons using frequencies of the homozygous deletions (HD). The study focused on HDs because they ensure a complete loss of function, unlike other mutational aberrations that can be masked because of haplo-sufficiency. While accounting for potential confounding factors, authors find that paralogs tend to have a relatively high frequency of HDs, suggesting a relaxed negative selection. Furthermore, the authors specifically attribute this association to the dispensable paralogs by analyzing gene inactivation data generated from multiple experimental systems. Overall, the findings of this study can potentially have significant implications in cancer biology field and specifically to the researchers studying cancer genome evolution.

We thank the reviewer for the careful reading and positive assessment of our manuscript

Major comments:

1. To dissect further which dispensable paralogs are more likely to be associated with a high HD frequency, synthetic lethal paralogs could be compared with non-synthetic lethal ones.

In the section titled 'Homozygous deletion frequency of paralog passengers is influenced by paralog properties' (begins from line #289), authors have shown that paralogs with a high frequency of HDs are more likely to have the properties of dispensability (in Figure 4). It seems that all of those properties are also associated with synthetic lethality as the authors identified in their previous study (DeKegel et al. 2021). Furthermore, as shown in the subsequent section ('Essential paralogs are less frequently homozygously deleted than non-essential paralogs', begins from line #344), the high HD is associated with the dispensable paralogs. Some of those dispensable paralogs are expected to be synthetic lethal. Therefore, the association of paralogs with a high frequency of HDs with experimentally validated or predicted sets of synthetic lethal paralogs could be tested. This may help authors to contextualize their findings in terms of genetic interactions between paralogs.

We thank the reviewer for highlighting the potential relationship with our previous work. We agree that many of these properties are associated with synthetic lethality, but we note that they are also associated with single gene essentiality. This makes the relationship between synthetic lethality, essentiality, and deletion frequency somewhat difficult to dissect.

Nonetheless we have tested, in a number of ways, whether there is a relationship between a paralog having a reported/predicted synthetic lethality and being homozygously deleted. We find no obvious connection between the two.

We first tested using a set of synthetic lethal interactions identified by integrating molecular profiling data with genome wide CRISPR screens in a large panel of cancer cell lines (the data used to train the classifier in De Kegel et al, 2021). As there is an ascertainment bias in this dataset (paralogs must have frequent loss of function alterations / silencing to be tested) we restricted our analysis to only those paralog pairs tested for synthetic lethality. We identified no clear pattern (p>0.05, Fisher's Exact Test).

We next tested using an integrated set of four combinatorial CRISPR screens (aggregated in De Kegel et al) where we considered a pair to be synthetic lethal if it was a hit in any screen and not synthetic lethal if it was screened at least once and never identified as a hit. Again we restricted our analysis to paralogs that were present in this dataset to prevent issues with ascertainment bias. We found no clear association.

We further tested using a consensus dataset derived from the same combinatorial screens, where a pair were marked as synthetic lethal if they were identified as a hit in at least two screens and not synthetic lethal if they were screened at least twice and never identified as a hit. Again we restricted our analysis to paralogs that were present in this dataset and found no clear association.

We finally tested using our predicted synthetic lethal interactions – annotating the top 3% of predictions as synthetic lethal and the remainder as non-synthetic lethal. The 3% threshold is similar to the observed frequency of synthetic lethality in the training set. In this case, as this dataset covers all paralogs considered, no restriction was necessary.

None of the above analyses revealed a clear relationship between deletion frequency and synthetic lethality. A caveat of these analyses is that none of the experimental datasets are complete (covering only a minority of all paralog pairs) and they are all somewhat noisy. Furthermore, as we show in our modelling analysis (Fig S3) the observed homozygous deletions are far from saturating.

However we think there may be a simpler explanation, beyond limitations of the data, for why we do not observe a relationship between HDs and synthetic lethality.

As the reviewer notes, there is evidence in cell lines that one reason paralogs are more dispensable than singletons is because of buffering / redundant relationships as revealed by synthetic lethal interactions. These relationships therefore provide an explanation for why some paralogs are dispensable. As our primary claim is that paralogs are more frequently deleted because they are more dispensable we might anticipate a relationship between deletion frequency and synthetic lethality. However, by definition, synthetic lethal interactions can only be observed for non-essential (dispensable) genes. Therefore when analysing the overlap with synthetic lethal interactions we are primarily restricting our analyses to genes that are already individually dispensable. Consequently we might not anticipate observing any enrichment. The buffering relationship revealed by synthetic lethality provides an explanation for why a paralog is dispensable but once we are restricting our analysis to dispensable paralogs we do not necessarily expect to see further enrichment.

We think that an ideal way to explore this question further would be to look at selection on deletions of pairs of paralogs – we anticipate that if a gene is dispensable because of paralog buffering then both paralogs should not be deleted simultaneously. However, the current copy number datasets are too small to evaluate such pairwise relationships. This is discussed in manuscript as follows:

Analyzing the frequency with which two members of a paralog family are lost would provide more direct insight into the contribution of paralog redundancy, but due to the overall rarity of passenger gene HDs, we cannot make a comprehensive assessment of co-deletions here – e.g. among paralog pairs where both genes are non-drivers, and not on the same chromosome, only two pairs are co-deleted in at least one TCGA sample. Larger cohorts would also allow us to search for patterns of mutual exclusivity of HDs to identify genetic interactions – this has been applied for identifying interactions between driver genes [57,58]__, but is more challenging for interactions between non-driver genes, which are much less frequently altered.

Minor comments:<br /> 1. The number of TCGA and ICGC tumor samples analyzed:<br /> As mentioned in the Results section (line #106), 9966 tumor samples were analyzed. However, the sample size mentioned in Figure 2A is 9951. Is the lower number shown in the figure due to the filtering procedure mentioned in the Methods section (line #455)? The change in sample sizes could be explained. A similar difference in sample sizes exists for the ICGC data also.

The difference was indeed due to filtering process, but numbers were only provided in the methods. We have now addressed this in the main text :

After removing a small number of ‘hyper-deleted’ samples (see Methods) we retained 9,951 samples for further analysis.

1. The rationale behind setting the threshold at 100 HD genes to classify 'hyper-deleted' samples for TCGA (line #462) and ICGC data (line #473) could be explained.

We excluded hyper-deleted samples to avoid any individual sample having undue influence on the genes observed to be ever deleted or indeed to influence the overall patterns observed. It is also common in analyses of selection in tumours that make use of mutational profiles (rather than copy number profiles) to exclude hypermutated samples (e.g. Martincorena et al, Cell 2017; Lopez et al, Nature 2020). However the exact threshold of 100 samples was somewhat arbitrary and this query prompted us to assess whether it had any significant impact on the results.

We therefore repeated all analyses using a more stringent threshold (50 samples) and also without thresholding. Although the exact percentages and odds-ratios vary somewhat with the different thresholds, all major conclusions are still supported.

We appreciate that this was minor comment and that reviewer did not request this new analysis, but in the absence of a strong justification for a single threshold we felt it appropriate to assess multiple thresholds (and none).

1. Citation for DepMap is missing (caption of Figure 5). We have added the text below to the legend for Figure 5 :

Essential genes for the DepMap dataset (Meyers et al, 2017) are obtained from a version of the data reprocessed in (De Kegel et al, 2021) to reduce off-target sgRNA effects (see Methods).

CROSS-CONSULTATION COMMENTS<br /> Along the lines of Reviewer #3's second major comment, I have a suggestion, the possible benefits of which would depend on the target audience to which the authors intend to communicate their study.

I would suggest including a brief comparison of the findings of this study which deal with human paralogs, with the findings in model organisms such as yeast, perhaps in the discussion section. To facilitate such a comparison, authors could try measuring the enrichments of, for example, molecular functions, gene families, types of genetic interactions, etc., among the paralogs associated with a high frequency of HDs and then discussing their comparison with what is known in the literature for paralogs in other model organisms that tend to be frequently deleted.

Such a comparison could be of interest to the community of researchers working on other model organisms and put this study in a much broader context. However, as I said before, this would depend on the authors' intended target audience.

We thank the reviewer for the suggestion. We have added an additional section to the discussion highlighting differences and similarities to the observations from yeast as follows:

Much of our understanding of the factors that influence gene dispensability comes from studies in model organisms, in particular the budding yeast Saccharomyces cerevisiae [3,9,10,43,44]__. Analyses of the yeast gene deletion collection, a set of gene deletion mutants systematically generated in a single S. cerevisiae strain, revealed that paralogs were less likely to be essential than singleton genes [3,45]__. Furthermore, more detailed analyses of yeast paralogs revealed that paralogs from large families were less likely to be essential as were genes with highly sequence similar paralogs [43,44]__. Previous analyses, including our own, demonstrated that many of these trends are also evident when analyzing gene essentiality from CRISPR screens in cancer cell lines [12,13,15,35]__. Our results here are also consistent with these findings – many of the features that are associated with paralog dispensability in yeast are also associated with gene deletion frequency in tumor genomes.

The connection between the budding yeast observations and those in cancer is less clear when it comes to the relative dispensability of WGDs and SSDs. Analyses of the yeast gene deletion collection revealed that SSDs are more likely to be essential than WGDs in the single genetic background studied [43,44]__. In our previous analyses of gene essentiality in hundreds of cancer cell lines we found that SSDs were more likely to be broadly essential (essential in most cell lines) than WGDs but that WGDs were less likely to be never essential (i.e. more likely to be essential in at least one cell line)__[13]__. As the analyses of gene essentiality in budding yeast were generated in a single genetic background the concordance with our cancer cell line results was difficult to assess, but as gene deletion collections are now being generated in additional yeast strains it should become possible to perform a more direct comparison__[46–48]__.

Here we found that WGDs are less likely to be deleted than SSDs in tumors. This is surprising in light of the yeast gene deletion collection results, where SSDs were more likely to be essential than WGDs in the strain studied, but less so in light of the cancer cell line results, where WGDs were less likely to be never essential. It is also worth noting that experimental evolution studies in yeast found that SSDs accumulate protein-altering mutations at a higher rate than WGDs [49,50]__. These results are perhaps especially relevant when analyzing the influence of paralog features on selection in tumors.

We note that there are many additional differences in the features of WGDs and SSDs in budding yeast that may alter their relative dispensability in tumors. An obvious large scale difference is that in the ancestor of humans there were two rounds of whole genome duplication compared to a single duplication event in yeast__[51,52]__. Less obvious, but potentially of importance for cancer, is that the two classes of paralogs are enriched in pathways in humans that do not have obvious counterparts in yeast. For example, WGDs are highly enriched in signaling pathways involved in development while SSDs are enriched in immune response genes__[53]__. How the membership of these pathways influences the dispensability and selection of genes in tumors and cancer cell lines warrants further study.

Reviewer #1 (Significance):

As the authors note in their manuscript, it is expected that paralog dispensability could be associated with the relaxed negative selection in tumor genomes because (1) paralogs are prevalent in the human genome, and (2) many of them are dispensable, as apparent from the large-scale gene inactivation screens in hundreds of cancer cell lines (Blomen et al. 2015, Wang et al. 2015, Dandage and Landry 2019, De Kegel and Ryan 2019). However, direct mapping of this association, while importantly accounting for potential confounding factors, has been lacking.<br /> As a researcher with prior experience in the research topics such as gene duplication and genetic interactions, it appears to me that this study presents formal proof of the important association between paralog dispensability and tumor genome evolution which could be of major implication for the research community of cancer biology field and specifically to the researchers dealing with the topics such as cancer evolution, copy number alterations in cancer genomes, and synthetic lethality-based precision oncology therapeutics.

Thank you again for the positive assessment.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary

Here, De Kegel & Ryan analyse thousands of tumour samples from the TCGA and ICGC projects to identify homozygously deleted genes, finding that about 40% of protein-coding genes are deleted in at least one sample. They find homozygously deleted genes to be enriched for paralogous genes, and further, more frequently deleted genes are increasingly likely to be paralogs. The authors then test the influence of several factors on the likelihood of being deleted, including gene length, distance to a fragile site or chromosomal region, and distance to a recurrently deleted tumour suppressor gene (TSG). They find that proximity of a TSG, telomere, centromere, and fragile site all increase likelihood of being deleted in a sample, as does gene length. Having a paralog also remains an important predictor of deletion after accounting for these other factors. Additionally, the more similar in sequence the closest paralog is to the gene and having a larger gene family size are also predictive of deletion. Conversely, if a gene is a whole genome duplicate as opposed to a small-scale duplicate, it is less likely to be deleted. Finally, the authors test the hypothesis that paralogs that are deleted in cancer are less likely to be essential and find that this is indeed the case.

Comments

The authors have done a good job of identifying trends of paralog deletion in cancer samples and the factors influencing them. The results are well described and presented and support the conclusions. I like the inclusion of the saturation analysis as an estimate of what to expect given current and potential future sample sizes, and I appreciate the inclusion of a WGD/SSD paralog distinction. The data and methods are sufficiently detailed. I have a few minor comments below.

We thank the reviewer for the careful reading and positive assessment of our manuscript

1. Around line 160 in the text and supplemental figure 4A, the authors test if the trends they see are observed across individual cancer types. With 9 of 33 cancer types reaching a sample size threshold, 8 of 9 comparisons are significant. The authors do not state correcting for multiple testing.

We have now also assessed the significance of the results after performing a Holm-Bonferroni correction for multiple hypothesis testing and find that all 8/9 cancer types remain significant.

1. I initially misunderstood the hemizygously deletion analysis, thinking the analysis in supplement figure 4B/C was asking if a sample has any singleton or any paralog deleted and comparing the number of samples with any deletion of either - given the number of genes deleted per sample this wouldn't make sense as a good test. I think the authors are actually comparing the number of loss-of-hemizygosity events per gene and grouping by paralog/singleton. I think this is a good analysis, but I think it would be helpful to clarify this in the text and figure legend e.g. "Samples w/ gene LOH" could be "LOH events per gene" or something similar.

As suggested we have now updated the y-axis label in these charts to ‘LOH events per gene’. We note that there are now two additional panels in this figure to address copy neutral LOH, per Reviewer 3’s request.

1. Occasionally, I wanted some more detail in the text for context, which was sometimes later provided - e.g. I noted when reading about line 125 that I was curious at this point how often TSGs occurred on segments, and this was later provided on line 241. Similarly, around line 114 I was curious how many genes are typically deleted per HD segment, for which the median value was provided on line 206 (and distribution in supplemental figure 1), and again for hemizygous deletions. I think sometimes it would be helpful to provide this context earlier in the text to aid interpretation of the results.

We thank the reviewer for these suggestions which we have now incorporated into the text.

On line 115 (previously 114) the relevant sentence now reads:

Typically an HD that results in the loss of a protein coding gene also results in the loss of several chromosomally adjacent genes – in the TCGA dataset a median of three genes are lost per gene-deleting HD segment

On line 124 the relevant sentence now reads:

We found that almost half (49%) of the HDs that result in the loss of at least one protein coding gene overlap a known tumor suppressor.

1. In the discussion, on line 420, the authors include the point that a paralog might not be required at all in a tumour cell and therefore easily deleted. I think this possibility could be expanded on here and in the introduction/results section, as it is an important point. I think it would be helpful to include more about the possibility that a paralog might be deleted in a tumour cell because it is simply not required or that is more likely to have less of a phenotypic impact compared to a singleton, and that this could be a reason for the observed enrichment of paralogs in deleted genes. A citation to support this point could be Áine N O'Toole, Laurence D Hurst, Aoife McLysaght, Faster Evolving Primate Genes Are More Likely to Duplicate, Molecular Biology and Evolution, Volume 35, Issue 1, January 2018, Pages 107-118, https://doi.org/10.1093/molbev/msx270. Duplicate genes can be duplicates because copy number variation of them has minimal impact.

We thank the reviewer for raising this important point.

We have briefly addressed this in the introduction as follows:

In multiple model organisms, paralogs have been demonstrated to be more dispensable than singletons (genes without a paralog) [3–5]__. There are a number of reasons for why a paralog might be more dispensable than a singleton gene, including preferential retention of duplications of non-essential genes [6,7]__, but perhaps the most obvious explanation is buffering between paralogs.

Where references 6 and 7 are as follows:

1. O’Toole ÁN, Hurst LD, McLysaght A. Faster Evolving Primate Genes Are More Likely to Duplicate. Mol Biol Evol. 2018;35: 107–118.
2. He X, Zhang J. Higher duplicability of less important genes in yeast genomes. Mol Biol Evol. 2006;23: 144–151.

We discuss this more comprehensively in the discussion as follows:

In both yeast and cancer there are a number of reasons for why paralogs might be more dispensable than singleton genes. Perhaps the most obvious is the existence of buffering relationships between paralog pairs, such that when one paralog is lost the other paralog can compensate for this loss. Such buffering relationships between paralogs can be revealed through synthetic lethality screens and a number of recurrently deleted paralogs in cancer have already been reported to display synthetic lethal interactions with their paralog (recently reviewed in [54]__). Supporting this model, in previous work analysing essentiality in cancer cell lines we found that buffering relationships between paralogs could explain 13-17% of cases where a paralog was essential in some cell lines but not others__[13]__. This suggests that at least some of the increased dispensability of paralogs in cancer cells can be attributed to buffering relationships between paralog pairs. However this is not the only explanation for paralogs displaying increased dispensability in tumour cells. An additional explanation is that paralogs may perform essential functions in specific contexts (e.g. within specific tissues or at specific developmental stages) but are not required within the specific context of a tumour. Consistent with this model, human paralogs are more likely to display tissue-specific expression patterns [55]__. Finally we note that there is evidence to suggest that genes whose perturbation has a lower phenotypic impact may more ‘duplicable’ – i.e. rather than paralogs being under weaker selection because they are duplicated, their duplication was tolerated because they were already under weaker selection__[6,7]__. Teasing apart the relative contributions of these factors to the increased dispensability of paralogs in cancer will require further research and potentially new data resources such as gene essentiality profiles in diverse non-cancer cell types [56]__.

CROSS-CONSULTATION COMMENTS<br /> I agree, that's a helpful suggestion from reviewer 1.

Reviewer 3's suggestion regarding age of the two whole genome duplication events is quite difficult to unpick as the duplication events seem to have happened relatively close in time to each other while rediploidisation of the first was occurring. Additionally, paralogs from SSDs tend to be more similar in sequence simply because the two WGD events are relatively old while SSDs can occur at any time up to present. They're therefore biased by young duplicates that have not had the opportunity to diverged much and decrease in sequence similarity.

We appreciate these comments.

Reviewer #2 (Significance):

This is a novel study as it examines the frequency of paralog deletion in cancer samples and the factors influencing it, building upon work already conducted in cancer cell lines. This study extends the knowledge of the field confirming previous trends observed in cell lines, this time in actual cancer samples. It confirms that paralogs are more dispensable than singletons, likely because they have a similar counterpart that can provide some level of functional redundancy. The more similar the closest paralog, the more likely it is to be deleted provides support for this.<br /> It is certainly limited by the number of samples currently available in the two cancer sample projects included but the authors attempt to quantify how limiting this sample size is by conducting a saturation analysis using down-sampling to estimate how many gene deletions one can expect from different numbers of samples. This is important as the lack of observance of many gene deletions is likely due to the limited sample size and not due to negative selection. This low observance of gene deletions disappointingly limits further testing beyond single paralogs to consider the deletion effects of multiple gene family members and more directly test evidence of functional redundancy between paralogs. The authors provide a good discussion of the limitations of their study.

The results are of interest to evolutionary biologists and cancer biologists. Those with an interest in duplicate genes, and/or factors affecting gene loss in tumours will be interested in this work.

My field of expertise is molecular evolution, gene duplication and copy number variation.

We thank the reviewer for the positive assessment of the significance of our work.

Reviewer #3 (Evidence, reproducibility and clarity):

Thank you review "Paralog dispensability shapes homozygous deletion patterns in tumor genomes" by DeKegel et al. This manuscript uses TCGA and ICGC tumor data to show evidence for paralog dispensability. They analyze the rate of homozygous deletions and show that it is higher for paralogs compared to singletons. Their findings are robust to a number of confounding variables that they take into account e.g. distance to tumor suppressor, telomere, centromere or fragile site. They show that paralogs that belong to large families and have higher sequence identity tend to show more dispensability and these dispensable paralogs are less likely to be WGD.

We thank the reviewer for the time taken to review our manuscript.

Major comments.<br /> 1. Does the finding pertaining to lack of enrichment of paralogs in regions LOH take into account whether LOH is copy neutral or not i.e. how does dosage affects this finding? Is it possible that there is a difference in paralog rate in LOH that results in total copy 1 and that the presence of copy neutral LOH masks the effect? Also, Integration of gene expression dataset would be helpful to resolve the difference between dosage paralog that compensate of the lack of their sister by upregulating their gene expression.

In the submitted manuscript we focussed solely on LOH events where the copy number of one allele was 0 and the other allele was ≥1. These include copy loss events (total copy number = 1), copy neutral events (total copy = 2), as well as amplifications (total copy number > 2). The rationale for this approach was that we were interested in understanding whether the mechanism that was generating deletions was preferentially generating deletions in paralog-rich regions.

However, we agree that understanding the influence of dosage is of interest here. We have therefore expanded the analysis in the paper to separately assess the enrichment of paralogs in copy neutral LOH regions (total copy number = 2) and copy loss LOH regions (total copy number = 1).

As shown in the new updated Figure S4B we do not find an enrichment of paralogs in genes subject to either copy neutral LOH or copy loss LOH.

The relevant section of the text on page 6 now reads :

We do not find that paralogs are more frequently subject to LOH than singletons in either the TCGA or ICGC cohort (Fig. S4B-C); when considering all LOH segments we even see that singletons are slightly more frequently subject to LOH in the ICGC cohort (Fig. S4C, left), but when considering only focal LOH segments – i.e. segments whose length is less than half of the chromosome arm’s length, which is the case for all HD segments – there is no significant difference between paralog and singleton LOH frequency in either cohort. To assess whether gene dosage influenced the observed LOH frequency we further restricted our analysis to copy neutral LOH events (total copy number = 2) and copy loss LOH events (total copy number = 1) and again found no significant increase in deletion frequency of paralogs compared to singletons (Fig. S4B-C).

Regarding the integration of gene expression to identify dosage compensation between paralogs – we agree that this is extremely interesting. However, it is quite challenging to address properly. Most paralogs are only observed to be homozygously deleted a single time and so statistically identifying how loss of one gene impacts the mRNA abundance of another is challenging. In the minority of cases where a paralog is recurrently deleted, often these deletions occur in samples from different cancer types and so integrating transcriptomic data still presents some technical challenges. Given this complexity, and as the question of dosage compensation is not central to our key observations, we have not integrated transcriptomic data here.

1. Is the finding that paralogs are depleted among WGD is influenced by the age of WGD since there are 2 WGD events? Do SSD tend to be more or less similar by seq than WGD? This should be explored further since this observation is the opposite of what is observed in model organisms such as yeast whereby SSD are less functionally similar than WGD and often show properties similar to singletons than WGD.

As noted by reviewer 2 in the cross commentary, it is extremely challenging to age the duplicates that arose from the WGD due to the close temporal proximity of the two whole genome duplication events. In the dataset of paralogs analysed used here, SSDs have lower average sequence identity than WGDs. However we note that both sequence identity and duplication type are included in our regression analysis (Figure 4D) and both are significantly associated with homozygous deletion frequently.

This should be explored further since this observation is the opposite of what is observed in model organisms such as yeast whereby SSD are less functionally similar than WGD and often show properties similar to singletons than WGD.

We do not actually think that our results are in opposition to the findings from model organisms. The bulk of studies on the functional consequences of deletions of SSDs/WGDs in model organisms are derived from analyses of the budding yeast gene deletion collection, which is generated in a single strain and grown in lab conditions. Consequently these studies report on which genes can be lost in a single genetic background when grown in rich media. We think it is not fully clear how these findings will apply in the context of a panel of genetically heterogenous tumours derived from multiple different cell types. We note that there are additional complexities when analysing human genes (tissue types, two rounds of WGD, metazoan specific pathways enriched in either WGDs/SSDs) that make a straightforward comparison with yeast challenging. We also note that although the results of analyses of the yeast gene deletion collection suggest that SSDs are more likely to be essential than WGDs, experimental evolution studies have demonstrated that SSDs are more likely to accumulate protein altering mutations than SSDs (Keane et al, Genome Research 2014; Fares et al, PLoS Genetics 2013). This is not what would expect based on the analyses of the yeast gene deletion collection, but is closer to what we observe for tumour genomes where SSDs are more likely to be homozygously deleted.

We agree that we did not adequately discuss these issues in the previous version of our manuscript and so have added a new section to the discussion where we compare our results here with those from budding yeast:

Much of our understanding of the factors that influence gene dispensability comes from studies in model organisms, in particular the budding yeast Saccharomyces cerevisiae [3,9,10,43,44]__. Analyses of the yeast gene deletion collection, a set of gene deletion mutants systematically generated in a single S. cerevisiae strain, revealed that paralogs were less likely to be essential than singleton genes [3,45]__. Furthermore, more detailed analyses of yeast paralogs revealed that paralogs from large families were less likely to be essential as were genes with highly sequence similar paralogs [43,44]__. Previous analyses, including our own, demonstrated that many of these trends are also evident when analyzing gene essentiality from CRISPR screens in cancer cell lines [12,13,15,35]__. Our results here are also consistent with these findings – many of the features that are associated with paralog dispensability in yeast are also associated with gene deletion frequency in tumor genomes.

The connection between the budding yeast observations and those in cancer is less clear when it comes to the relative dispensability of WGDs and SSDs. Analyses of the yeast gene deletion collection revealed that SSDs are more likely to be essential than WGDs in the single genetic background studied [43,44]__. In our previous analyses of gene essentiality in hundreds of cancer cell lines we found that SSDs were more likely to be broadly essential (essential in most cell lines) than WGDs but that WGDs were less likely to be never essential (i.e. more likely to be essential in at least one cell line)__[13]__. As the analyses of gene essentiality in budding yeast were generated in a single genetic background the concordance with our cancer cell line results was difficult to assess, but as gene deletion collections are now being generated in additional yeast strains it should become possible to perform a more direct comparison__[46–48]__.

Here we found that WGDs are less likely to be deleted than SSDs in tumors. This is surprising in light of the yeast gene deletion collection results, where SSDs were more likely to be essential than WGDs in the strain studied, but less so in light of the cancer cell line results, where WGDs were less likely to be never essential. It is also worth noting that experimental evolution studies in yeast found that SSDs accumulate protein-altering mutations at a higher rate than WGDs [49,50]__. These results are perhaps especially relevant when analyzing the influence of paralog features on selection in tumors.

We note that there are many additional differences in the features of WGDs and SSDs in budding yeast that may alter their relative dispensability in tumors. An obvious large scale difference is that in the ancestor of humans there were two rounds of whole genome duplication compared to a single duplication event in yeast__[51,52]__. Less obvious, but potentially of importance for cancer, is that the two classes of paralogs are enriched in pathways in humans that do not have obvious counterparts in yeast. For example, WGDs are highly enriched in signaling pathways involved in development while SSDs are enriched in immune response genes__[53]__. How the membership of these pathways influences the dispensability and selection of genes in tumors and cancer cell lines warrants further study.

Minor comments<br /> 1. There is a missing reference on line 55.

We thank the reviewer for catching this oversight. We have now added a reference to Zerbino et al, NAR 2018 on this line.

CROSS-CONSULTATION COMMENTS<br /> That's a good suggestion by reviewer 1. Homozygous deletion collection is available in yeast so these data can be used directly in addition tot he haploid gene deletion collection data.

Since authors of this manuscript included in their analysis the comparison of WGD and SSD then they should do it more thoroughly. It is not sufficient what they presented here especially given that it contradicts the findings from model organisms.

As noted above we have now added a significant discussion of the yeast findings and also of the SSD/WGD observations

Reviewer #3 (Significance):

This work provides the first systematic assessment of paralog dispensability specifically looking at homozygous deletions of paralogs across primary tumor samples and builds on the existing findings in cancer cell lines. It will be broadly interesting to those studying duplicated gene evolution and genome robustness. My expertise is in complex genetic networks in yeast and human cancer as well as genome evolution.

We thank the reviewer for the positive assessment of our manuscript.

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Referee #3

Evidence, reproducibility and clarity

Thank you review "Paralog dispensability shapes homozygous deletion patterns in tumor genomes" by DeKegel et al. This manuscript uses TCGA and ICGC tumor data to show evidence for paralog dispensability. They analyze the rate of homozygous deletions and show that it is higher for paralogs compared to singletons. Their findings are robust to a number of confounding variables that they take into account e.g. distance to tumor suppressor, telomere, centromere or fragile site. They show that paralogs that belong to large families and have higher sequence identity tend to show more dispensability and these dispensable paralogs are less likely to be WGD.

Major comments.

1. Does the finding pertaining to lack of enrichment of paralogs in regions LOH take into account whether LOH is copy neutral or not i.e. how does dosage affects this finding? Is it possible that there is a difference in paralog rate in LOH that results in total copy 1 and that the presence of copy neutral LOH masks the effect? Also, Integration of gene expression dataset would be helpful to resolve the difference between dosage paralog that compensate of the lack of their sister by upregulating their gene expression.
2. Is the finding that paralogs are depleted among WGD is influenced by the age of WGD since there are 2 WGD events? Do SSD tend to be more or less similar by seq than WGD? This should be explored further since this observation is the opposite of what is observed in model organisms such as yeast whereby SSD are less functionally similarthan WGD and often show properties similar to singletons than WGD.

Minor comments

1. There is a missing reference on line 55.

Referees cross-commenting

That's a good suggestion by reviewer 1. Homozygous deletion collection is available in yeast so these data can be used directly in addition tot he haploid gene deletion collection data.

Since authors of this manuscript included in their analysis the comparison of WGD and SSD then they should do it more thoroughly. It is not sufficient what they presented here especially given that it contradicts the findings from model organisms.

Significance

This work provides the first systematic assessment of paralog dispensability specifically looking at homozygous deletions of paralogs across primary tumor samples and builds on the existing findings in cancer cell lines. It will be broadly interesting to those studying duplicated gene evolution and genome robustness. My expertise is in complex genetic networks in yeast and human cancer as well as genome evolution.

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Referee #2

Evidence, reproducibility and clarity

Summary

Here, De Kegel & Ryan analyse thousands of tumour samples from the TCGA and ICGC projects to identify homozygously deleted genes, finding that about 40% of protein-coding genes are deleted in at least one sample. They find homozygously deleted genes to be enriched for paralogous genes, and further, more frequently deleted genes are increasingly likely to be paralogs. The authors then test the influence of several factors on the likelihood of being deleted, including gene length, distance to a fragile site or chromosomal region, and distance to a recurrently deleted tumour suppressor gene (TSG). They find that proximity of a TSG, telomere, centromere, and fragile site all increase likelihood of being deleted in a sample, as does gene length. Having a paralog also remains an important predictor of deletion after accounting for these other factors. Additionally, the more similar in sequence the closest paralog is to the gene and having a larger gene family size are also predictive of deletion. Conversely, if a gene is a whole genome duplicate as opposed to a small-scale duplicate, it is less likely to be deleted. Finally, the authors test the hypothesis that paralogs that are deleted in cancer are less likely to be essential and find that this is indeed the case.

Comments

The authors have done a good job of identifying trends of paralog deletion in cancer samples and the factors influencing them. The results are well described and presented and support the conclusions. I like the inclusion of the saturation analysis as an estimate of what to expect given current and potential future sample sizes, and I appreciate the inclusion of a WGD/SSD paralog distinction. The data and methods are sufficiently detailed. I have a few minor comments below.

1. Around line 160 in the text and supplemental figure 4A, the authors test if the trends they see are observed across individual cancer types. With 9 of 33 cancer types reaching a sample size threshold, 8 of 9 comparisons are significant. The authors do not state correcting for multiple testing.
2. I initially misunderstood the hemizygously deletion analysis, thinking the analysis in supplement figure 4B/C was asking if a sample has any singleton or any paralog deleted and comparing the number of samples with any deletion of either - given the number of genes deleted per sample this wouldn't make sense as a good test. I think the authors are actually comparing the number of loss-of-hemizygosity events per gene and grouping by paralog/singleton. I think this is a good analysis, but I think it would be helpful to clarify this in the text and figure legend e.g. "Samples w/ gene LOH" could be "LOH events per gene" or something similar.
3. Occasionally, I wanted some more detail in the text for context, which was sometimes later provided - e.g. I noted when reading about line 125 that I was curious at this point how often TSGs occurred on segments, and this was later provided on line 241. Similarly, around line 114 I was curious how many genes are typically deleted per HD segment, for which the median value was provided on line 206 (and distribution in supplemental figure 1), and again for hemizygous deletions. I think sometimes it would be helpful to provide this context earlier in the text to aid interpretation of the results.
4. In the discussion, on line 420, the authors include the point that a paralog might not be required at all in a tumour cell and therefore easily deleted. I think this possibility could be expanded on here and in the introduction/results section, as it is an important point. I think it would be helpful to include more about the possibility that a paralog might be deleted in a tumour cell because it is simply not required or that is more likely to have less of a phenotypic impact compared to a singleton, and that this could be a reason for the observed enrichment of paralogs in deleted genes. A citation to support this point could be Áine N O'Toole, Laurence D Hurst, Aoife McLysaght, Faster Evolving Primate Genes Are More Likely to Duplicate, Molecular Biology and Evolution, Volume 35, Issue 1, January 2018, Pages 107-118, https://doi.org/10.1093/molbev/msx270. Duplicate genes can be duplicates because copy number variation of them has minimal impact.

Referees cross-commenting

I agree, that's a helpful suggestion from reviewer 1.

Reviewer 3's suggestion regarding age of the two whole genome duplication events is quite difficult to unpick as the duplication events seem to have happened relatively close in time to each other while rediploidisation of the first was occurring. Additionally, paralogs from SSDs tend to be more similar in sequence simply because the two WGD events are relatively old while SSDs can occur at any time up to present. They're therefore biased by young duplicates that have not had the opportunity to diverged much and decrease in sequence similarity.

Significance

This is a novel study as it examines the frequency of paralog deletion in cancer samples and the factors influencing it, building upon work already conducted in cancer cell lines. This study extends the knowledge of the field confirming previous trends observed in cell lines, this time in actual cancer samples. It confirms that paralogs are more dispensable than singletons, likely because they have a similar counterpart that can provide some level of functional redundancy. The more similar the closest paralog, the more likely it is to be deleted provides support for this.

It is certainly limited by the number of samples currently available in the two cancer sample projects included but the authors attempt to quantify how limiting this sample size is by conducting a saturation analysis using down-sampling to estimate how many gene deletions one can expect from different numbers of samples. This is important as the lack of observance of many gene deletions is likely due to the limited sample size and not due to negative selection. This low observance of gene deletions disappointingly limits further testing beyond single paralogs to consider the deletion effects of multiple gene family members and more directly test evidence of functional redundancy between paralogs. The authors provide a good discussion of the limitations of their study.

The results are of interest to evolutionary biologists and cancer biologists. Those with an interest in duplicate genes, and/or factors affecting gene loss in tumours will be interested in this work.

My field of expertise is molecular evolution, gene duplication and copy number variation.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors delineate the association of paralog dispensability with the frequency of homozygous deletions (HDs) and thereby show that paralog dispensability can play a significant role in shaping tumor genomes. The authors analyzed the strength of negative selection on the paralogs relative to the singletons using frequencies of the homozygous deletions (HD). The study focused on HDs because they ensure a complete loss of function, unlike other mutational aberrations that can be masked because of haplo-sufficiency. While accounting for potential confounding factors, authors find that paralogs tend to have a relatively high frequency of HDs, suggesting a relaxed negative selection. Furthermore, the authors specifically attribute this association to the dispensable paralogs by analyzing gene inactivation data generated from multiple experimental systems. Overall, the findings of this study can potentially have significant implications in cancer biology field and specifically to the researchers studying cancer genome evolution.

Major comments:

1. To dissect further which dispensable paralogs are more likely to be associated with a high HD frequency, synthetic lethal paralogs could be compared with non-synthetic lethal ones.<br /> In the section titled 'Homozygous deletion frequency of paralog passengers is influenced by paralog properties' (begins from line #289), authors have shown that paralogs with a high frequency of HDs are more likely to have the properties of dispensability (in Figure 4). It seems that all of those properties are also associated with synthetic lethality as the authors identified in their previous study (DeKegel et al. 2021). Furthermore, as shown in the subsequent section ('Essential paralogs are less frequently homozygously deleted than non-essential paralogs', begins from line #344), the high HD is associated with the dispensable paralogs. Some of those dispensable paralogs are expected to be synthetic lethal. Therefore, the association of paralogs with a high frequency of HDs with experimentally validated or predicted sets of synthetic lethal paralogs could be tested. This may help authors to contextualize their findings in terms of genetic interactions between paralogs.

Minor comments:

1. The number of TCGA and ICGC tumor samples analyzed:<br /> As mentioned in the Results section (line #106), 9966 tumor samples were analyzed. However, the sample size mentioned in Figure 2A is 9951. Is the lower number shown in the figure due to the filtering procedure mentioned in the Methods section (line #455)? The change in sample sizes could be explained. A similar difference in sample sizes exists for the ICGC data also.
2. The rationale behind setting the threshold at 100 HD genes to classify 'hyper-deleted' samples for TCGA (line #462) and ICGC data (line #473) could be explained.
3. Citation for DepMap is missing (caption of Figure 5).

Referees cross-commenting

Along the lines of Reviewer #3's second major comment, I have a suggestion, the possible benefits of which would depend on the target audience to which the authors intend to communicate their study.

I would suggest including a brief comparison of the findings of this study which deal with human paralogs, with the findings in model organisms such as yeast, perhaps in the discussion section. To facilitate such a comparison, authors could try measuring the enrichments of, for example, molecular functions, gene families, types of genetic interactions, etc., among the paralogs associated with a high frequency of HDs and then discussing their comparison with what is known in the literature for paralogs in other model organisms that tend to be frequently deleted.

Such a comparison could be of interest to the community of researchers working on other model organisms and put this study in a much broader context. However, as I said before, this would depend on the authors' intended target audience.

Significance

As the authors note in their manuscript, it is expected that paralog dispensability could be associated with the relaxed negative selection in tumor genomes because (1) paralogs are prevalent in the human genome, and (2) many of them are dispensable, as apparent from the large-scale gene inactivation screens in hundreds of cancer cell lines (Blomen et al. 2015, Wang et al. 2015, Dandage and Landry 2019, De Kegel and Ryan 2019). However, direct mapping of this association, while importantly accounting for potential confounding factors, has been lacking.<br /> As a researcher with prior experience in the research topics such as gene duplication and genetic interactions, it appears to me that this study presents formal proof of the important association between paralog dispensability and tumor genome evolution which could be of major implication for the research community of cancer biology field and specifically to the researchers dealing with the topics such as cancer evolution, copy number alterations in cancer genomes, and synthetic lethality-based precision oncology therapeutics.

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Reply to the reviewers

We would like to thank all reviewers for taking the time to evaluate our manuscript. Many helpful suggestions and discussion points were raised. These comments were instrumental to provide more data that strengthen our conclusion about the relevance of centrin condensation in vivo, expand our findings to other organisms, and improve the manuscript in general. Details are given in the following individual replies.

Reviewer #1 (Evidence, reproducibility and clarity):

Voss and colleagues show calcium-dependent assembly of Plasmodium falciparum centrins in vitro and in parasites. This assembly is dependent on the EF-hands of centrin and an N-terminal disordered region.

Major concerns:

1. The very definitive title is not wholly supported by the data. This should be qualified by specifying the conditions under which the centrins can accumulate in this way.

We understand this comment by the reviewer. There are multiple dimensions to the potential of centrins to condensate, such as the specific centrin family member, in vivo vs in vitro situation, and media conditions. Naturally it is difficult to represent these various conditions in a concise and compelling title but in line with the suggestion by Reviewer 2 we are changing the title to “Malaria parasite centrins can assemble by Ca2+-inducible condensation” to reflect the conditionality of this process.

1. A major concern is whether this behaviour of centrins represents a biologically relevant mechanism in centriolar plaque formation. Is this limited to high overexpression conditions or in vitro high concentrations? Or is it a result of the tagging of the P. falciparum centrins?...

Centrin accumulation at the centriolar plaque and assembly of the centriolar plaque itself must be differentiated. Although compelling we are already very careful in the text about extrapolating our findings about centrin accumulation in cells to centriolar plaque or centrosomal assembly in general. We, however, thank the reviewer for this important comment and now have carried out hexanediol treatment of wild type parasites to test the effect on centrin in a native context. After IFA staining we failed to detect any centrin foci at the centriolar plaques, suggesting that they can be resolved by inhibiting weak hydrophobic interactions that are typical for phase separation (now Fig. 6, lines 283ff).

Concerning the effect of tagging we have generated new data of cells overexpressing an untagged version of PfCen1 in parasites, which still shows formation of ECCAs as revealed by IFA (now Fig. 4H-K, lines 243ff). This significantly alleviates the concern that the observed phenomenon is only a consequence of GFP-tagging. Our in vitro data already showed that native and tagged PfCentrin1 & 3 can undergo condensation.

Concerning the critical concentration of our in vitro assay we find it to be around 10-15 µM without the addition of crowding agents such as PEG (now Fig. S3C, lines 120ff). To our understanding it is challenging to select an in vitro concentration that is adequate to define a threshold for “biological relevance” due to so many additional factors playing a role in vivo. Those factors can also favor a phase separation locally when total saturation concentration is not reached as we now discuss in more detail (lines 440ff). For reference the critical concentration of FUS, which is one of the most studied phase separating proteins in model system, is around 2 µM, but concentrations below 15 µM are well within the range of what is observed for in vitro LLPS. Additionally, it is important to consider that we find Cen1/3 and HsCen2 LLPS is inducible and reversible and that very homologous proteins i.e. Cen2 and 4 serve as an adequate internal control.

… A convincing approach to addressing this issue would be to knock-in a fluorescent tag to the centrin loci. Roques et al. (ref. 12 in this submission) report the GFP tagging of centrin-4 in P. berghei, although they note that centrins-1 to -3 were refractory to tagging in this organism. It is unclear whether Voss et al. attempted this tagging in P. falciparum. This should be clarified and relevant data presented.

We indeed attempted several unsuccessful iterations of tagging Cen1/3 with HA and GFP tag and now explain this in the text more clearly (lines 81ff). We did not attempt tagging Cen2 and 4 as they do not display phase separation in vitro or carry IDRs.

If the tagged molecules used in the biochemical parts of this study are functional, it is challenging to understand why the centrins cannot be tagged in P. falciparum. If the tags render the P. falciparum centrins dysfunctional, the study becomes significantly less useful.

Our data shows that in vitro Cen1-GFP can undergo Ca2+-inducible and reversible LLPS and that GFP-tagged centrins can still localize to the centriolar plaque. Centrin function, however, certainly goes beyond its ability to condensate and localize. It is easily conceivable that interaction with critical binding partners at the centriolar plaque is inhibited by tagging a protein as small as centrin, which prohibits tagging the endogenous version, while its ability to phase separate remains unaltered. To dynamically study a protein in cells tagging is, however, unavoidable. Even though tagging affects any proteins function to highly variable degree we are still convinced that studying those proteins still provides useful information. Our mutant versions of PfCen1 in vivo shows that non-condensating version display different localization. Importantly, as mentioned above, we now provide images of cells overexpressing an untagged Cen1 version, which still causes ECCA formation (Fig. 5H-K). Ultimately, even though tagged versions might not be fully functional, our observations are compatible with the ability of centrins to condensate in vivo.

1. If a knock-in cannot be achieved, it must be shown that the transgenic expression of tagged Plasmodium centrins does not confound the analysis of centrin behaviour. It is known that these proteins can behave anomalously when overexpressed (Yang et al. 2010, PMID: 20980622; Prosser et al. 2009, PMID: 19139275), at least in other species.

Thank you for this comment. Transgenic expression of proteins can in principle influence their behavior. In the context of this study the overexpression is, however, used intentionally since protein concentration correlates with the phase separation. Here, transgenic overexpression is used as a tool, rather than being a confounding factor, and ECCA formation can be used as quantifiable phenotype. The observation that ECCAs appear significantly earlier the higher they are expressed is in our opinion one of the stronger points of evidence that this result from phase separation in vivo. Yet centrins maintain their centriolar plaque localization and no significant impact on growth is observed. To definitely answer whether phase separation of endogenous centrin is occurring during centriolar plaque accumulation is challenging. These challenges and limitations are now addressed in the significantly extended discussion. As explained above untagged Cen1 also forms ECCAs.

A previous description of centriolar plaque from the authors' lab (Simon et al. 2021, PMID: 34535568) shows an organized structure of an established size. It should be demonstrated whether the structures formed with the GFP tagged centrins show the same dimensions and dynamics as those in wild-type parasites. The extent of the overexpression of the GFP-tagged centrins should also be demonstrated.

We thank the reviewer for this suggestion. We have now added spatial measurements of the centrin signal dimensions at the centriolar plaque of mitotic spindle containing nuclei in PfCen1-GFP overexpressing vs non-induced cell lines. We found that the width of the centrin-signal at the centriolar plaque was unaltered while the height only increased by 11% (Fig. S9). Further, we found no significant growth phenotype in overexpressing parasites, which indicates that the centriolar plaque is functional.

Due to several confounding factors, we were, unfortunately, unable to clearly quantify the extent of overexpression. Most notably the induction of overexpression only works in about 50% of the cells (Fig. S6). The mean intensity after induction further displays quite some variability. Furthermore, the expression kinetics along the IDC of endogenous centrin and our overexpression system that we use as a tool differ. Lastly, our centrin antibodies display crossreactivity (see also Fig. S12) making it impossible to identify how much of the endogenous pool we are labeling in comparison to the GFP- tagged Cen1 protein.

1. It would also be useful to remove the His tag from the recombinantly expressed and purified centrins for the in vitro analyses, particularly if concern remains about the impact of tags on Plasmodium centrin behaviour.

Based on the published in vitro studies on other centrins, we did not anticipate the His-tag to change LLPS properties. Also, Cen1 and 3 and Cen2 and 4 would need to be differentially affected by the tag. We further have experimented with N-terminally tagged 6His-Cen3 protein and found no significant differences in our turbidity assays. Nevertheless, we expressed new versions of the recombinant PfCen1-4 proteins with a TEV cleavage site inserted after the His-tag to purify untagged proteins and found no fundamental differences in our LLPS assay aside some slight variation in the kinetics (Fig. S3E).

1. The discussion is very short and does not consider the findings presented here in the context of the literature, with respect to centrins, Plasmodium MTOC assembly mechanisms, or to general considerations around biological condensates. Andrea Musacchio's recent commentary (ref. 44 in the current submission) advocates caution in ascribing phase separation as an assembly mechanism for organelles in vivo, particularly on the basis of in vitro experiments with high concentrations of homogeneous protein. It is not clear that the concentration dependence of extracentrosomal centrin accumulations (ECCAs) at the onset of schizogony provides sufficient justification of a phase separation model in vivo. The authors' recent description of the involvement of an SFI1-like protein, SIp (Wenz et al. 2023 PMID: 37130129), in the centriolar plaque makes a case for non-homotypic interactions also driving assembly and alternative models for ECCA are not convincingly excluded. The absence of a robust discussion of such considerations is unhelpful to the reader.

We very much thank the reviewer for this suggestion, which helped to significantly improve the manuscript. We have purposefully included the commentary by Andrea Musacchio to highlight a different (possibly the most antipodal) point of view on the role of biomolecular condensation in membraneless organelle formation for the unfamiliar readers that might be just getting to know the field of phase separation. In the absence of word limitations, the reviewer is right to point out the lack of more extensive discussion. We now have significantly extended this section and address the suggested points including the potential role of the novel centriolar plaque protein Slp, which was not published upon submission of our previous version (lines 450ff.)

1. It is also unclear whether the analysis of human centrin is suggested to indicate a phase separation mechanism for centrins in human cells. As this is readily testable, this notion could be considered further. Although its experimental examination may lie outside the theme of this study, one would expect some discussion of the significance of the data presented in the study.

Since it is the first description of phase separation of centrin, it would indeed be interesting to explore the functional relevance in other organisms such as humans. We are considering approaching this in the future. We have, as requested above, significantly extended the discussion and now also include this aspect. Earlier reports have e.g. shown centriole overduplication in human cells upon centrin overexpression.

Minor points

1. There are only three centrins in humans. Centrin 4 is a pseudogene (Gene ID: 729338 on NCBI).

Thank you for detecting this error, which we now corrected (line 60). Centrin 4 seems only to be an expressed gene in mice.

1. Line 175 should say 'temporally', rather than 'temporarily. The Abstract should say 'evolutionarily conserved', rather than 'evolutionary conserved'. 'To condensate' is not ideal as a phrase- 'to form a condensate' would be clearer.

Thank you for those suggestions. The text has been modified accordingly.

Referees cross-commenting

I think the other 2 reviewers have made fair, cogent and constructive points. There is good convergence between the reviewers on the significant issues around the study. These concern in vivo and in vitro effects of tagging and of high concentrations.

Reviewer #1 (Significance):

The biology of the Plasmodium centriolar plaque is of great interest as an alternative MTOC structure, with obvious additional interest deriving from the role of this organism in malaria. Much remains to be learned about this structure, so the topic of this paper is likely to attract a broad readership. Furthermore, the centrins are a widely-expressed and evolutionarily conserved family of eukaryotic proteins, with multiple roles; a new model for their behaviour, such as is suggested here, would be of interest to many cell biologists.

With that in mind, significant additional data should be provided to substantiate the model proposed by the authors.

We appreciate that the reviewer considers our manuscript of interest for a broad audience. We feel that our modifications of the text including a more thorough contextualization and addition of some new experimental data now sufficiently supports our claims.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors analyzed the properties of the four Centrin proteins of the malaria parasite using a combination of in vitro and in vivo approaches. Their findings indicate that two of the four Plasmodium Centrin proteins, PfCen1 and PfCen3, as well as the human Centrin protein HsCen2, exhibit features of biomolecular condensates. Moreover, analysis of cells overexpressing PfCen1 indicates that such biomolecular condensates become more numerous as cells approach mitosis and are dissolved thereafter.

Major comments

A) A critical point that requires clarification is how the protein concentrations used in the in vitro and in vivo assays (20-200 microM in vitro, and not estimated in vivo) compare to that of the endogenous components. This is important because it may well be that 6His-tagged PfCen1, PfCen3 and HsCen2 can form biomolecular condensates when present in vast excess, but not when present in physiological concentrations. The authors should report the estimated cellular concentration of PfCen1-4, as well as that achieved upon PfCen1-GFP overexpression (on top of endogenous PfCen1), for instance using semi-quantitative immunoblotting analysis. Given this limitation, the authors may also want to temper their title by introducing the word "can" after "centrins".

In the context of phase separation, protein concentration is of course a critical metric. However, in vitro and in vivo concentrations cannot be directly compared as the composition of the surrounding solute has a significant impact on the effective saturation concentration. In vitro we find a saturation concentration for Cen1 of 10-15 µM (Fig. S3C), which is within a range that is frequently found other in vitro studies as listed in the in vitro LLPS data base (PMID: 35025997). We now more explicitly discuss this in the text (lines 422ff). At this point, unfortunately, we have no means of investigating the absolute concentrations of centrin in vivo and to our knowledge no such data is available for apicomplexan. Additionally, one has to keep in mind the presence of other centrin family members in the cell which can interact and co-condensate as well as other centriolar plaque proteins, like PfSlp, but are difficult to separate through analysis. Further we now discuss several contexts that modify the saturation concentration in vivo (lines 440ff).

As explained above in a response to Reviewer 1, we were not able to produce a satisfactory quantification of the overexpression levels. We are repasting the previous response here:

“Due to several confounding factors we were, unfortunately, unable to clearly quantify the extent of overexpression. Most notably the induction of overexpression only works in about 50% of the cells (Fig. S6). The mean intensity after induction further displays quite some variability. Lastly the expression kinetics along the IDC of endogenous centrin and our overexpression system that we use as a tool differ. Lastly, our centrin antibodies display crossreactivity (see also Fig. S12) making it impossible to identify how much of the endogenous pool we are labeling in comparison to the GFP- tagged Cen1 protein. “

Concerning the title, as explained above, we followed the suggestion and added the word “can”.

B) Movies S1 and S2 (and the related Fig. 1D and 1E) are not the most convincing to support the notion that the observed assemblies are biomolecular condensates, as not much activity is going on during the recordings. Likewise, Movies S3, and even more so Movie S4, as out of focus for a large fraction of the time, making it difficult to assess what happens at the beginning of the process. Moreover, it appears that fusion events, while occurring, are rather rare. The movies should be exchanged for ones that are in focus, and ideally a rough quantification of fusion events as a function of biomolecular condensate size provided.

We thank the reviewer for requesting clarification. Movies S1 and S2 are by no means direct evidence for biomolecular condensation and we do not claim them to be but rather say that they are “…reminiscent of biomolecular condensates…”. We think that this is an appropriate entry into the subsequent analyses. For Movie S1 it is noteworthy that the shape of the accumulation, which can only be resolved by super-resolution microscopy in live cells, is round as would be expected for a liquid condensate in the absence of forces and on these short time scales. Nevertheless, the centriolar plaque must be duplicated which might be the process partly depicted in Movie S2. The observation that centrin can be still change its shape at least suggests that it is not a solid aggregate. In the context of centriolar plaque biology and the technological advance of applying live cell STED in P. falciparum, we think these data are still worth reporting.

Concerning Movies S3 and S4 we have carefully selected the focal plane to highlight all the hallmarks of LLPS. Since the protein droplets freely move in 3D throughout the entire imaged liquid volume there is no z-plane that is in focus. Our positioning of the focal plane presents the best compromise between showing round droplet shape, droplet fusion events, and surface wetting. All those observations demonstrate the liquid nature of the condensates. Fusion events are indeed relatively rare, and we do not go beyond this qualitative statement that it can be seen.

C) An important control is missing from Fig. 2, namely assaying PfCen1-4 without the 6His tag, to ensure that the tag does not contribute to the observed behavior (although it can of course not be sufficient as evidenced by the lack of biomolecular condensates for PfCen2 and PfCen4).

Thank you for this suggestion. Since reviewer 1 made a similar comment, I’m reiterating our previous reply here: Generally speaking, and based on the published in vitro studies on other centrins, we didn’t anticipate the very small His-tag to change LLPS properties. Also, Cen1 and 3 and Cen2 and 4 would need to be differentially affected by the tag. We further have experimented with N-terminally tagged 6xHis-Cen3 protein and found no significant differences in our turbidity assays. However, we expressed new versions of the recombinant PfCen1-4 proteins with a TEV cleavage site inserted after the His-tag to purify untagged proteins and found no significant differences in our LLPS assay (Fig. S3E).

D) The authors should test whether the assemblies formed by PfCen1 and PfCen3 are sensitive to 1,6-hexanediol treatment, as expected for biomolecular condensates.

This is an interesting and helpful suggestion. We now tested 1,6-hexanediol addition to recombinant PfCen1 and wildtype parasites (now Fig. 6). Interestingly the dissolving effect of hexanediol on PfCen1 in vitro was moderate, which we attribute to the polar component in centrin assembly, which has been documented earlier (Tourbez et al. 2004). In vivo, however, only 5 min of treatment caused a striking dissolution of most centrin foci in wild type parasites, which is compatible with the interpretation that centrin or centriolar plaque assembly could be driven by biomolecular condensation.

E) The fact that HsCen2 also forms biomolecular condensates is very intriguing, but further investigation would be needed to assess the generality of these findings. For instance, the authors could test in vitro also S. cerevisiae Cdc31, the founding member of the Centrin family of proteins to further enhance the impact of their study.

We thank the reviewer for this suggestion. It would of course be exciting to investigate in more detail how widely this biochemical property of some centrins is conserved. To take a first step in that direction, we have recombinantly expressed centrins containing some N-terminal IDRs from C. reinhardtii, T. brucei and S. cerevisiae to represent organism of significant evolutionary distance. Using our in vitro phase separation assays, we found a very similar behavior to PfCen1 for two centrins while yeast Cdc31, although forming droplets, had a much higher saturation concentration, which could be explained by the significantly lower intrinsic disorder in its sequence (now new Fig. 3).

Minor comments

1) For the experiments reported in Fig. 3D, the same concentrations as those used in Fig. 3A-C (namely 10 microM, and not 30 microM as in Fig. 3D) should be used. Moreover, it would be informative to test whether PfCen2 and PfCen4 as PfCen3 when added to PfCen1.

Unfortunately, this experiment is not feasible since Cen3 does not produce droplets at 10 µM. Hence, in Fig. 3D we aimed to test if Cen1 is incorporated into preformed droplets i.e. whether there is still some interaction between them. We have, however, tested the addition of Cen2 to Cen1 and Cen3 and as expected from the inability PfCen2 to condensate we did not find the same synergistic effect as for Cen1 and 3 together (now Fig. S6). The combination of Cen1/2/3 still enabled co-condensation while addition of Cen4 did not further improve droplet formation. Taken together this strongly suggests that only Cen1 and 3 contribute to the phase separation in vitro (lines 184ff).

2) The authors mention that the effect of Calcium in inducing biomolecular condensates is specific, as Magnesium was not effective (lines 94-95). However, an examination of Fig. S3B indicates that the Magnesium also exhibits some activity, albeit less potent than Calcium. The authors should discuss this point and rectify the wording in the main text.

Thank you for pointing this out. While PfCen1 is not reactive to Magnesium, PfCen3 and HsCen2 do display a small reaction, which we now more clearly mention in the text (lines 118ff). Of note Mg2+ and other divalent cation are known to generally promote phase separation.

3) Do the authors think that PfCen2 and PfCent4 localize to the centriolar plaque in vivo using another mechanism that deployed by PfCen1 and PfCent3? It would be good to discuss this point.

This is indeed a point worth discussing. Centrins can of course still interact in the absence of biomolecular condensation and their localization to the centriolar plaque is not dependent on their ability to phase-separate as seen for PfCen2 and 4. We have recently described a novel centriolar plaque protein PfSlp that interacts with centrins and might assist recruitment (Wenz et al. 2023). Cellular condensates are, however, often separated into scaffold proteins, which actually phase separate and client protein which get recruited into those condensates. It is easily conceivable that Cen1 and 3 participate in formation of the biomolecular condensate into which Cen2 and 4 as well as other centriolar plaque proteins might be recruited. Unfortunately, we were not yet able to establish a recruitment hierarchy by e.g. dual-labeling of centrins to test whether PfCen1 and 3 might appear prior to PfCen2 and 4. We now include those aspects in the extended discussion.

4) Given that the EFh-dead mutant exhibits no activity in vitro and fails to localize in vivo, one potential concern is that the protein is misfolded. The authors should conduct a CD spectrum to investigate this.

Thank you for suggesting this relevant control experiment. We have carried out CD spectroscopy of wild type and EFh-dead PfCen1 and find no difference in secondary structure distribution. We now added these data to the supplemental information (now Fig. S14).

5) It is not entirely clear from the main text in lines 103-104, as well as from the legend, what Fig. S3B shows. When was EDTA added in this case?

Thank you for requesting clarification. We will assume the reviewer is referring to Fig S4B. We wanted to show that contrary to PfCen3 that PfCen1 droplets can still be resolved after an elongated period of incubation with calcium but forgot to mark the timepoint of EDTA addition at 180 min in the graph. We have now corrected this and further reworded the sentence for more clarity (lines 132ff).

6) Fig. S7: the correlation between PfCen1-GFP expression levels and ECCA appearance is modest at best. What statistical test was applied? This should be spelled out. Moreover, the authors should combine the two data sets, as this will provide further statistical power to assess whether a correlation is truly present.

Indeed, the correlation is modest but statistically significant, which is why we decided to place this data in the supplemental information. The used statistical test was an F-test provided by Prism, which compares two competing regression models, which we now mention in the legend. Combining the two data sets is unfortunately not possible since they arise from two independent sets of measurements where different imaging settings had to be used to adjust for the very different fluorescent protein levels in both lines after induction.

7) The authors may want to discuss how their findings can be reconciled with the notion that Centrin assemble into a helical polymer on the inside of the centriole (doi: 10.1126/sciadv.aaz4137).

This is an interesting point. Although centrin does localize to the inside of the centriole (https://doi.org/10.15252/embj.2022112107), more precisely one pool at the distal part and one pool at the core, there is no evidence that it is itself part of the helical inner scaffold described by the authors even though it might localize in close proximity to it. Further, there are several examples where polymers such as microtubules act as seeding point for biomolecular condensates or the other way around, and our work suggest this could be a potential working model for centrins. We have discussed our results extensively with the two corresponding authors of the aforementioned study (i.e. Virginie Hamel and Paul Guichard) and agreed that our data are not conflicting. Nevertheless, we include the inner centriole localization and potential association with polymer structures of centrin in our extended discussion.

9) Likewise, the authors may want to speculate regarding what their findings signify for the role of Centrin proteins in detection of nucleotide excision repair (doi: 10.1083/jcb.201012093).

We appreciate the comment by the reviewer. Centrins seem to have many different potential roles that remain to be clarified. While we are excited about this, we think it is too early to speculate about the impact of centrin condensation on less well studied aspects of centrins such as nucleotide excision repair. We, however, now cite this study in the discussion to highlight the functional diversity of centrins.

Small things

• Fig. 1A: change color for microtubules as red on red is difficult to discern.

Throughout our publications we use this shade of magenta to label microtubules in schematics and have therefore opted to use a slightly brighter shade of red for the RBCs instead to improve visibility.

• Fig. 1C: the indicated boxes in the top row do not seem to correspond exactly to the insets shown in the bottom row.

We have verified the position of the boxes and found them to be accurate. Possibly the different imaging modality used for both panels (confocal vs STED) creates this impression.

• line 266: typo, promotor > promoter.

Has been corrected.

• line 360: a reference should be provided for the GFP-booster, including the concentration at which it was used.

Has been added.

• line 363: "an" missing before "HC".

Has been corrected.

• line 428: it would be best to deposit the macros on Github or an analogous repository.

Macros have been deposited on https://github.com/SeverinaKlaus/ImageJ-Macros (line 737)

• line 461: "to the" is duplicated.

Has been corrected.

• Fig. S5A: maybe draw the lines in red (as red in Fig. S5B correspond to the proteins that do not have IDRs).

Since we cannot easily change the line colors of the IDR graphs, we have inverted the font color for Fig. S5B instead.

• Movie S7, legend: left frames shows PfCen1-GFP, not microtubules as currently stated.

Has been corrected.

Reviewer #2 (Significance):

This is a provocative study that extends initial observations regarding self-assembly properties of Centrin proteins, and posits that some members of this evolutionarily conserved family can form biomolecular condensates. After the above outstanding issues have been properly addressed, these data could have important implications for understanding Centrin function in centriole biology and DNA repair. Therefore, these findings will be of interest to a cell biology audience.

Field of expertise: cell biology.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The authors have provided a comprehensive characterisation of centrin proteins in Plasmodium falciparum. Through expression of episomal GFP-tagged centrin for in vitro, they were able to observe co-localisation of centrin with centriolar plaques during the replicative stage of the parasite. They also utilised live cell STED microscopy to track dynamic changes in centrin morphology. They have also demonstrated calcium-dependent phase separation dynamics in bacterially-expressed P. falciparum centrin and human centrin 2. The formation of liquid-liquid phase separation in PfCen1, 3 and HsCen2 tied well with IUPred3 predictions of intrinsically disordered regions in these proteins. Using an inducible DiCre overexpression system with two promoters of varying strengths, the authors have shown accumulation of centrin1 outside of centrosomes and premature appearance of centriolar plaques. Finally, changes on the centrin1 protein, i.e., N-terminal deletion, and mutations in calcium binding sites in the EFh domains, have shown a reduction in the formation of ECCAs during overexpression and inability to form LLPS in vitro, respectively.

Major comments:

1. Given that parasites cannot tolerate endogenous C-terminal tagging of some centrins (but not all, as PbCen4 was successfully tagged), has N-terminal tagging been attempted either by the authors or in previous publications? Note that this is not a request for further experimentation; rather, maybe this can be noted in the manuscript; and line 62 can be rephrased for transparency.

We have not attempted N-terminal tagging ourselves but through personal communication with Rita Tewari we were informed that neither N- nor C-terminal tagging for PbCen1-3 was successful in the context of the study published by Roques et al 2018. We have only unsuccessfully attempted C-terminal tagging in several iterations. Due to importance of N-terminus for interaction and function in other organisms it is plausible that N-terminal tagging is even more unlikely to work. Since we have not exhaustively attempted every tagging strategy on every centrin we, as suggested, rephrased the text accordingly (lines 81ff).

1. Is there a possibility that by adding a C-terminal tag, centrin may lose a specific function or cause change in the physicochemical properties of the protein (thus making C-terminal tagging lethal)? Was His tag removal attempted so the native protein can be used in the LLPS experiments? IUPred3 analysis showed potential IDR at the C-terminal end of PfCen4. Could the C-terminal tag have caused the protein to not form droplets in the presence of Ca2+?

As we could show for PfCen1-GFP, the tag did not impair its ability to undergo LLPS which is at least partly mediated by the N-terminus, and that it could still properly localizes to the centriolar plaque. The fact that some endogenous centrins cannot be tagged suggest that there is a functional relevance to the C-terminus that could e.g. be an interaction with other essential centriolar plaque components. As suggested in a reply to Reviewer 1, we consider a substantial and centrin-specific effect of the small His-tag on phase separation unlikely. To be sure, we have repeated our turbidity assays with tag-free versions of PfCen1-4 and found no change in phase separation properties (now Fig. S3E).

1. It has been shown by the authors that different tagged centrins co-condense which may support the localisation data (Figure 1C). However, is there a way to show that the episomally- and endogenously-expressed centrin co-localise with each other (e.g., confocal microscopy with anti-centrin vs anti-gfp in PfCen-GFP lines, that is if the authors have access to anti-centrin antibodies)? Has endogenous centrin been demonstrated to form ECCAs (in previous publications or by the authors)?

These are important questions by the reviewer. Due to the high sequence homology centrin antibodies, even if raised against a specific centrin (such as PfCen3 in this study), will likely cross-react with other centrins. So far, we have not been able to produce a staining were the anti-GFP-positive foci are devoid of anti-centrin3 staining, which limits the interpretation of these data. The outer centriolar plaque compartment containing centrin is, however, well defined by now and the localization pattern of endogenous centrin and Centrin1 and 4-GFP seems identical. In a more recent study from our lab Cen1-GFP IP has identified other endogenous centrins as interaction partners (Wenz et al 2023), like the Roques et al. 2018 study did for PbCen4-GFP indicating that the tag does not abolish interaction between centrins. So far, we have never detected any ECCAs, nor have we identified any similar structure in the literature. This suggest that this is indeed a consequence of excessive centrin concentration. Importantly we now have added data from a new parasite line overexpressing untagged PfCen1 using the T2A skip peptide (pFIO+_GFP-T2A-Cen1) which displays ECCAs upon induction, showing that this effect is not a mere consequence of tagging (now Fig. 5H-K).

Minor comments:

1. How were the times (post addition of Ca2+) presented in Figure 2A determined?

We noted down the time of calcium addition and cross-referenced it with the timestamps available in the metadata of the movie files (e.g. file creation timepoint marks the start of the movie). We now mention this in the legend.

1. Line 126: Figure 1B should be Figure 1C

2. Line 145: Figure 1C-D should be Figure 1D-E

3. Line 151: Figure 3A should be Figure 4A

Thank you for spotting these mistakes, which now have been corrected.

1. Line 152: Suggest rephrasing "placing the gene of interest in front of the promoter" to "placing the gene of interest immediately downstream of the promoter" or something similar

Thank you for this good suggestion.

1. Any growth phenotype changes observed in the overexpressors?

The parasite lines seem to silence the Cen1-4-GFP expression plasmids readily, which suggest that there might be a growth disadvantage. However, repeated attempts to quantify a growth phenotype were unsuccessful due to high variability in the data, which might be partly connected to the fact that the fraction of GFP positive cells after induction can vary between lines and replicas.

1. How often are ECCAs observed in pARL strains, or are they not observed at all? This might be good to mention.

ECCAs in the pArl strains have been observed on very limited instances but are too rare to be quantified. We now mention this in the text (lines 217ff).

1. Line 192 and Figure S8: n {less than or equal to} 33 (either a typographical error and should have been {greater than or equal to}, otherwise, it may be expressed as a range)

It was indeed a typographical error that was now corrected.

1. Line 258: Methods on the generation of FIO/FIO+ was a bit difficult to understand. Maybe a simple plasmid schematic with the restriction sites (at least for the original plasmid) in the supplementary may help clarify this.

Cloning strategy has been expanded with additional information for clarity.

1. Line 295: include abbreviation of cRPMI here rather than in Line 303

Has been corrected.

1. Line 322: typographical error on WR99210 working concentration?

Has been corrected.

1. Line 372: Last sentence on area and raw integrated density measurement is unclear.

We have reformulated the sentence for more clarity.

1. Line 461: typographical error in last sentence

Has been corrected.

1. Line 532: Figure 4E should be Figure 4F

Has been corrected.

Reviewer #3 (Significance):

DNA replication is vital to the survival of malaria parasites. A deeper understanding on their unusual form of replication may be exploited to find drug targets uniquely directed to the parasite. Biological insights from this work can also provide a jump-off point for unravelling unusual replication in other organisms. Data on the physicochemical analysis of centrin is not just of great interest for those in the field of parasitology, but also for those in the much wider fields of biology, physics and chemistry. Techniques presented in this work (e.g., DiCre overexpression with different promoters) can definitely be utilised for the elucidation of protein function within and outside the field of parasitology.

My field of expertise is in Plasmodium spp., particularly in parasite replication, molecular and cellular biology, and epigenetics.

We thank the reviewer for the appreciation of our work in terms of insight and technology development.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors have provided a comprehensive characterisation of centrin proteins in Plasmodium falciparum. Through expression of episomal GFP-tagged centrin for in vitro, they were able to observe co-localisation of centrin with centriolar plaques during the replicative stage of the parasite. They also utilised live cell STED microscopy to track dynamic changes in centrin morphology. They have also demonstrated calcium-dependent phase separation dynamics in bacterially-expressed P. falciparum centrin and human centrin 2. The formation of liquid-liquid phase separation in PfCen1, 3 and HsCen2 tied well with IUPred3 predictions of intrinsically disordered regions in these proteins. Using an inducible DiCre overexpression system with two promoters of varying strengths, the authors have shown accumulation of centrin1 outside of centrosomes and premature appearance of centriolar plaques. Finally, changes on the centrin1 protein, i.e., N-terminal deletion, and mutations in calcium binding sites in the EFh domains, have shown a reduction in the formation of ECCAs during overexpression and inability to form LLPS in vitro, respectively.

Major comments:

1. Given that parasites cannot tolerate endogenous C-terminal tagging of some centrins (but not all, as PbCen4 was successfully tagged), has N-terminal tagging been attempted either by the authors or in previous publications? Note that this is not a request for further experimentation; rather, maybe this can be noted in the manuscript; and line 62 can be rephrased for transparency.
2. Is there a possibility that by adding a C-terminal tag, centrin may lose a specific function or cause change in the physicochemical properties of the protein (thus making C-terminal tagging lethal)? Was His tag removal attempted so the native protein can be used in the LLPS experiments? IUPred3 analysis showed potential IDR at the C-terminal end of PfCen4. Could the C-terminal tag have caused the protein to not form droplets in the presence of Ca2+?
3. It has been shown by the authors that different tagged centrins co-condense which may support the localisation data (Figure 1C). However, is there a way to show that the episomally- and endogenously-expressed centrin co-localise with each other (e.g., confocal microscopy with anti-centrin vs anti-gfp in PfCen-GFP lines, that is if the authors have access to anti-centrin antibodies)? Has endogenous centrin been demonstrated to form ECCAs (in previous publications or by the authors)?

Minor comments:

1. How were the times (post addition of Ca2+) presented in Figure 2A determined?
2. Line 126: Figure 1B should be Figure 1C
3. Line 145: Figure 1C-D should be Figure 1D-E
4. Line 151: Figure 3A should be Figure 4A
5. Line 152: Suggest rephrasing "placing the gene of interest in front of the promoter" to "placing the gene of interest immediately downstream of the promoter" or something similar
6. Any growth phenotype changes observed in the overexpressors?
7. How often are ECCAs observed in pARL strains, or are they not observed at all? This might be good to mention.
8. Line 192 and Figure S8: n {less than or equal to} 33 (either a typographical error and should have been {greater than or equal to}, otherwise, it may be expressed as a range)
9. Line 258: Methods on the generation of FIO/FIO+ was a bit difficult to understand. Maybe a simple plasmid schematic with the restriction sites (at least for the original plasmid) in the supplementary may help clarify this.
10. Line 295: include abbreviation of cRPMI here rather than in Line 303
11. Line 322: typographical error on WR99210 working concentration?
12. Line 372: Last sentence on area and raw integrated density measurement is unclear.
13. Line 461: typographical error in last sentence
14. Line 532: Figure 4E should be Figure 4F

Significance

DNA replication is vital to the survival of malaria parasites. A deeper understanding on their unusual form of replication may be exploited to find drug targets uniquely directed to the parasite. Biological insights from this work can also provide a jump-off point for unravelling unusual replication in other organisms. Data on the physicochemical analysis of centrin is not just of great interest for those in the field of parasitology, but also for those in the much wider fields of biology, physics and chemistry. Techniques presented in this work (e.g., DiCre overexpression with different promoters) can definitely be utilised for the elucidation of protein function within and outside the field of parasitology.

My field of expertise is in Plasmodium spp., particularly in parasite replication, molecular and cellular biology, and epigenetics.

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

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Referee #2

Evidence, reproducibility and clarity

The authors analyzed the properties of the four Centrin proteins of the malaria parasite using a combination of in vitro and in vivo approaches. Their findings indicate that two of the four Plasmodium Centrin proteins, PfCen1 and PfCen3, as well as the human Centrin protein HsCen2, exhibit features of biomolecular condensates. Moreover, analysis of cells overexpressing PfCen1 indicates that such biomolecular condensates become more numerous as cells approach mitosis and are dissolved thereafter.

Major comments

• A) A critical point that requires clarification is how the protein concentrations used in the in vitro and in vivo assays (20-200 microM in vitro, and not estimated in vivo) compare to that of the endogenous components. This is important because it may well be that 6His-tagged PfCen1, PfCen3 and HsCen2 can form biomolecular condensates when present in vast excess, but not when present in physiological concentrations. The authors should report the estimated cellular concentration of PfCen1-4, as well as that achieved upon PfCen1-GFP overexpression (on top of endogenous PfCen1), for instance using semi-quantitative immunoblotting analysis. Given this limitation, the authors may also want to temper their title by introducing the word "can" after "centrins".
• B) Movies S1 and S2 (and the related Fig. 1D and 1E) are not the most convincing to support the notion that the observed assemblies are biomolecular condensates, as not much activity is going on during the recordings. Likewise, Movies S3, and even more so Movie S4, as out of focus for a large fraction of the time, making it difficult to assess what happens at the beginning of the process. Moreover, it appears that fusion events, while occurring, are rather rare. The movies should be exchanged for ones that are in focus, and ideally a rough quantification of fusion events as a function of biomolecular condensate size provided.
• C) An important control is missing from Fig. 2, namely assaying PfCen1-4 without the 6His tag, to ensure that the tag does not contribute to the observed behavior (although it can of course not be sufficient as evidenced by the lack of biomolecular condensates for PfCen2 and PfCen4).
• D) The authors should test whether the assemblies formed by PfCen1 and PfCen3 are sensitive to 1,6-hexanediol treatment, as expected for biomolecular condensates.
• E) The fact that HsCen2 also forms biomolecular condensates is very intriguing, but further investigation would be needed to assess the generality of these findings. For instance, the authors could test in vitro also S. cerevisiae Cdc31, the founding member of the Centrin family of proteins to further enhance the impact of their study.

Minor comments

1. For the experiments reported in Fig. 3D, the same concentrations as those used in Fig. 3A-C (namely 10 microM, and not 30 microM as in Fig. 3D) should be used. Moreover, it would be informative to test whether PfCen2 and PfCen4 as PfCen3 when added to PfCen1.
2. The authors mention that the effect of Calcium in inducing biomolecular condensates is specific, as Magnesium was not effective (lines 94-95). However, an examination of Fig. S3B indicates that the Magnesium also exhibits some activity, albeit less potent than Calcium. The authors should discuss this point and rectify the wording in the main text.
3. Do the authors think that PfCen2 and PfCent4 localize to the centriole plaque in vivo using another mechanism that deployed by PfCen1 and PfCent3? It would be good to discuss this point.
4. Given that the EFh-dead mutant exhibits no activity in vitro and fails to localize in vivo, one potential concern is that the protein is misfolded. The authors should conduct a CD spectrum to investigate this.
5. It is not entirely clear from the main text in lines 103-104, as well as from the legend, what Fig. S3B shows. When was EDTA added in this case?
6. Fig. S7: the correlation between PfCen1-GFP expression levels and ECCA appearance is modest at best. What statistical test was applied? This should be spelled out. Moreover, the authors should combine the two data sets, as this will provide further statistical power to assess whether a correlation is truly present.
7. The authors may want to discuss how their findings can be reconciled with the notion that Centrin assemble into a helical polymer on the inside of the centriole (doi: 10.1126/sciadv.aaz4137).
8. Likewise, the authors may want to speculate regarding what their findings signify for the role of Centrin proteins in detection of nucleotide excision repair (doi: 10.1083/jcb.201012093).

Small things

• Fig. 1A: change color for microtubules as red on red is difficult to discernn.
• Fig. 1C: the indicated boxes in the top row do not seem to correspond exactly to the insets shown in the bottom row.
• line 266: typo, promotor > promoter.
• line 360: a reference should be provided for the GFP-booster, including the concentration at which it was used.
• line 363: "an" missing before "HC".
• line 428: it would be best to deposit the macros on Github or an analogous repository.
• line 461: "to the" is duplicated.
• Fig. S5A: maybe draw the lines in red (as red in Fig. S5B correspond to the proteins that do not have IDRs).
• Movie S7, legend: left frames shows PfCen1-GFP, not microtubules as currently stated.

Significance

This is a provocative study that extends initial observations regarding self-assembly properties of Centrin proteins, and posits that some members of this evolutionarily conserved family can form biomolecular condensates. After the above outstanding issues have been properly addressed, these data could have important implications for understanding Centrin function in centriole biology and DNA repair. Therefore, these findings will be of interest to a cell biology audience.

Field of expertise: cell biology.

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Referee #1

Evidence, reproducibility and clarity

Voss, Reinert and colleagues show calcium-dependent assembly of Plasmodium falciparum centrins in vitro and in parasites. This assembly is dependent on the EF-hands of centrin and an N-terminal disordered region.

Major concerns:

1. The very definitive title is not wholly supported by the data. This should be qualified by specifying the conditions under which the centrins can accumulate in this way.
2. A major concern is whether this behaviour of centrins represents a biologically relevant mechanism in centriolar plaque formation. Is this limited to high overexpression conditions or in vitro high concentrations? Or is it a result of the tagging of the P. falciparum centrins? A convincing approach to addressing this issue would be to knock-in a fluorescent tag to the centrin loci. Roques et al. (ref. 12 in this submission) report the GFP tagging of centrin-4 in P. berghei, although they note that centrins-1 to -3 were refractory to tagging in this organism. It is unclear whether Voss et al. attempted this tagging in P. falciparum. This should be clarified and relevant data presented.

If the tagged molecules used in the biochemical parts of this study are functional, It is challenging to understand why the centrins cannot be tagged in P. falciparum. If the tags render the P. falciparum centrins dysfunctional, the study becomes significantly less useful.<br /> 3. If a knock-in cannot be achieved, it must be shown that the transgenic expression of tagged Plasmodium centrins does not confound the analysis of centrin behaviour. It is known that these proteins can behave anomalously when overexpressed (Yang et al. 2010, PMID: 20980622; Prosser et al. 2009, PMID: 19139275), at least in other species.

A previous description of centriolar plaque from the authors' lab (Simon et al. 2021, PMID: 34535568) shows an organized structure of an established size. It should be demonstrated whether the structures formed with the GFP tagged centrins show the same dimensions and dynamics as those in wild-type parasites. The extent of the overexpression of the GFP-tagged centrins should also be demonstrated.<br /> 4. It would also be useful to remove the His tag from the recombinantly expressed and purified centrins for the in vitro analyses, particularly if concern remains about the impact of tags on Plasmodium centrin behaviour.<br /> 5. The discussion is very short and does not consider the findings presented here in the context of the literature, with respect to centrins, Plasmodium MTOC assembly mechanisms, or to general considerations around biological condensates. Andrea Musacchio's recent commentary (ref. 44 in the current submission) advocates caution in ascribing phase separation as an assembly mechanism for organelles in vivo, particularly on the basis of in vitro experiments with high concentrations of homogeneous protein. It is not clear that the concentration dependence of extracentrosomal centrin accumulations (ECCAs) at the onset of schizogony provides sufficient justification of a phase separation model in vivo. The authors' recent description of the involvement of an SFI1-like protein, SIp (Wenz et al. 2023 PMID: 37130129), in the centriolar plaque makes a case for non-homotypic interactions also driving assembly and alternative models for ECCA are not convincingly excluded. The absence of a robust discussion of such considerations is unhelpful to the reader.<br /> 6. It is also unclear whether the analysis of human centrin is suggested to indicate a phase separation mechanism for centrins in human cells. As this is readily testable, this notion could be considered further. Although its experimental examination may lie outside the theme of this study, one would expect some discussion of the significance of the data presented in the study.

Minor points

1. There are only three centrins in humans. Centrin 4 is a pseudogene (Gene ID: 729338 on NCBI).
2. Line 175 should say 'temporally', rather than 'temporarily. The Abstract should say 'evolutionarily conserved', rather than 'evolutionary conserved'. 'To condensate' is not ideal as a phrase- 'to form a condensate' would be clearer.

Referees cross-commenting

I think the other 2 reviewers have made fair, cogent and constructive points. There is good convergence between the reviewers on the significant issues around the study. These concern in vivo and in vitro effects of tagging and of of high concentrations.

Significance

The biology of the Plasmodium centriolar plaque is of great interest as an alternative MTOC structure, with obvious additional interest deriving from the role of this organism in malaria. Much remains to be learned about this structure, so the topic of this paper is likely to attract a broad readership. Furthermore, the centrins are a widely-expressed and evolutionarily conserved family of eukaryotic proteins, with multiple roles; a new model for their behaviour, such as is suggested here, would be of interest to many cell biologists.

With that in mind, significant additional data should be provided to substantiate the model proposed by the authors.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript by Schauer et al. uses embryonic explants to study the coordination of Nodal and BMP signaling for embryo morphogenesis. They show that Nodal signaling triggers explant elongation by inducing mesendodermal progenitors that undergo cell intercalation. Looking at the role of BMP signaling, they show that BMP overactivation ventralizes the explants, reducing cell intercalation and therefore explant elongation. Looking at pSmad5, they then establish that BMP signaling in the explant is attenuated by Nodal signaling, through activation of chordin expression, and through some unidentified chordin-independent mechanisms. Moving to the entire embryo, using combinations of BMP overexpression and Nodal inhibition, authors show that Nodal signaling limits BMP signaling on the dorsal side of the embryo, which is key to proper embryo elongation.

Major comments:

• The authors used the sebox::EGFP line to show that the growing region of the explant consists mostly of mesendodermal cells. Although this transgenic line had not been used to do so, the authors and others, had previously demonstrated that the extending part of the explant is mostly made of mesoderm and even shows some patterning (1,2). This should be stated and not presented as a new finding.
• Explant elongation is driven by cell intercalation. The authors analyzed the shape of the mesendodermal tissue to conclude that cells intercalate. While I do not question this conclusion, as it is well known in the embryo, direct observation of cell intercalation, as was done in the embryo (3), would be a better demonstration.
• Explant elongation is driven by mesendodermal cell intercalation. I certainly agree from the movies and images that the extending region is mostly made of mesendoderm. However, it seemed clear to me that in Movie 1, starting at about 140 minutes, most of the convergence movement is taking place in a non-green region of the explant, fueling the extension of the mesendodermal region. Also, to demonstrate that cell intercalation is occurring in the mesendoderm, the authors performed clone dispersal analysis, comparing clones of mesendodermal and ectodermal cells. However, the selected ectodermal clone is very far from the extending region. To show that the cell intercalation is specific to mesendoderm, I think the authors should try to compare the behavior of mesendodermal and non-mesendodermal cells that are located at the same distance from the extending region. For example, from the image in Figure 1E (235 mpe), it appears that the right side of the base of the extended region is not green and could be compared to the left side. Currently, the quantification shown in 1G mostly demonstrates that the extending region is extending, and that the non-extending region is not.
• Based on their observations in explants, the authors propose that Nodal signaling maintains an area of low BMP signaling on the dorsal side of the gastrula for robust axis elongation. While I acknowledge that the experiments performed by the authors have not been previoulsy reported, I did not understand how this differs from the very well established fact that Nodal inhibits BMP signaling, in particular through chordin expression. Von der Hardt for instance already reported that overexpression of bmp and inhibition of chordin leads to severe elongation defects (4). More insight could probably be gained by analyzing the effect in more detail: Is the elongation defect due to cell intercalation defects? How are cell fates affected? Is this Nodal effect mediated by Chordin?...

Minor comments:

• Fig6B. Are the curves significantly different? If so, how were they compared?
• Fig6D-E, I found the quantification a bit confusing. The reader is left with the impression of an all-or-nothing answer (effect only with BMP overexpression and strong Nodal inhibition), whereas the effect on the pSmad5 gradient is gradual. Plotting and comparing the pSmad5 intensity gradients would be better.
• Fig6G. 'Axis length/embryo height' should appear on the x-axis, not the y-axis.

Referees cross-commenting

I feel that the three reviews are very much in agreement, recognising that the experiments carried out are well done and calling for a reasonable amount of additional data. The three reviews also agree that the results obtained here in explants were already known from intact embryos, limiting the relevance to ex vivo research.

Significance

Overall, the experiments appear carefully carried out, and very precisely quantified. The paper is well written and easy to read. The results add to our understanding of the morphogenetic events occurring in embryonic explants. I therefore support their publication.

My main concern is with the significance of the results. I am convinced that embryonic explants are great tools, to reduce the complexity of the embryo and to address questions that cannot be addressed in the embryo, as the authors and others have done, for instance, to address the role of extraembryonic tissues and patterning by maternal contributions. Here, however, I felt that most, if not all, of the experiments essentially demonstrate in embryonic explants, results that have been known for years in the intact embryo. While gathering detailed information on what happens in embryonic explants will certainly prove useful in further understanding the self-organizing abilities of these explants, and is worth publishing, the significance of the results reported here seems limited. Specifically, that elongation is driven by cell intercalation, that BMP-mediated dorsoventral patterning affects cell intercalation, that BMP signaling is attenuated by Nodal through Chordin, that Chordin is required for elongation, has been well established in the embryo over the last 20 years. Again, showing that it works the same way in embryonic explants is of interest, but at this point, does not add to our understanding of embryonic development.

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Referee #2

Evidence, reproducibility and clarity

This paper from the Heisenberg lab takes a reductionist approach to understanding how BMP and Nodal signaling interact to coordinate morphogenesis. They mostly use blastoderm explants that they culture in vitro. These explants elongate over time, with Nodal signaling that induces mesendoderm driving the cell intercalations that explain the elongation. They show that increased BMP signaling inhibits this process, but reducing BMP signaling has no effect. They see that reducing Nodal signaling results in an upregulation of BMP activity as read out by phosphorylated Smad5 staining and increasing Nodal signaling has the opposite effect. They explain this mostly by the observation that Nodal induces the expression of the BMP antagonist, Chordin, and validate this idea by demonstrating that a reduction in Chordin expression reduces explant elongation. Returnign to the embryo, the authors show that manipulation of Nodal signaling levels influences the size of the BMP activity gradient as expected from the in vitro results. Finally, they show that reduction of Nodal signaling with SB505124 sensitises the embryos the effects of bmp2b overexpression, and that BMP overeactivation at 90% epiboly reduced C&E movements.

Major comments

In general I think the work is well done and the data justify the conclusions.

I have several suggestions for additional experiments and discussion that I think would improve the paper.

1. In Figure S1 they present data on elongation of explants treated with a Nodal inhibitor. It would be good to show some examples of images of the explants.
2. In Figure 1G and 3A, the same wildtype images are shown. This is mentioned and I assume therefore that the results were all part of the same experiment. How many times were these experiments performed? It would be much better to use different biological replicates in the two figures.
3. It is important for the authors to make clear how many biological replicates each of the experiments correspond to.
4. In Figure 4E, it would be good to show the levels of P-Smad2 in the Oep and MZ lefty1, 2 explants.
5. On page 11 the authors mention chordin-independent inhibition of BMP signaling. The most likely candidate would be noggin as it too is expressed dorsally and is at least in part activated by Nodal. This should be tested in their model.
6. The authors focus on Chordin as downstream of Nodal signaling, and discuss the role of Nodal signaling in inducing chordin as being due to peak Nodal signaling. However, Chordin has been shown to also be downstream of Fgf signaling and Bozozok (PMIDs 23499658 and 16873584), which likely explains its dorsal expression domain. Furthermore, Rogers et al, (PMID 33174840) who the authors refer to, also show that to disrupt BMP signaling in embryos, inhibition of Nodal and Fgf is required. These issues need to be discussed in more detail. It is the combinatorial signaling that is thought to be responsible for the dorsal location of the chordin (and noggin) expression domains.

Minor comments

I think in general the manuscript is well written and the figures are clear. Previous data is generally well cited. My only comment is that there is a wealth of data from Xenopus and zebrafish that BMP antagonists are induced as a result of combinatorial Nodal signaling and other pathways (dorsal wnt and fgf) that inhibit BMP signaling. I think this could be better referenced.

Significance

The paper is well done and provides important information about the interactions between Nodal and BMP signaling to induce axis elongation. I think the work would be improved if the authors revise it along the lines suggested above. In terms of novelty, many of the component parts of the paper are known (Nodal signaling is important for elongation via cell intercalation and Nodal and BMP can antagonize on another by the induction of BMP antagonists by Nodal), but it is novel to put them together to investigate axis extension using explants. The paper will be of interest to those interested in how these signaling pathways operate in early vertebrate development and to those interested in morphogenesis.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors presented intriguing observations on the molecular mechanisms regulating morphogenic cell movement, with a particular focus on convergent-extension (CE) movement associated with cell type specification in the zebrafish blastoderm explant. In this manuscript, Schauer et al. identified the CE movement of the mesendoderm as triggering the elongation of the zebrafish embryonic explant. In this process, the Nodal signal represses the BMP signal, which negatively regulates the movement of the mesendoderm precursors, through the induction of its inhibitor chordin. This suggests that the Nodal signal is the key factor coordinating cell fate specification and morphogenesis in the zebrafish blastoderm explant. Finally, suppression of Nodal signalling increases sensitivity to BMP signalling in the CE movement of intact embryos. This suggests that promotion of mesendoderm cell intercalation via BMP suppression by Nodal may be involved in conferring robustness to morphogenic cell movement in vivo.

Major comments

1. While one of the main conclusions of this manuscript is that "Nodal signaling regulates CE movement of mesendodermal cells by promoting their intercalation through inhibition of BMP signaling". However, this was predicted by changes in individual cell morphology and cell dispersal, and the authors didn't directly examine the behavior of individual cells. It would be better to confirm intercalation during the process of explant elongation by cell tracking analysis.
2. Although the authors discuss that Nodal signaling inhibits BMP signaling in the later gastrulation stage, this has not been experimentally tested. If possible, the time window in which Nodal signaling acts should be investigated by temporal inhibition of Nodal signaling using chemical inhibitors.
3. Only the signal gradient of pSmad5 and axis elongation were examined in the intact embryo part of the study (Fig. 6 and Fig. S7). The information on the domain of pSmad2 and the expression of chordin would be helpful for the comparison of the blastoderm explant and the intact embryos.

Minor concerns

The first letter of a gene name should be in lowercase. ( ex. Fig.S3C; Smad5 MO)

Significance

The zebrafish blastoderm explant assay has the potential to elucidate the molecular mechanisms regulating the complex processes of morphogenesis during vertebrate gastrulation, as the authors demonstrate in this paper. In this manuscript, the authors addressed the molecular mechanism coordinating cell fate specification and morphogenic cell movement in the blastoderm explant. All of the experiments are well-designed, the interpretation of the results is convincing and the paper is well-written. Also, the conclusion is very clear and well supported by the presented data. These findings provide fundamental and important insights for studying morphogenic cell movements in early vertebrate embryos using zebrafish blastoderm explants. On the other hand, most of the molecular mechanisms reported in this manuscript are already predicted by previous studies using intact embryos. Therefore, the impact of this work may be limited to ex vivo research.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Summary: This manuscript describes molecular mechanisms by which ACBD3 is recruited to the Golgi complex. ACBD3 recruits PI4KIIIb which is required to generate PI4P, a phosphoinositide which is key for the recruitment of essential Golgi proteins and hence is key to Golgi identity. The authors have used a combination of mass spectrometry, high quality fluorescence imaging, transient CRISPR knockdowns, and biochemical approaches such as IPs to identify the key determinant for recruitment of ACBD3 to the Golgi complex. They map the interaction between ACBD3 and the Golgi as a unique region (UR) upstream of its GOLD domain, identifying, in particular, an MWT motif as key for this recruitment. Using mass spectrometry they identify several novel interactors of ACBD3 as well as some established binding partners. Knockdown of these interactors reveal a key role for the SNARE, SCFD1, where reduced levels lead to complete loss of ACBD3 localisation to the Golgi without apparent disruption of Golgi structure. They further validate this interaction and that of another SNARE (Sec22b), which is part of the same SNARE complex as SCFD1, mapping the interaction to the longin domain of Sec22b. Surprisingly however they demonstrate that the UR domain does not mediate the interaction between ACBD3 and these SNAREs suggesting an alternative mechanism of recruitment. Previously identified ACBD3 interactors, Golgi proteins giantin and golgin-45 were also identified in the mass spectrometry screen and the authors demonstrate that these two proteins can recruit ACBD2 to the Golgi and this is dependent on the MWT motif identified in the UR domain. By knocking down SCFD1, they show reduced recruitment of ACBD3 leading them to propose a model of sequential recruitment of ACBD3 by SCFD1 followed by interactions with the golgins.

Major points: This study is a well-executed and rigorous study of the molecular requirements for the recruitment of ACBD3 to the Golgi. The experimental approaches are state-of-the-art and the data are clean and convincing. The only caveat, raised by the authors themselves, is their interpretation that there are two sequential steps for Golgi recruitment of ACBD3. While they show that loss of SCFD1 reduces the interaction of ACBD3 with giantin and golgin 45, their model depends on doing the reverse experiment, i.e. assessing the effects of knocking down either giantin or golgin-45. This is especially relevant given the demonstration that golgin-45 is sufficient to recruit ACBD3 to mitochondria. It may well be that recruitment involves a tripartite complex, which is not uncommon in vesicular transport mechanisms Giantin is not an essential protein do it should be feasible to perform this experiment. The authors are equipped in the quantitative fluorescence microscopy which would be required and which would help resolve whether sequential or redundant mechanisms are required for ACBD3 recruitment.

We thank the reviewer for the positive comments and are glad that they consider our study "well-executed and rigorous". We totally agree with the reviewer that our conclusions regarding the sequential aspect of the recruitment of ACBD3 in the original submission could be better supported. We have worked to strengthen this in our resubmission. As the reviewer states, this limitation was already discussed in the original submission. To further support our model, we have performed the experiment suggested by the reviewer, in which we test the effects of knocking down both giantin and golgin45 (double knockdown) on the binding of ACBD3 to SCFD1.

The results of this experiment further support our sequential model with little to no effect of loss of the Golgins on ACBD3. As we already knew, a large effect of SCFD1 KO on the binding of the Golgins to ACBD3 was also observed here. We should note that this was performed in a different cell line than before (HeLa cells rather than HEK cells), as the efficiency of multiple knockdowns was much lower in HEK cells, as determined by qPCR. Taken together, the new data in Figure 7 supports a sequential model for Golgi recruitment. We also agree that other, less likely models could explain our data and have included this openly in the discussion. In conclusion, we thank the reviewer for their comments and have revised the manuscript with a new experiment with the relevant repeats, which supports our model.

Reviewer #1 (Significance):

Significance PI4P is a phosphoinositide that is important for the recruitment of Golgi proteins. As with most PIs it is likely to act by coincidence detection in that Golgi associated proteins will recognise PI4P as well as other factors on Golgi membranes. This results in different local membrane environments which will be specific for particular functions. PI4KIII__b_ is key for PI4P production although the absolute levels of PI4P are likely to be determined by a balance of lipid kinases and phosphatases. However, since ACBD3 is key for the recruitment of PI4KIII__b, it is important to understand the molecular mechanisms by which it is recruited. The manuscript thus makes a significant contribution to understanding one of the underlying mechanisms for PI4KIII__b _recruitment although, as indicated above, stops short of establishing a clear model for the roles SCDF1 and Sec22b versus golgin 45 and giantin. For the future it will be of interest to determine why either a sequential or a redundant mechanism is required for the recruitment of ACBD3 as a scaffold protein.

We thank the reviewer for this set of positive comments on the manuscript and for agreeing that this is a significant contribution. Our revised version further supports our sequential model of ACBD3 recruitment to the Golgi apparatus, and the comments here have helped us further to strengthen the quality and clarity of the manuscript.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary This is a very interesting and potentially important paper for the field of membrane biology and membrane trafficking, in which the authors have studied the molecular mechanisms by which ACBD3 (and consequently PI4KIIIb) is recruited to the cis-Golgi membranes. The authors suggest that this recruitment is based on a two-step process, mediated by interactions to, on the one hand, SCFD-1 (SLY1) and, on the other hand, two redundant golgins (golgin-45 and giantin).

We once again thank the reviewer for the positive comments and are glad that they consider our manuscript important.

Comments:- Pg.1 : arfaptins, as far as I know, have not been shown to be involved in intra-golgi trafficking but rather in Golgi export (see e.g. ref. 12)

We thank the reviewer for pointing this out. We have corrected the text accordingly.

• Pg. 1: reigon --> region

We thank the reviewer for noticing this typo. We have corrected the text accordingly.

• Arf1 also recruits PI4KIIIb right?

This is correct. The De Matteis lab has shown that PI4KIIIβ associates with the Golgi complex in an Arf1-dependent manner (Godi et al. 1999). We think this is excellent work. However, Arf1 is somewhat of a master regulator of the Golgi, affecting the recruitment and localisation of many different Golgi proteins. It has also previously been reported that Arf1 does not directly interact with PI4KIIIβ (Klima et al. 2016). Overall, the molecular relationship between Arf1 and the kinase remains unclear. We do not exclude, however, that there are factors other than ACBD3 important for recruiting and regulating PI4KIIIβ levels at the Golgi. We have changed the wording in the manuscript to reflect that there are multiple ways that PI4KIIIβ is recruited to the Golgi apparatus.

Fig. S1: the information about the number of cells per experiment is missing. Also, please add the information about what exactly is represented in the box plots (is it the distribution of the mean value of R per experiment? or the total distribution on a cell-by-cell basis of a representative experiment?)

For each experiment, a minimum of 100 cells per condition were imaged. The Pearson's correlation was then calculated, and the average was taken for each biological repeat. The plot in Fig. S1B represents 3 independent biological repeats. We have included this information in the revised manuscript.

• The definition of Avg. Golgi int/avg. cell int. (a.u.) in Fig 1E,F is a bit difficult to understand to me. If I understand correctly, the total fl. int in the Golgi mask was computed and divided by the area of the Golgi mask (this is the av. Golgi intensity). A similar computation is done for the entire cell (including the Golgi), i.e., total fl. intensity in the cell mask is computed and divided by the area of the cell mask. Then the two av. intensities are divided (ratio = av. Golgi int / av. cell int.). This ratio, for a protein that is enriched in the Golgi area, should be larger than 1. For a protein that is equally distributed all over the cell, it should be 1, and for a protein that is excluded from the Golgi area, smaller than 1. Then to this value, the authors subtract the value of the ratio found for an inert construct (GFP of Halo alone), which I imagine should have an original ratio value of the order of 1, and hence, after this subtraction, norm. ratio values larger than 0 mean that they are more enriched at the Golgi area than GFP/HaloTag themselves. Is this correct? In principle, I don't see anything entirely wrong with this way of thought, but I just found it a bit difficult to understand, and in general one has to be careful when computing rations (quotients) and then subtract another ratio. Also, the units are not a.u., the value is dimensionless, what is "arbitrary" is the definition of 0 value and the based on this definition, also the actual value. I think it would probably be much clearer for the readers to compute somthing like the relative enrichment in the Golgi area as compared to the rest of the cell (excluding the Golgi area). That is, a value r'=(Int. Golgi mask / Area Golgi mask) / [(Int. Cell mask - Int. Golgi mask)/(Area cell mask - Area Golgi mask)]. This can be computed directly or defining a mask that is the cell mask - the Golgi mask. Also, some maths (unless I made a mistake) give that this r'= r (1-aG)/(1-r aG); where r is the ratio (before subtraction) defined by the authors, and aG=Area cell mask/Area Golgi mask. In any case, I'd suggest the authors to either adopt this other quantitation (without subtraction of the GFP/HAloTAG), which gives directly the fold-enrichment in the intensity density in the Golgi area with respect to the rest of the cell; or explain in more detail the maths of the value they are plotting now.

We thank the reviewer for these well-reasoned and thoughtful suggestions for our imaging analysis. These are issues that we have also considered when quantifying this dataset. At the heart of it, the second method of calculation (Golgi/outside of Golgi), results in a non-linear distribution, as the pool of proteins re-distribute from inside the Golgi to the cytosol. This is why we have chosen to use the first method of Golgi/total, as it provides a linear distribution.

The reviewer is also correct that the GFP (inert protein) ratio is 1 without adjustment. We have chosen to normalise to GFP/HaloTag (inert protein) as we think this is the clearest way of conveying our conclusions from these experiments. We have included the non-normalised graph here for the reviewer to see; however we thought that this conveys the key result less clearly. Overall, we agree this was poorly communicated in the manuscript and we have clarified it in the revised version.

• Fig. 1C&F: Besides the MWT mutant, the FKE mutant also seems to have a somewhat compromised Golgi localization. Have the authors followed on that, or what is the reason that they have just focused on the MWT mutant?

In contrast to the MWT mutant, the FKE mutant does not affect ACBD3 localisation significantly. In addition, when having a close look at the pdb structure of the GOLD domain of ACBD3 with 3A protein of Aichivirus A (5LZ3), the MWT patch, in particular residues M and T, make clear contact with protein 3A, which is not the case for FKE residues. Therefore we focused on the MWT residues, which we hypothesised to interact with a Golgi resident protein which competes with protein 3A to interact with ACBD3.

• Very minor point, and without wanting to sound pedant at all, but I think (I might be wrong of course, so apologies if I am) that the plural of apparatus in latin is not apparati, but apparatus (fourth declination). So, I'd change the word in page 2 (or just rephrase the sentence: e.g. "resulting in Golgi fragmentation"). But of course, I'd leave this to the authors' discretion.

We thank the reviewer for this precision, do not consider it pedantic, and have made the suggested change to the text.

• Fig. 3A: have the authors tried or been able to perform IF of the endogenous SCFD1 protein?

As suggested by the reviewer, we attempted to perform IF of endogenous SCFD1, as shown below. Despite trying several different antibodies, we were not satisfied that we were detecting real SCFD1 signal as there was no change in this staining upon SCFD1 CRISPR KO. Please see an example of this IF below (ProteinTech, 12569-1-AP). We have contacted the antibody manufacturers to inform them of this issue.

• Similarly to what has been done for other panels, could you quantify Fig. 3C? Are PI4KIIIb protein levels affected upon the different KOs?

As suggested by the reviewer, we are now showing in Figure S2D the percentage of cells with a partial or total loss of PI4KIIIβ at the Golgi in CRISPR-Cas9 KO cells of either PI4KIIIβ, ACBD3 or SCFD1. 3 independent biological repeats were performed and approximately 150 cells were quantified (~50 cells per condition). The results show that the PI4KIIIβ antibody used (BD Bioscience, 611816) is specific (93.22% of cells lose the antibody signal) and that ACBD3 and SCFD1 KO affects PI4KIIIβ recruitment to the Golgi in 88% and 73% of the cells, respectively._-

The last paragraph of the "SCFD1 and ACBD3 interact upstream of PI4KIIIβ recruitment to the Golgi apparatus" section reads a bit odd placed there. I think it is more appropriate for the discussion or for the intro part on SCFD1.

Many thanks to the reviewer for pointing this out. We simplified that paragraph to describe the relationship between SCFD1 and SEC22B.

• I am confused on Fig. 5A/B. The labels in the blots show that 390-528 (without UR) does not bind sec22 or scfd1, but the 368-529 does? Or I guess, judging by the MW seen in the middle blots, that there's some error in the labelling?

Many thanks to the reviewer for noticing this, which was clearly a labelling error. We corrected this accordingly in Figures 5A and B. We apologise for this oversight.

also, the IP efficiency of the MWT mutant in the panel A blot is quite low, still sec22 seems to be very efficiently pulled down. Can the authors comment on that please? Would co-IPing against endogenous sec22 and scfd1 would work (so you don't need to rely on HaloTag+ligand?)

We know that the MWT residues of ACBD3 are important for recruiting ACBD3 to the Golgi (Figure 1C and F). We also know that ACBD3 interacts with SEC22B and SCFD1 (Figure 3B and 4A) and that SCFD1 is important for ACBD3 Golgi recruitment. Therefore we initially speculated that ACBD3 interacts with SEC22B and SCFD1 through the MWT residues. However, as the reviewer points out, Figure 5 shows the opposite. Mutating MWT residues makes the interaction of ACBD3 with SEC22B and SCFD1 stronger. For this reason, we hypothesised that another player(s) also contributes to ACBD3 recruitment through interactions with the MWT residues. We have shown that the second recruitment factors are the 2 golgins, golgin-45 and giantin (Figure 6C). In short, whilst we agree that the IP efficiency is low, the binding is actually stronger, supporting our conclusions. No interaction of ACBD3 with endogenous SEC22B could be detected due to a lack of a sufficiently sensitive antibody (we tried Abcam ab181076 and ProteinTech 14776-1 AP).

• I really like the experiment 6B. Have the authors tested whether SEC22 is also recruited to mitochondria in those conditions? But not SCFD1?

We thank the reviewer for the positive comment. We have performed the suggested experiment and are now including this as an additional figure (Figure S3). Ectopic expression of golgin-45 targeted to the mitochondria is not sufficient to redistribute SCFD1-HaloTag or HaloTag-SEC22B to the mitochondria (Figure S3A and B, respectively). We, therefore, speculate that the fraction of ACBD3 that gets redirected in Figure 6B must be the small fraction of ACBD3 that is spontaneously in an open conformation and compatible for interaction with golgin-45.

• The results shown in Fig 7 might show a partial depletion in the interactions, but to be fully trusted they would need to be quantified and a statistical test used to compare the values. I think this part is important to show very clearly, because even with low binding to golgins (remember, single knockouts do not prevent Golgi localization of ACBD3), one could expect that ACBD3 still localized to the Golgi but it does not in the absence of SCFD1 as shown in this paper. A prediction of the proposed model is that in cells depleted of the two Golgins, SCFD1 and ACBD3 should still bind to one another, right? Did the authors test this?

We fully agree with the reviewer. As discussed in the replies to reviewer 1, we have repeated this experiment, including both sets of KO. This was not trivial, as a double transient KO is technically challenging and involves validation with qPCR and switching cell types (HEK cells to HeLa). The new data supports our current model and suggests some additional regulatory mechanisms at play.

• The model presented here (fig 8) seems to suggest that only the conformational variation of ACBD3 that binds Golgins is able to recruit (bind) PI4KIIIb. Is this known, or is there any experimental evidence for that?

HDX-MS experiments show that the ACBD and GOLD domains undergo conformational changes in the presence of 3A proteins (McPhail et al. 2017). Demonstrating this would require a complicated reconstitution experiment which is technically very challenging and would involve purifying various complex proteins, including SNAREs, SM proteins and golgins. This could perhaps be the subject of several future studies.

• Have the authors thought about testing the FKE mutant in the experiemnts shown in Fig. 5?

As mentioned above, since the FKE residues are not making any contact with the protein 3A and since the loss of ACBD3 recruitment to the Golgi is not statistically significant (Figure 1F), we haven't tested the FKE mutant for the binding to SEC22B and SCFD1. We do, however, agree with the reviewer that there might be something interesting happening here. We would like to experimentally interrogate this in future studies and develop more sensitive assays to test if there is a significant effect with the FKE mutant.

In general, I think the title might be a bit misleading because of the use of PI4Kiiib. I understand what the authors mean, but because they have not thoroughly tested PI4Kiiib recruitment in their experiments, I think they should focuse rather on the mechanism of recruitment of ACBD3 the authors have found.

We thank the reviewer for their advice regarding the manuscript title, and this is something that we have discussed internally. We chose that title as it highlights the key mechanistic impact of our findings and note that we did include a figure on the recruitment of PI4KIIIβ. However, we remain open to discussing this with advice from the journal editorial team.

Reviewer #2 (Significance):

I think, as said above, that this is potentially an important paper for the field of membrane trafficking and membrane biology. Most of the experiments are in general well performed and well controlled, and the paper is clearly written and follows a logical line.

We once again thank the reviewer for their comments and overall thoughtful and considered review. We believe that the suggestions here have improved the manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Stalder and colleagues report experiments designed to identify interactors of the Golgi-localized protein ACBD3 (a.k.a. GCP60), and to delineate mechanisms that allow ACBD3 to localize at Golgi compartments. ACBD3 is a 528aa protein with diverse previously reported interactions and functions, both in normal physiology and as a host factor in viral assembly processes. Stalder et al. first map which domains of ACBD3 are required for Golgi localization in HeLa cells, concluding that residues 368-528 are sufficient for localization. This region includes a GOLD (GOLgi Dynamics) domain previously reported to interact with Golgin tethering proteins. Alanine scanning identifies the motif MWT just upstream of the GOLD motif as necessary for Golgi localization. Acute CRISPR knockout identifies two Golgins, Golgin45 and Giantin, as necessary for ACBD3 Golgi localization, and IP indicates that the MWT motif breaks this interaction. These data are a bit scattered around the paper but taken together are reasonably persuasive, particularly when viewed in context with published work. This reader would have found the manuscript easier to follow had the Golgin and MWT motif data been presented en bloc.

We thank the reviewer for these comments and have considered presenting and rewriting the data as the reviewer suggested. On reflection, we have decided to present it in the original order. We feel that this allows us to highlight the two independent mechanisms individually, bringing them together at the end. In addition, as the experiments were performed in the order presented, it allows for more appropriate controls for each experiment rather than trying to combine them. We hope the reviewer accepts our preferred order.

In a second set of experiments, IP-mass spec is used to identify ACBD3 interactors that might assist in the protein's localization. The MS data presented are filtered to exclude proteins not already identified as Golgi-localized. This is, I think, a mistake. Even if the authors choose to focus on known Golgi interactors as candidates for a localization function, the biological functions of ACBD3 are far from fully understood, and the full dataset would be of value to both cell biologists and virologists.

We agree with the reviewer that there are many interesting mysteries surrounding ACBD3 and have therefore included an additional table (table S1) in the revised manuscript, showing the dataset of newly identified ACBD3 interactors before applying the Golgi localisation filter.

Hits in the filtered dataset include the R-SNARE Sec22B, and the SNARE chaperone Sly1/SCFD1. Acute CRISPR inactivation of Sec22 decreases ACBD3 localization to the Golgi and SCFD1 inactivation more or less abolishes localization. Co-IP experiments are used to argue that ACBD3 interacts with the N-terminal regulatory Longin domain of SEC22B, as well as with SCFD1. The Sec22 data are more detailed and persuasive. No experiments with purified proteins are presented to establish that the detected interactions are direct rather than mediated through a bridging factor or factors. Importantly, SCFD1 is likely to have multiple different client SNARE complexes that operate at different stages of ER and Golgi traffic. Hence its inactivation is likely to be pleiotropic and consequently phenotypes arising must be interpreted with caution.

We completely agree that studying membrane trafficking in an interconnected system is challenging. We also agree that direct binding experiments in reconstituted systems would be key to proving our model. Our data uses multiple different experimental approaches, including co-localisation, co-immunoprecipitation, CRISPR-KO, and biochemistry, to support our model. In the future, we agree full reconstitution would be necessary to examine this further, and we hope that either ourselves or others can do this in further studies.

Lastly, the authors perform IP experiments which show that ACBD3-Golgin co-IP efficiency is lower in cells with acute inactivation of SCFD1. This epistatic relationship is used to argue for a sequential model of recruitment with SCFD1 and perhaps client SNARE proteins operating upstream of ACBD3-Golgin interaction. This argument is not persuasive because we do not know whether SCFD1 and its downstream activities increase the rate of ACBD3-Golgin complex asssembly, or alternatively stabilizes ACBD3-Golgin complexes, decreasing the rate of their dissociation.

We agree with this weakness in our original submission, and it is a comment shared among all reviewers. Overall, we feel that we have chosen the model that best summarises our data. We, of course, accept that there are still components of this pathway that need clarification and are open for further study. This includes the issue raised here by the reviewer, as well as the intriguing observation that both golgins are transcriptionally upregulated upon SCFD1 KO in HeLa cells. In the revised manuscript, we have more clearly laid out the weaknesses of our model in the discussion and suggested future experiments to help clarify some of these issues. We have also modified the model to reflect some of these potential additional regulatory mechanisms.

In general the methods are fairly clear but that there is room for improvement. The "high throughput" imaging pipeline is not clearly described.

We agree with the reviewer, and apologise for not clearly explaining this. We feel that this unbiased approach of quantification is particularly rigorous and we have clarified this in the methods section of the updated manuscript.

Each figure legend should specify the microscopy methods used, and for each result the number of biological replicates and cells analyzed should be specified.

We agree with the reviewer and have included these details appropriately in the revised manuscript.

The statistical methods (Student, Tukey, etc.) used for each experiment should be specified. Saying that statistics were calculated using Python 3.7 is useless without additional details. e.g. at least the libraries and codebase used should be indicated or deposited.

We agree with the reviewer and have updated the manuscript accordingly. In short, all comparisons were made using either Student's t-test or Multiple Comparison of Means - Tukey HSD, FWER=0.05. These were conducted in Python 3.9 using pandas, matplotlib, seaborn and scipy. We used the MultiComparison function in scipy, and the comp.tukeyhsd for the post-hoc adjustment.

Many figure labels (e.g. Fig. 2) use absurdly small fonts.

We apologise for this. We believe that this is because we submitted it with in-line formatting. Our resubmission has full-page figures, and we feel the text is clearer now.

The mass spec hits obtained should be provided both with and without exclusion of non-Golgi-localized proteins.

We agree with the reviewer. Please see the new Table S1.

Reviewer #3 (Significance):

In general I think this is a useful and well controlled set of experiments producing useful insights. However, the interpretations need to be more carefully considered, and alternative interpretations must laid out as clearly as possible. Specifying the limitations of the study will make it more, not less, useful to the field. If the authors want to make the case more robustly that the interactions described are mediated through direct binding, or that the operation of SCFD1 and Golgins operate sequentially to recruit ACBD3, additional wet bench work will be required which will of course take time to complete.

We once again thank the reviewer for the thoughtful and critical comments. These have helped to strengthen the manuscript. We have performed the additional bench work requested by the reviewer, which has further supported the paper and our model.

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Referee #3

Evidence, reproducibility and clarity

Stalder and colleagues report experiments designed to identify interactors of the Golgi-localized protein ACBD3 (a.k.a. GCP60), and to delineate mechanisms that allow ACBD3 to localize at Golgi compartments. ACBD3 is a 528aa protein with diverse previously reported interactions and functions, both in normal physiology and as a host factor in viral assembly processes. Stalder et al. first map which domains of ACBD3 are required for Golgi localization in HeLa cells, concluding that residues 368-528 are sufficient for localization. This region includes a GOLD (GOLgi Dynamics) domain previously reported to interact with Golgin tethering proteins. Alanine scanning identifies the motif MWT just upstream of the GOLD motif as necessary for Golgi localization. Acute CRISPR knockout identifies two Golgins, Golgin45 and Giantin, as necessary for ACBD3 Golgi localization, and IP indicates that the MWT motif breaks this interaction. These data are a bit scattered around the paper but taken together are reasonably persuasive, particularly when viewed in context with published work. This reader would have found the manuscript easier to follow had the Golgin and MWT motif data been presented en bloc.

In a second set of experiments, IP-mass spec is used to identify ACBD3 interactors that might assist in the protein's localization. The MS data presented are filtered to exclude proteins not already identified as Golgi-localized. This is, I think, a mistake. Even if the authors choose to focus on known Golgi interactors as candidates for a localization function, the biological functions of ACBD3 are far from fully understood, and the full dataset would be of value to both cell biologists and virologists. Hits in the filtered dataset include the R-SNARE Sec22B, and the SNARE chaperone Sly1/SCFD1. Acute CRISPR inactivation of Sec22 decreases ACBD3 localization to the Golgi and SCFD1 inactivation more or less abolishes localization. Co-IP experiments are used to argue that ACBD3 interacts with the N-terminal regulatory Longin domain of SEC22B, as well as with SCFD1. The Sec22 data are more detailed and persuasive. No experiments with purified proteins are presented to establish that the detected interactions are direct rather than mediated through a bridging factor or factors. Importantly, SCFD1 is likely to have multiple different client SNARE complexes that operate at different stages of ER and Golgi traffic. Hence its inactivation is likely to be pleiotropic and consequently phenotypes arising must be interpreted with caution.

Lastly, the authors perform IP experiments which show that ACBD3-Golgin co-IP efficiency is lower in cells with acute inactivation of SCFD1. This epistatic relationship is used to argue for a sequential model of recruitment with SCFD1 and perhaps client SNARE proteins operating upstream of ACBD3-Golgin interaction. This argument is not persuasive because we do not know whether SCFD1 and its downstream activities increase the rate of ACBD3-Golgin complex asssembly, or alternatively stabilizes ACBD3-Golgin complexes, decreasing the rate of their dissociation.

In general the methods are fairly clear but that there is room for improvement. The "high throughput" imaging pipeline is not clearly described. Each figure legend should specify the microscopy methods used, and for each result the number of biological replicates and cells analyzed should be specified. The statistical methods (Student, Tukey, etc.) used for each experiment should be specified. Saying that statistics were calculated using Python 3.7 is useless without additional details. e.g. at least the libraries and codebase used should be indicated or deposited. Many figure labels (e.g. Fig. 2) use absurdly small fonts. The mass spec hits obtained should be provided both with and without exclusion of non-Golgi-localized proteins.

Significance

In general I think this is a useful and well controlled set of experiments producing useful insights. However, the interpretations need to be more carefully considered, and alternative interpretations must laid out as clearly as possible. Specifying the limitations of the study will make it more, not less, useful to the field. If the authors want to make the case more robustly that the interactions described are mediated through direct binding, or that the operation of SCFD1 and Golgins operate sequentially to recruit ACBD3, additional wet bench work will be required which will of course take time to complete.

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Referee #2

Evidence, reproducibility and clarity

Summary

This is a very interesting and potentially important paper for the field of membrane biology and membrane trafficking, in which the authors have studied the molecular mechanisms by which ACBD3 (and consequently PI4KIIIb) is recruited to the cis-Golgi membranes. The authors suggest that this recruitment is based on a two-step process, mediated by interactions to, on the one hand, SCFD-1 (SLY1) and, on the other hand, two redundant golgins (golgin-45 and giantin).

Comments:

• Pg.1 : arfaptins, as far as I know, have not been shown to be involved in intra-golgi trafficking but rather in Golgi export (see e.g. ref. 12)
• Pg. 1: reigon --> region
• Arf1 also recruits PI4KIIIb right?
• Fig. S1: the information about the number of cells per experiment is missing. Also, please add the information about what exactly is represented in the box plots (is it the distribution of the mean value of R per experiment? or the total distribution on a cell-by-cell basis of a representative experiment?)
• The definition of Avg. Golgi int/avg. cell int. (a.u.) in Fig 1E,F is a bit difficult to understand to me. If I understand correctly, the total fl. int in the Golgi mask was computed and divided by the area of the Golgi mask (this is the av. Golgi intensity). A similar computation is done for the entire cell (including the Golgi), i.e., total fl. intensity in the cell mask is computed and divided by the area of the cell mask. Then the two av. intensities are divided (ratio = av. Golgi int / av. cell int.). This ratio, for a protein that is enriched in the Golgi area, should be larger than 1. For a protein that is equally distributed all over the cell, it should be 1, and for a protein that is excluded from the Golgi area, smaller than 1. Then to this value, the authors subtract the value of the ratio found for an inert construct (GFP of Halo alone), which I imagine should have an original ratio value of the order of 1, and hence, after this subtraction, norm. ratio values larger than 0 mean that they are more enriched at the Golgi area than GFP/HaloTag themselves. Is this correct? In principle, I don't see anything entirely wrong with this way of thought, but I just found it a bit difficult to understand, and in general one has to be careful when computing rations (quotients) and then subtract another ratio. Also, the units are not a.u., the value is dimensionless, what is "arbitrary" is the definition of 0 value and the based on this definition, also the actual value. I think it would probably be much clearer for the readers to compute somthing like the relative enrichment in the Golgi area as compared to the rest of the cell (excluding the Golgi area). That is, a value r'=(Int. Golgi mask / Area Golgi mask) / [(Int. Cell mask - Int. Golgi mask)/(Area cell mask - Area Golgi mask)]. This can be computed directly or defining a mask that is the cell mask - the Golgi mask. Also, some maths (unless I made a mistake) give that this r'= r (1-aG)/(1-r aG); where r is the ratio (before subtraction) defined by the authors, and aG=Area cell mask/Area Golgi mask. In any case, I'd suggest the authors to either adopt this other quantitation (without subtraction of the GFP/HAloTAG), which gives directly the fold-enrichment in the intensity density in the Golgi area with respect to the rest of the cell; or explain in more detail the maths of the value they are plotting now.
• Fig. 1C&F: Besides the MWT mutant, the FKE mutant also seems to have a somewhat compromised Golgi localization. Have the authors followed on that, or what is the reason that they have just focused on the MWT mutant?
• Very minor point, and without wanting to sound pedant at all, but I think (I might be wrong of course, so apologies if I am) that the plural of apparatus in latin is not apparati, but apparatus (fourth declination). So, I'd change the word in page 2 (or just rephrase the sentence: e.g. "resulting in Golgi fragmentation"). But of course, I'd leave this to the authors' discretion.
• Fig. 3A: have the authors tried or been able to perform IF of the endogenous SCFD1 protein?
• Similarly to what has been done for other panels, could you quantify Fig. 3C? Are PI4KIIIb protein levels affected upon the different KOs?
• The last paragraph of the "SCFD1 and ACBD3 interact upstream of PI4KIIIβ recruitment<br /> to the Golgi apparatus" section reads a bit odd placed there. I think it is more appropriate for the discussion or for the intro part on SCFD1.
• I am confused on Fig. 5A/B. The labels in the blots show that 390-528 (without UR) does not bind sec22 or scfd1, but the 368-529 does? Or I guess, judging by the MW seen in the middle blots, that there's some error in the labelling? also, the IP efficiency of the MWT mutant in the panel A blot is quite low, still sec22 seems to be very efficiently pulled down. Can the authors comment on that please? Would co-IPing against endogenous sec22 and scfd1 would work (so you don't need to rely on HaloTag+ligand?)
• I really like the experiment 6B. Have the authors tested whether SEC22 is also recruited to mitochondria in those conditions? But not SCFD1?
• The results shown in Fig 7 might show a partial depletion in the interactions, but to be fully trusted they would need to be quantified and a statistical test used to compare the values. I think this part is important to show very clearly, because even with low binding to golgins (remember, single knockouts do not prevent Golgi localization of ACBD3), one could expect that ACBD3 still localized to the Golgi but it does not in the absence of SCFD1 as shown in this paper.
• A prediction of the proposed model is that in cells depleted of the two Golgins, SCFD1 and ACBD3 should still bind to one another, right? Did the authors test this?
• The model presented here (fig 8) seems to suggest that only the conformational variation of ACBD3 that binds Golgins is able to recruit (bind) PI4KIIIb. Is this known, or is there any experimental evidence for that?
• Have the authors thought about testing the FKE mutant in the experiemnts shown in Fig. 5?
• In general, I think the title might be a bit misleading because of the use of PI4Kiiib. I understand what the authors mean, but because they have not thoroughly tested PI4Kiiib recruitment in their experiments, I think they should focuse rather on the mechanism of recruitment of ACBD3 the authors have found.

Significance

I think, as said above, that this is potentially an important paper for the field of membrane trafficking and membrane biology. Most of the experiments are in general well performed and well controlled, and the paper is clearly written and follows a logical line.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript describes molecular mechanisms by which ACBD3 is recruited to the Golgi complex. ACBD3 recruits PI4KIII which is required to generate PI4P, a phosphoinositide which is key for the recruitment of essential Golgi proteins and hence is key to Golgi identity. The authors have used a combination of mass spectrometry, high quality fluorescence imaging, transient CRISPR knockdowns, and biochemical approaches such as IPs to identify the key determinant for recruitment of ACBD3 to the Golgi complex. They map the interaction between ACBD3 and the Golgi as a unique region (UR) upstream of its GOLD domain, identifying, in particular, an MWT motif as key for this recruitment. Using mass spectrometry they identify several novel interactors of ACBD3 as well as some established binding partners. Knockdown of these interactors reveal a key role for the SNARE, SCFD1, where reduced levels lead to complete loss of ACBD3 localisation to the Golgi without apparent disruption of Golgi structure. They further validate this interaction and that of another SNARE (Sec22b), which is part of the same SNARE complex as SCFD1, mapping the interaction to the longin domain of Sec22b. Surprisingly however they demonstrate that the UR domain does not mediate the interaction between ACBD3 and these SNAREs suggesting an alternative mechanism of recruitment. Previously identified ACBD3 interactors, Golgi proteins giantin and golgin-45 were also identified in the mass spectrometry screen and the authors demonstrate that these two proteins can recruit ACBD2 to the Golgi and this is dependent on the MWT motif identified in the UR domain. By knocking down SCFD1, they show reduced recruitment of ACBD3 leading them to propose a model of sequential recruitment of ACBD3 by SCFD1 followed by interactions with the golgins.

Major points:

This study is a well-executed and rigorous study of the molecular requirements for the recruitment of ACBD3 to the Golgi. The experimental approaches are state-of-the-art and the data are clean and convincing. The only caveat, raised by the authors themselves, is their interpretation that there are two sequential steps for Golgi recruitment of ACBD3. While they show that loss of SCFD1 reduces the interaction of ACBD3 with giantin and golgin 45, their model depends on doing the reverse experiment, i.e. assessing the effects of knocking down either giantin or golgin-45. This is especially relevant given the demonstration that golgin-45 is sufficient to recruit ACBD3 to mitochondria. It may well be that recruitment involves a tripartite complex, which is not uncommon in vesicular transport mechanisms Giantin is not an essential protein do it should be feasible to perform this experiment. The authors are equipped in the quantitative fluorescence microscopy which would be required and which would help resolve whether sequential or redundant mechanisms are required for ACBD3 recruitment.

Significance

PI4P is a phosphoinositide that is important for the recruitment of Golgi proteins. As with most PIs it is likely to act by coincidence detection in that Golgi associated proteins will recognise PI4P as well as other factors on Golgi membranes. This results in different local membrane environments which will be specific for particular functions. PI4KIII is key for PI4P production although the absolute levels of PI4P are likely to be determined by a balance of lipid kinases and phosphatases. However, since ACBD3 is key for the recruitment of PI4KIII it is important to understand the molecular mechanisms by which it is recruited. The manuscript thus makes a significant contribution to understanding one of the underlying mechanisms for PI4KIII recruitment although, as indicated above, stops short of establishing a clear model for the roles SCDF1 and Sec22b versus golgin 45 and giantin. For the future it will be of interest to determine why either a sequential or a redundant mechanism is required for the recruitment of ACBD3 as a scaffold protein.

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Reply to the reviewers

We would like to thank all reviewers for taking the time to evaluate our manuscript fairly and critically. Many helpful suggestions and discussion points were raised. One important group of comments raised concerns whether our proposed timer and counter models were the appropriate conceptual framework to discuss nuclear multiplication in schizogony, whether they were mutually exclusive, and whether other alternatives should be considered. These comments were instrumental for us to uncover some inconsistencies in our previous modeling approach. In the new manuscript, we now define the counter and timer models much more rigorously in the context of Plasmodium cell division. Based on these refined models we now provide a new statistical analysis that goes beyond the previous analysis, significantly improving the statistical support for our conclusions. Details are given in the following individual replies.

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

Malaria parasites replicating in human red blood cells show a striking diversity in the number of progeny per replication cycle. Variation in progeny number can be seen between different species of malaria parasites, between parasite isolates, even between different cells from the same isolate. To date, we have little understanding of what factors influence progeny number, or how mechanistically it is controlled. In this study, the authors try to define how the mechanism that determines progeny number works. They propose two mechanisms, a 'counter' where progeny number is determined by the measurement of some kind of parasite parameter, and a 'timer' where parasite lifecycle length would be proportional to progeny number. Using a combination of long-term live-cell microscopy and mathematical modelling, the authors find consistent support for a 'counter' mechanism. Support for this mechanism was found using both Plasmodium falciparum, the most prominent human malaria parasite, and P. knowlesi, a zoonotic malaria parasite. Of the parameters measured in this study, the only thing that seemed to predict progeny number was parasite size around the onset of mitosis. The authors also found that during their replication inside red blood cells, malaria parasites drastically increase their nuclear to cytoplasmic ratio, a cellular parameter remains consistent in the vast majority of cell-types studied to date.

Major Comments

It is stated a few times in this study that P. knowlesi has an ~24 hour lifecycle, and while this is the case for in vivo P. knowlesi, it was established in the study when P. knowlesi A1-H1 was adapted to human RBCs (Moon et al., 2013) that this significantly extended the lifecycle to ~27 hours, which should be made clear in the text. As much of this study revolves around lifecycle length and timing, the authors should consider some of their findings with the context that in vitro adaption can significantly alter lifecycle length.

The reviewer raises an important point that we didn’t discuss for P. knowlesi. We now mention this directly in the introduction chapter (line 67) and in the discussion (lines 470ff). We are aware that P. knowlesi takes about 27 hours in the lab, which was also communicated by the Moon lab. We now cite relevant studies again in this context. We further address the issue of modified cell cycle time in vitro in the discussion in the sense that absolute values must be taken with caution and the focus of this study is about the relative ratio and correlation between the different cell cycle metrics.

• The dichotomous distinction between 'timer' and 'counter' as mutually exclusive mechanisms seems to be a drastic oversimplification. Considering the drastic variation we see in merozoite number across species, between isolates, and between cells, it seems much more likely that there are factors controlled by both time-sensed and counter-sensed mechanisms that both influence progeny number.

The study of progeny regulation in malaria parasites is very much in the early stages. We can agree that our models are simplifications, as is the case with all models. Our choice of just the two models timer and counter was driven by the number of cellular parameters we measure, i.e., duration of division phase and progeny number. These data essentially allow us to test the two competing models we presented. As we quantify more and more cellular parameters, based on the quantitative live cell imaging protocols established here, we will be able to test more complex cell cycle models. With our current data, we believe more complex models are not warranted.

However, this valuable criticism, in conjunction with related remarks by other reviewers, made us reevaluate the constraints of our model more precisely. We noticed that the criteria used in the previous version in the manuscript contained unnecessary additional assumptions. Briefly, the previous counter model also required that final merozoite number was tightly controlled, while the previous timer model required the growth rate to be tightly controlled. These side assumptions were not made explicit in the manuscript and could bias the support towards one or the other model.

We now improved the modeling approach substantially by removing implicit side assumptions, and clearly defining timer and counter models in terms of their correlations. The refined formulation of the timer posits that between individual parasites the target duration and the nuclear multiplication rate vary in a statistically independent way; while in a counter, target number and nuclear multiplication rate are statistically independent. We now explain this extended analysis in more detail in the introduction (lines 86ff). We also now more clearly state the dichotomous nature of the model (line 488). A new results paragraph (lines 213ff) and an entirely new Fig. 2 (and Fig. S4) contains the model predictions and statistical comparison between the models.

This more rigorous treatment showed that including the variance of the multiplication rate was critical to allow a clean discrimination between the models. Also, with the sole exception of P.knowlesi H2B, where no model was clearly favored (Fig. 2G-H,K), the timer model was found to be inconsistent with the data, while the counter was clearly favored. Our new goodness-of-fit analysis also showed that although the counter is strongly simplified, it produced adequate fits, demonstrating that potential model refinements would need to be justified by new, more extensive data.

It is also important to consider that the degree of variation in merozoite number could rather be an expression of varying growth conditions and does not directly predict which of the proposed models are true. For instance, a counter where the target merozoite number varies strongly depending on growth conditions, would be consistent with all available data. It is an interesting question for future work whether a counter would indeed describe growth across different isolates.

The biological reality of growth regulation is certainly complex, and the counter model will likely need to be refined in the future, which we acknowledge in a corresponding statement in the discussion (lines 491ff). Nevertheless, we find it encouraging that a simple model can explain the vast majority of our data very well.

Additionally, the only parasite parameter measured in this study, size at time of first nuclear division, explained only a small proportion of the variance observed in merozoite number.

It is indeed the case that amongst the measured parasite parameters i.e. schizont stage duration, nuclear volume, and cell size we only found the latter to correlate with the final progeny number. We did not aim to imply that all variation in progeny number is explained by cell size. It is likely that a putative counter relies on a set of factors, which are somehow linked to cell size. In addition, intrinsic stochasticity in nuclear growth is likely to contribute to final merozoite number variability, which is included in our models via a variable growth rate. Defining the actual limiting factor or combination of factors will be an exciting challenge for the future studies building on this one.

• For modelling of a timer-based mechanism, the designation of t0 is subjective. The authors chose the time of first nuclear division as their t0. It is possible that a timer-based mechanism could not be supported based on this model the chosen t0 differs from when the "parasite's timer" starts. For example, t could also have been designated as the time from merozoite invasion (t0) to egress (tend). It would be unreasonable to suggest the authors repeat experiments with a longer time-frame to address this, but this possibility should be discussed as a limitation of the model. It may also be possible to develop a different model where t0 = merozoite invasion and tend = egress, and test this model against the data already collected in this study.

This is a valid point. We indeed, considered the time point of invasion as the other relevant time point in the IDC for a possible timer. Due to necessary compromises in imaging protocols between acquisition length, temporal, and spatial resolution we have not been able yet to combine full-length IDC measurements with quantification of progeny number. Given the choice, however, between time point of invasion and the onset of nuclear division as starting point for a potential timer we would still favor the latter: An argument can be made that a timer that regulates offspring number would be more accurate when activated at the moment of the relevant cellular events rather than “running” for a very prolonged growth phase before any “decision” concerning parasite replication. We are still convinced that the entry into the schizont stage, which we analyze here, marks an important cell cycle transition point that has been highlighted in many different studies. As suggested, we now discuss the limitations of our selection of t0 in the text (lines 146ff).

• The calculation of the multiplication rate is confusingly defined. In Figure 1 it is stated that it is "...based on t and n", which would imply that the multiplication rate is the number of merozoites formed per hour of schizogony, which would give an average value of ~2 for P. falciparum and ~1.5 for P. knowlesi. The averages rate values shown, however, are in the range of 0.15-3. The authors should clarify how these values were determined.

Thank you for pointing out the need for more clarity. Since the nuclear multiplication, similar to e.g. cell population growth, follows an exponential law, the multiplication rate used (lambda) is in fact a logarithmic growth rate. Therefore, it occurs in the exponent (not as a coefficient) in the exponential growth function ( ), which explains the range. We now mention this more explicitly in the results (lines 163ff).

• In Figure 2, the time from tend until egress is calculated, and this is interpreted as the time required for segmentation. In the Rudlaff et al., 2020 study cited in this paper, it is shown that segmentation starts before the final round of nuclear divisions are complete. Considering this, the time from tend until egress is not an appropriate proxy for segmentation time. The authors should consider rewording to something akin to "time from final nuclear division until egress" to more accurately reflect these data.

Thank you for indicating our imprecise use of the nomenclature. Indeed, some essential segmentation-associated structures such as rhoptries and subpellicular microtubules are clearly forming before the last division. We were referring to “segmentation” as the time window where actual ingression of the plasma membrane occurs between nuclei with the concurrent formation of more prominent IMC-associated sub-pellicular microtubules between nuclei (as in Fig. 1A last panel). We can, however, agree that consistently using the term “merozoite formation” is more adequate here. We have now corrected the terminology according to the suggestions of the reviewer (lines 271ff).

• There is a significant discrepancy between the data in Figure 5 and Supplementary Figure 8. In Supplementary Figure 8, the authors establish that culturing parasites in media diluted 0.5x has a marginal effect on parasite growth, with no discernible change in parasitaemia over 96 hours. By contrast, in Figure 5a the parasitaemia of parasites cultured in 0.5x diluted media is approximately 5-fold lower than those in 1x media. The authors should explain the significant discrepancy between these results.

The reviewer correctly points out a difference in parasitaemia between two parasite culture experiments, shown in Figs 5a (now 6A) and S8 (now S11), respectively. There were several differences in the experimental setup used in the two experiments that could explain this discrepancy. In Fig. 5a the parasites were synchronized to early ring stages while in Fig. S8 we used asynchronous cultures (maybe with a slight majority of late stages). One could speculate that by the time the synchronized ring stage culture reached egress the effect of nutrient depletion, which started at t = 0 h is more pronounced. This effect could have been exacerbated by the more frequent media change of 24 h in Fig. 5a vs 48h in Fig. S8. Lastly, the starting parasitemia was differently set being higher at around 0.5% in the Fig. 5a while only 0.2% in Fig. S8. Possibly a lack of nutrient is “felt less” by the culture at lower parasitemias. Generally, in Fig. S8 we were more focused on highlighting the difference between 1x/0.5x and the more diluted conditions on the long-term culture and to show that continuous culture is actually possible in 0.5x medium. We have now expanded the legends to highlight those differences more clearly.

• In Supplementary Figure 4, the mask on the cell at t0 shows two distinct objects, but it seems very unlikely that they are two distinct nuclei as they vary approximately 5-fold in diameter. The authors should provide more detail on how their masking was performed for their volumetric analysis. Specifically, whether size thresholds were also applied during object detection.

Thank you for requesting clarification here. Fig S4 (now S7) shows only one z-slice (not a projection) of the entire image stack, to illustrate how the thresholding approach was performed on every single image slice. The two objects in the shown cell are indeed two nuclei, but because they are not in the same z-plane appear to be of different size. In particular, only a slice of the upper part of the nucleus on the lower right is visible in the shown slice. Throughout the study, volume determination was realized by adding up the individual slices, as is explained in detail in the Materials and Methods sections. We have now added a more explanation in the figure legend to clarify the procedure.

Minor Comments

• Line 45-48 mentions that merozoite number influences growth rate and virulence, but the corresponding reference (Mancio-Silva et al., 2013) only discusses the relationship between merozoite number and growth rate, not virulence.

We thank the reviewer for requesting this distinction. Merozoite number and virulence have not been correlated in vivo so far. Certainly, because one can’t retrieve late-stage P. falciparum parasites from patients, but maybe partly because merozoite number has not gotten significant attention as a metric in the previous decades. Even if merozoite number is intuitively connected to growth rate which might causes higher parasitemia which is in turn linked to more severe disease outcome it is important to emphasize that those are certainly not equivalent. We have therefore removed the statement about virulence (line 48).

• Line 59 states that a 48 hour lifecycle is a baseline from which in vitro cultured parasites deviate. Clinical isolates also show variation in lifecycle length and so it is more accurate to just say that 48 hours is an average, rather than a baseline.

The word “baseline” has been changed to “average” (line 61).

• Line 63 cites a study for the lifecycle length of P. knowlesi (Lee et al., 2022), but there seems to be no mention of lifecycle length in this reference

This reference was meant to serve as an introductory review article to research in P. knowlesi. Actually, to the knowledge of the authors, there is no study presenting quantitative data showing that the in vitro cycle of P. knowlesi is actually around 27 h. Our lab experience is however coherent with a 27 h cycle, which was confirmed by personal communication by the Moon lab. We now also cite in the next sentence the inaugural P. knowlesi adaptation publication (Moon et al. 2013) showing some time course data indicating the duration of the IDC to be around ~27h (lines 67ff).

• If I am interpreting Figure 3B correctly, this is essentially a paired analysis where the same erythrocytes are measured twice, once at t0 and once at tend. If this is the case, this data may be better represented with lines that connect the t0 and tend values.

Yes, these are the same erythrocytes measured twice. We have modified Figure 3 (now Fig. 4) accordingly.

• Figure 3A seems to imply that to calculate diameter of the erythrocytes, three measurements were made and averaged for each cell. I think this is a nice way to get a more accurate erythrocyte diameter, but if this is the case, it should be specified in the figure legend or methods.

This is already described in the figure legend (line 305).

• In Figure 4I it is shown that in P. falciparum merozoite number doesn't correlate with nucleus size, but for P. knowlesi in Supplementary Figure 7c, a significant anticorrelation is observed. The authors should state this in the text and discuss this discrepancy.

Contrary to all other graphs, visual inspection of the distribution of data points in Fig. S10C shows that it contains two outlier data points at the bottom right. Those two specific points are also responsible for the significant anticorrelation. We did not filter or remove any quantification results but also didn’t have sufficient confidence in this data distribution (which is further based on the segmentation of the Histone2B not on an NLS mCherry signal) to make substantial claims about anticorrelation. Because we considered it informative we still decided to show it in the supplements. We now briefly mention the issues with the data set and its interpretation in the text (lines 350ff).

• The authors show that merozoite number roughly correlates with cell size at t0 but it would be interesting to see whether cell size at tend also corresponds with cell size at t0. This might help answer whether the cell is larger because it has more merozoites, or whether it has more merozoites because it is larger.

Plotting parasite cell volume at t0 against cell volume at tend (as well as between t-2 and tend) indeed shows a positive correlation (see below). While it is an interesting thought we concluded after some discussion that no convincing causal relationship between cell size and merozoite number can be inferred based on this analysis. Since we consider the possible statement that cells that are bigger in the beginning are also bigger in the end unavailing, we decided not to include the data.

• I don't feel that "nearly identical" is an appropriate summary of erythrocyte indices in Supplementary Figure 9, considering there is a statistically significant increase in mean cell volume. I think it is unlikely that this change is consequential, and performing these haematology analyses is a nice quality control step, but this change should be stated in the text.

In the modified text we now express the significant change in MCV in terms of percentage, which is around 1.2% (line 381).

• In Supplementary Figure 8, parasitaemia only increases ~2-fold compared to >5-fold the previous two cycles. It seems likely that at the final timepoint on this graph the parasites are starting to crash, and therefore it may be best to end the graph with the 96 hour timepoint.

The reviewer suggests that cultures at those parasitemias might not be in perfect health. Our Giemsa stains did not show signs of an unhealthy culture and kept growing. It was, however, important for us to show that cultures can be maintained in culture over a prolonged period of time in 0.5x medium, even when resulting in reduced growth, while this was not possible with lower dilutions. Therefore, we would like to keep the data point. We have added a cautionary comment in the legend.

• The error bars in Figure 5C aren't easily visible, moving them in front of the datapoints may help their visibility.

Error bars were moved in front of the data points.

• In Figure 6D & E, the y-axis labels should be changed to whole integers as all the values in the graph are whole numbers.

We have changed the y-axis labels accordingly.

• My interpretation of Figure 6 C-E, is that these are the same cells measured at three time points (t-2, t0 and tend). If this is the case, 6C is missing the cell that has a merozoite number of 8, which is presumably why the y-axes are not equalised for the three graphs.

It is correct that the same cells are displayed in all three plots, with the exceptions of three cells in 6C (for the timepoint t-2), which are missing for the following reasons: 1) it was not possible to determine the volume at this respective timepoint due to technical issues or 2) the cell was already just before t0 at the start of the movie so that t-2 had already passed. We now note this in the figure legend and have also equalized the y-axes (now Fig. 7C-E).

Reviewer #1 (Significance):

In the asexual blood-stage of their lifecycle, malaria parasites replicate through a process called schizogony. During schizogony an initially mononucleated parasite undergoes multiple asynchronous rounds of mitosis followed by nuclear division without cytokinesis, producing a variable number of daughter nuclei. Parasites then undergo a specialised cytokinesis, termed segmentation to where nuclei are packaged into merozoites that go on to invade new host cells. While nucleus, and therefore merozoite, number are known to be varied between cells, across isolates, and across species, little is known about the mechanisms regulating merozoite number. In this study, the authors use live-cell microscopy to understand how parasites determine their progeny number. They suggest that parasites regulate their progeny number using a 'counter' mechanism, which would respond to the size or concentration of a cellular parameter, as opposed to a 'timer' mechanism. Long-term live-cell microscopy experiments using malaria parasites are extremely technically challenging, and the authors should be commended for their efforts in this regard. While I agree that the data generated from these experiments are technically sound, I have some reservations expressed above about the interpretation of some of these results. I would strongly encourage the authors to consider rewording some of their interpretations taking into account some of the caveats listed above. I would also consider fitting/testing an additional mathematical model where the time-frame proposed for the 'timer' mechanism begins following merozoite invasion.

We thank the reviewer for the appreciation of our work and hope we have sufficiently reworked the manuscript based on the comments listed above. Furthermore, we think the improved model statement and analysis improves the clarity of our conclusions. Indeed, we would like to test additional models including the full IDC once, as mentioned above, we are technically able to generate these data.

This work is of specific interest to anybody who grows malaria parasites, as the dynamics of their growth is obviously important to understand. Further, this work is of interest more generally to cell biologists who study the regulation of progeny number or cell size. I have no experience with the application of mathematical modelling to understand biological systems, and so I cannot comment on the interest of this work to that field.

Reviewer #2 (Evidence, reproducibility and clarity):

This is a solid study that further characterises the dynamics of nuclear division in Plasmodium falciparum and P. knowlesi. Of two, among potentially several, models for how the number of daughter nuclei, and thus parasites - (called merozoites in this genus), are one that posits nuclei divide until a fixed timer ends, and one that posits that nuclei divide to reach a fixed number that is defined by a cellular counter. I find some practical difficulties in definitive measurement of either model, one issue with the former is that experimental definition of the start of the timer is problematic - we may define the starter's gun (eg by the first nuclear division) but it isn't necessary that the cell is using that same start time.

We are pleased that the Reviewer found our study ‘solid’. Concerning the timer model, we agree that the selection of the starting point is a critical aspect of this study, as also Reviewer 1 pointed out. We selected this particular “t0” because the entry into the mitotic phase marks an important cell cycle transition. Several studies have suggested a “schizogony entry checkpoint” might be active just before (Matthews et al, 2018; Voß et al, 2023; van Biljon et al, 2018; McLean & Jacobs-Lorena, 2020). Once cells are committed to the schizont stage they are less responsive to stimuli. Alternatively, the timepoint of erythrocyte invasion could be a legitimate starting point. Due to necessary compromises in our imaging protocol between acquisition length, temporal, and spatial resolution we have not been able yet to combine full-length IDC measurements with quantification of progeny number, and therefore we leave exploration of an earlier timer start for future work. Within the confines of the model comparison in the current study, we think the selected t0 is already highly informative. We now explain the selection and limitations more explicitly in the text (line 144ff).

Additionally, as the authors confirm here, being sure when that first nuclear division has occurred is particularly tricky with Plasmodium parasites, in part because the first few nuclei seem to clump together, preventing one from unambiguously calibrating the first division.

The Reviewer is concerned about difficulties with precise reporting of the time point of first nuclear division. We suspect there was a misunderstanding here. In the text (line 137) we had written the following:

“Although separating individual nuclei after the first two rounds of division was challenging due to their spatial proximity, the improvements in resolution and 3D image analysis allowed us to count the final number of nuclei routinely and reliably at the transition into the segmenter stage.”

To clarify, when analyzing 3D image stacks produced by the LSM900 Airyscan the first nuclear division can consistently and unambiguously be detected. In anaphase the nuclei are pushed apart quite substantially before getting a bit closer together afterwards (see e.g. Fig. 1B and C). Hence the precision of the detection is only limited by the 30 min interval of the time lapse. Later, at the four nuclei stage, crowding makes distinction more difficult. In the final segmenter stage, the reorganization and condensation of nuclei makes reliable counting possible again. We have now reformulated the quoted sentence for more clarity (lines 137ff).

Furthermore, getting decent replicate numbers is hard because of the difficulties of time lapse microscopy, and most Plasmodium studies (including this one) suffer from low enough numbers that it isn't always clear whether the numbers support one model over another.

The reviewer points out the difficulty of obtaining enough replicates in Plasmodium time-lapse studies. We agree that depending on technology, sufficient replicates can be challenging. In the present study we obtained Ns between 25 and 35 for all conditions in P. falciparum and P. knowlesi from three independent replicas. To gain confidence in the conclusions from a limited, but not austere, data, it is essential to 1) reduce model complexity to a minimum and 2) perform stringent statistical analysis including accounting for small-sample variation. Motivated by this concern of the Reviewer and a similar point raised by Reviewer 1, we have revisited our modeling approach in the revised manuscript. This led us to a corrected, more rigorous definition of what precisely we mean by ‘counter’ and ‘timer’ models: The timer posits that between individual parasites the target duration and the nuclear multiplication rate and vary in a statistically independent way, while in a counter target number and nuclear multiplication rate are statistically independent. With no further adjustable parameters, the two models are thus both mutually exclusive and minimal. Although biological reality is likely to be more complex, we feel that these minimal models are adequate for the amount and resolution of our current, state-of-the art data. The general result remained the same: The counter model is strongly preferred in almost all our experiments data (new Fig. 2), with the sole exception of P. knowlesi H2B, where indeed more data may be needed to come to a clear conclusion. Furthermore, we have taken care to scrutinize these conclusions accounting for goodness-of-fit for the respective sample size N. This analysis showed, surprisingly, that the counter model was sufficient to account for the data: the real dataset was as similar to the counter prediction as synthetic, counter-generated data. We hope that this improved statistical analysis can help the reader judge the robustness of our conclusions.

Nonetheless, several recent studies, particularly a study from the same institute (Klaus et al., 2022) employing timelapse imaging of nuclei, and timing the nuclear division of parasites, finds poor correlation between the duration of "schizogeny" (although perhaps using a different definition to the one used by the parasite) and the final number or merozoites. They therefore argue that there is poor evidence for a timer, and conclude by elimination that a counter must exist instead. A review by some of the authors of that study and some of this current study (Voß et al 2023), also concludes that the data from Klaus and colleagues "strongly support" a counter model. This current study also concludes that a counter model controls final nuclear/merozoite number in P. falciparum and P. knowlesi. This much at least is not particularly novel given the recent work on this topic, although the addition of the P. knowlesi data is interesting and consistent with the prior P. falciparum work.

Our present work, indeed, does confirm the previous report of a counter over a timer, through a more targeted approach. While Klaus et al. used timing data of first nuclear cycle vs. the full duration, we now provide, thanks to an improvement microscopy setup and protocol, simultaneous measurements of timing and final progeny number, i.e. counting of merozoites/nuclei. While the preference for a counter model is not fundamentally novel, the additional information that the counter model holds in different strains, conditions and species is, in our opinion, not trivial and points to some degree of evolutionary conservation. We also demonstrate here that the counter model is not only preferred over the timer, it also fits the data adequately, so that it can be considered ‘correct’ at this level of complexity. Another, possibly more important, value of this study lies in the quantitative and time-resolved assessment of multiple important parasite metrics such a cell volume and nuclear volume together with merozoite number at the single cell level. Although descriptive, this has not been achieved in Plasmodium until now.

As above, the authors concede that it is difficult to determine with strong confidence when the first nuclear division has occurred, so it may well be that there is substantial noisiness in the time that they define schizogeny to commence. If that were the case, this would contribute to the poor correlation observed between schizogeny duration and number of merozoites produced, so this could be an important confounding experimental factor. This deserves some more discussion by the authors.

Concerning the confidence with which we identify the first nuclear division we could hopefully clarify in the section above that our precision is only limited by the time resolution of the acquired time-lapse. Therefore, the uncertainty about the start time is not particularly high, and moreover, can expected to affect timer and counter (via the growth rate) to a similar degree. We see no unfair advantage for the counter for this reason.

Alternative methods to count absolute DNA content (rather than trying to count individual nuclei) might be useful ways of independently confirming this phenomenon. Alternative possibilities for what constitutes the "start" of a possible timer are also warranted - it could be for example, the first division of one of the other organelles.

This is an interesting suggestion. Next generation fluorogenic DNA dyes have been used by us and the Ganter group (Simon et al. 2021, Klaus et al. 2022, Wenz et l. 2023) to assess DNA content of single cells over time. Our experience shows that there are some caveats to using these Hoechst based dyes, some of which we discussed in the aforementioned publications. While they allow some reasonable absolute quantification of DNA content for the very first S-Phase (and subsequent nuclear division), in later stages only relative quantification can be achieved. One underlying reason is the apparent increase of dye permeability, and therefore higher intensity, at late schizont stages. This issue is exacerbated by the asynchronous DNA replication of multiple nuclei. Further, nuclear division itself can be delayed or even inhibited when increasing the concentration of the dye, which suggest an impact on cell physiology (well documented for Hoechst based dyes in other organisms). When reaching the segmenter stage, the resulting variance in fluorescent intensity would make it challenging to assign a reliable number of nuclei required for analysis, a problem that does not occur when counting individual nuclei. Taken together, unfortunately, all these confounding factors make DNA content analysis in live single cells for the entire schizont stage unachievable at this point.

These and previous authors in any case conclude that a counter model must exist through exclusion of a timer model. I am less convinced that the evidence discounting the timer is conclusive, and that a straight counter model is the only alternative. Indeed I am unconvinced by the suitability of this strictly dichotomous two-model system to categorise the division of unicellular eukaryotes, and these theories are not universally held to be sufficient to describe division.

We thank the Reviewer for this insightful comment. As already detailed above, we have clarified and corrected our model definitions in the revised manuscript. Further, we want to make the important distinction between organisms, including unicellular ones that undergo binary fission and the ones like Plasmodium that use schizogony. Our model, although inspired by model organisms, is tailored to a multinucleated division mechanism, and clearly defined within those boundaries. The timer and counter models we consider are defined by their correlation structures. They are at two extremes of a continuum of models which could be characterized, for instance, by the ratio of correlations (growth rate - nuclear number) vs. (growth rate – duration) as an additional parameter. As the reviewer points out, excluding the timer model is not equivalent to proving the counter model, and indeed a partially correlated model, or a more complex model entirely, could yield a better fit. However, within the realm of models without additional parameters, and which are testable with the available data, only timer and counter remain, as different timer start points are not experimentally accessible. Importantly and somewhat surprisingly, the counter model also gave a fit that is as good as can be reasonably expected for the experimental sample size (new Fig. 2). So, we maintain that within the current experimental constraints, the counter model is the only viable option for almost all our tested conditions. The observation that in H2B-GFP expressing P. knowlesi parasites no clear distinction can be made between the models, indeed, suggest that the reality of multiplication rate regulation is more complex and may be limited by different constraints in different growth regimes. We now state these limitations and the room for further model adjustments with more data in the Discussion section.

Nonetheless, if a counter exists, what is being counted that determines the final number? The authors consider that this might be a physical object or resource inside the parasite, or an extrinsic/extracellular resource. They investigate this by comparing the final cell number to a number of factors. First, the authors investigate the size of the RBC (by musing the diameter as an indicator)- little information is given about the source of the blood used, but it appears to be from a single donor of unknown age, who has approximately typical variance in RBC diameter (at least, after manipulation and storage). The authors observe little correlation between these variables.

We share the curiosity of the reviewer about what might be “counted” by the parasite. This shall be the subject of future studies, and our present study provides the necessary basis for asking this question and defines a framework to investigate it. Concerning the size of the host cell, the blood used was from a different donor for each of the replicas, which we now specify in the figure legend (line 302). No significant difference between the RBC diameters between the donors was observed. A correlation between RBC diameter and progeny number was indeed not observed.

Second the authors measure parasite size at the onset of schizogeny, and find that bigger parasites result in more daughter merozoites early in schizogeny (perhaps not surprising, given the earlier mentioned technical problems with measuring the first few steps of schizogeny), but that this different initial cell size doesn't result in a different final merozoite number, or as they describe it "not quite significant anymore". Previous p values were taken as cause for rejecting the timer hypothesis and the timer model. In this case the authors instead interpret the data as suggesting "that the setting of the counter might correlate with parasite cell size". This is inconsistent statistical and analytical handling, and highlights the earlier potential pitfall of rejecting timer-based models based on not gathering data that statistically show a correlation. This needs reworking to highlight that these data are inherently noisy, difficult to measure accurately, and aren't necessarily going strongly reveal a trend even where one biologically exists, and that this ought not be used as grounds for confident rejection of a model.

The Reviewer raises concerns about the consistency of the statistical interpretation of our data. We care deeply about the well-foundedness of our conclusions and hope to eliminate these concerns in the following. First, we hope that the issue about the “technical problems” in measuring the first division has been solved in our response to previous comments. Next, to clarify an apparent misunderstanding: As stated in the text (lines 329ff) and shown in now Fig. 5D-E, cell size at onset of nuclear division or 2 hours prior does significantly correlate with final merozoite number. The lack of significant p-value (0.08) only pertains to the correlation of cell size at the end of the schizont stage (tend) with merozoite number (now Fig. 5F). We have removed the unfortunate wording “not quite significant anymore” in that context. Finally, regarding potential mechanisms, a potential counter must be set before the first nuclear division is completed because only that way it can be set independent of the speed of nuclear multiplication. This observation gives the statistically significant correlation of volume at the onset of division and progeny number its relevance. We have reformulated the marked sentence for more clarity (lines 331ff). Furthermore, we point out that our rejection of the timer is now based on a revisited statistical analysis (Fig. 2), which is no longer based on a simple correlation between final number and duration, as detailed above.

Finally, the authors grow the parasites in dilute media, and find that they produce fewer daughter parasites. This is anecdotally unsurprising, as most Plasmodium laboratories are aware that sub-optimal growth conditions result in less healthy schizonts with fewer viable merozoites (and lower magnitudes of single-cycle expansion), but is nonetheless an important result that highlights explicitly how much this occurs in the specific conditions of dilute media. Given the lack of investigation of exactly which nutrient, carbon source, or combination thereof leads to the reduced merozoite number, it is unclear if or how much this is relevant to the scenario of a natural infection and realistic levels of that nutrient in a human or primate parasite environment.

As rightfully pointed out by the reviewer suboptimal growth conditions affecting parasite growth and multiplication rate have been shown in many instances. The number of studies that actually quantify a reduction in merozoite number under different growth conditions is certainly much lower (Brancucci et al. 2017 (lipids), Mancio-Silva et al. 2017 (calorie-restriction in mice), Tinto-Font et al. 2022 (temperature) come to mind). What our study adds to this body of literature is to which extent duration of the schizont stage and cell volume are affected in relation to progeny number at the single cell level. Importantly, we wanted to test whether the counter model still holds under these more adverse conditions, which we found to be the case. Along the lines of the work on calorie restriction and the likely implication of isoleucine in the process investigated in the laboratory of Maria Mota, it will be exciting to identify a “limiting factor” in future studies. Indeed, any study done in complete RPMI culture medium can be questioned regarding its physiological relevance and we added a sentence addressing this aspect in the discussion (lines 514ff). Yet, our medium dilution experiments suggest that at least to some degree an extracellular resource is implicated, which makes sense from a biological function point-of-view.

Minor issues

The manuscript confuses the terms "less" and "fewer". Fewer should be used for countable nouns (fewer daughter cells, fewer nuclei, fewer merozoites), less for uncountable nouns (e.g. less speed, less volume).

Thank you for pointing this out. The words have been replaced accordingly.

I didn't understand lines 93-95; "This excluded a timer and thereby confirmed a counter as the mechanism regulating termination of nuclear multiplication (Klaus et al., 2022). A direct correlation between duration of schizont stage and merozoite number is, however, still missing." If I understand the first sentence concludes that there ought not be a direct correlation between schizont duration and merozoite number, but the second sentence, says that that correlation is "however" missing. Isn't this expected? Perhaps reword for clarity?

Thank you for requesting clarification here. The exclusion of the timer by Klaus et al. 2022 was based on the correlation between duration of the first nuclear division cycle and the total duration of all nuclear replication phases. At no point did Klaus et al. count merozoites in live single cells, which was mainly due to lower spatial resolution of their images (M. Ganter, personal communication). Therefore, they could not directly assess the relation between progeny number and schizont stage duration, which we now report for the first time. The sentence was supposed to convey that this type of data was missing and was now reformulated for more clarity (line 114).

Lines 104

"We further uncover that throughout schizogony P. falciparum infringes on the otherwise ubiquitously constant N/C-ratio (Cantwell and Nurse, 2019)" This seems obvious to me, and not something uncovered by this study. In most of the numerous apicomplexans that divide by endoschizogeny, the cells achieve a near final size considerably before the final rounds of nuclear division so the N/C ratio must not remain constant - this is a direct corollary of many previous descriptions and not a novel finding of this study, and this claim here should be made more modest.

We understand the point raised by the reviewer but still think that our claim is justified due to several aspects. There are examples of eukaryotic cells that undergo multinucleated stages during division were the N/C-ratio is constant (Dundon et al. 2016, Cantwell and Nurse, 2019), while we are not aware of any counter-example in the literature. Studies have also shown that e.g. certain mutant yeast that fail to undergo cytokinesis will increase their volume by factor of up to 16 alongside the still replicating and growing nucleus maintain the N/C-ratio (Neumann et al. 2007, Jorgensen et al. 2007). This demonstrates the tremendous plasticity that cells can reveal with respect to nucleus and cell size regulation. Until the contrary was shown, it was conceivable that nuclear compaction, which does occur (Fig. 5H), compensates for the increase in nuclear number while the cell volume is only increasing slightly. Importantly, we are not aware of any literature where nuclear volume has been quantified for blood stage Plasmodium. Cell volume quantifications remain limited to modelling and the study by Waldecker et al., which provides a few datapoints throughout the IDC. Whether this finding is expected or not, formally speaking, our claim is justified, but for more clarity we replace “uncover” with “demonstrate”. We also introduce the N/C-ratio as cellular parameter in P. falciparum pointing out another divergent aspect of its biology and might in the future understand the functional implication of this usually constant ratio, which is still unclear.

Dundon SE, Chang SS, Kumar A, Occhipinti P, Shroff H, Roper M, Gladfelter AS. Clustered nuclei maintain autonomy and nucleocytoplasmic ratio control in a syncytium. Mol Biol Cell. 2016 Jul 1;27(13):2000-7.

Neumann FR, and Nurse P. Nuclear size control in fission yeast. J. Cell Biol. 2007; 179: 593–600. pmid:17998401

Jorgensen P, Edgington NP, Schneider BL, Rupeš I, Tyers M & Futcher B Molecular Biology of the Cell 18 (2007) The size of the nucleus increases as yeast cells grow.

Helena Cantwell, Paul Nurse; A homeostatic mechanism rapidly corrects aberrant nucleocytoplasmic ratios maintaining nuclear size in fission yeast. J Cell Sci; 132 (22)

I lack specialist statistical knowledge to comment on the statistical analyses performed on the correlation data, and in particular, whether the high p values for t-Tests for correlation are sufficient to support the argument that there is not a correlation, and whether these observations are sufficiently powered to robustly test that hypothesis.

We are confident that our reworked model analysis, as explained above, now sufficiently supports our hypotheses.

Reviewer #2 (Significance):

The manuscript purports to find a counting mechanism that determines parasite merozoite numbers, and that this coutner is set by an externally provided and diffusible resource. Many nutrients are in excess in normal culture media, but not all. If that counted nutrient(s) were normally in excess in the bloodstream, it could hardly be said to be the factor that is counted and that therefore defines merozoite number. Conversely, if the amount of that nutrient were increased in normal media, would parasites make even more merozoites? Further, if the "counted" item is a freely diffusible compound in the media, it should be equally accessible to each parasite in a culture condition, and isn't a reasonable explanation for the variable merozoite numbers in the normal media conditions. To me, it is unsurprising that parasites that are healthy and well fed are able to produce more merozoites, but I don't see this as being the same as support for a counter model where the parasite senses and counts a set number of merozoites to produce in response to a specific external counter. I think the shoehorning of this phenomenon into a paradigm used to describe some other eukaryotes may not be appropriate, and that the rejection of one overly simplistic timer model should not automatically lead to us dichotomously accepting a simple counter method as the alternative. The authors need to do more to either identify a countable input whose gradual increase leads to a predictable and gradual increase in merozoite number, to show that they do use a counter, or provide substantially more caveats to their argument that the parasites are using a counter based on an externally provided resource to determine merozoite number.

The reviewer comments on the feasibility of a counter mechanism based on an externally provided and diffusible resource. In fact this is a limited view of how a counter may arise and not the one we subscribe to. Rather, while a resource may be diffusible in the medium, it would need to be consumed during schizogony, and insufficiently replenished, in order to enable counting by dilution in the host cell. Furthermore, the reviewer has doubts that the fact that “healthy and well fed […] produce more merozoites” implies “support for a counter model”. We fully agree, and we argue in the manuscript that it is the correlations between schizogony durations and merozoite counts that support a counter model.

As we have argued above, the two alternative models we consider are inspired by paradigm from other eukaryotes, but their definitions in the present context are simple enough for them to be considered natural minimal models of schizogony. As the simplest imaginable phenomenological models of multiplication control, we find it natural to compare them, and we hope our new introductory section introduces them appropriately now. Naturally, we hope to expand on this simple model in the future and identify more precisely the limiting resources and describe a more direct response.

Audience - relatively specialised - likely interested audience would combine apicomplexan cell biologists, as well as theorists of cell division mechanism

Advance - limited - confirms phenomenon also described by other researchers in their institute, and extends to another related organism.

We would like to add that the present data are the first quantitative joint measurements of schizogony dynamics and outcome in P.falciparum and knowlesi. They allowed for the first time a direct correlation of duration and merozoite number, thereby accessing the question of growth control head on. Further they provide a quantitative reference of several key cellular parameters for anybody studying asexual blood stage parasites.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

Stürmer and colleagues used super-resolution time-lapse microscopy to probe the mechanism regulating the number of merozoites produced by a single cell in Plasmodium falciparum and P. knowlesi. The authors conclude the followings-

1. P. knowlesi has similar duration of schizont stage to P. falciparum, although having a 24 h intraerythrocytic developmental cycle (IDC) to 48 h of P. falciparum.
2. Nuclear multiplication dynamics suggests a counter mechanism of division- which is further suggested by a significant relation of merozoite numbers with schizont size at the onset of division.
3. Nutritional deprivation caused increase in nuclear volume and decrease in merozoite number. For the most part, the experiments that are presented in this manuscript support the conclusion of the authors. The data are presented in a concise and clear manner. However, some clarification and a couple of experiment (listed below) would improve this manuscript.

Major comments:

1. The authors generated at least 3 transgenic lines for this study, But the did not present any genetic validation of the lines in the manuscript. For completeness, I recommend to provide genetic validation (either pcr genotyping or whole genome sequencing) of the lines that were generated and used in this study in the supplement.

Our study exclusively used episomal expression of the respective fluorescent reporter (H2B-GFP, NLS-mCherry, and cytoplasmic GFP). As is customary in the field resistance to selection drugs and distinct fluorescent signals are assumed to sufficiently validate the presence of the plasmids. We now added the schematic maps of the plasmids in a new Fig. S1 to make our approach more visually clear.

1. In the H2B-GFP lines, the authors episomally GFP-tagged histone 2B to label the nuclear chromatin for both P. falciparum and P. knowlesi. This provides a very useful parasite line which enables the live time-lapse microscopy. Using these parasite lines, the authors first show that despite having a 24 h IDC in P. knowlesi vs 48 h in P. falciparum, both these parasites have a similar duration of the schizont stage (8.s vs 9.4 h). My concern here is whether this GFP-tagging is influencing the growth dynamics as in slowing down the P. knowlesi parasites. However, if that was the case authors should have seen that for P. falciparum too. Also, for the P. falciparum parasites that episomally express cytosolic GFP and Nuclear mCherry have a higher number of merozoites compared to the H2B-GFP P. falciparum and the authors speculate this is probably because of not tagging Histone 2B. Given this, it is important to show that none of the H2B-GFP parasites show any significant fitness cost due to GFP tagging of histone. I recommend a simple experiment to compare the multiplication rate of H2B-GFP lines to the parental lines in identical growth conditions. This suggested experiment was described in PMID: 35164549 to determine fitness cost of knockout lines. This experiment is vital for validation of the H2B-GFP lines and subsequent interpretation of the data that were presented in this manuscript.

We thank the reviewer for this excellent suggestion. To validate our lines further we now have carried out multiplication rate measurements similar to the one described in the designated publication for all the used lines alongside their parental strains (Fig. S2). We found no significant differences in between the wild type and the episomally expressing parasite lines (lines 131ff), which gives us confidence that episomal expression of tagged proteins do not significantly alter growth dynamics in these cases.

1. The authors used the microtubule live cell dye SPY555-Tubulin in P. falciparum to validate the findings presented in 1D and 1E. They did not do that for P. knowlesi. If there is no unsurmountable technical difficulty, I suggest doing the same with P. knowlesi. This will also address the concern that I have pointed out in #1.

Thank you for this suggestion. We have now generated the requested data with P. knowlesi, added it to what is now Supplemental Figure 3 and included it in our new analysis (Fig. 2I-J). The numerical values align well with the observations made when measuring schizont stage dynamics with the H2B-GFP expressing P. knowlesi line (line 158). A notable difference is that the Tubulin data strongly support the (refined) counter model, while the H2B data alone allow no distinction.

1. The data in Figure 3 shows that merozoite number does not depend on host cell diameter. My question here is, were these data collected using different donor blood? Or were this measured from different biological replicate? These are not clear from the writing. I am not sure about whether blood from various donor would have on the data, however, different preparation of the cells across various biological replicate will have some effect on host cell diameter hence on data. State if these were collected from independent biological replicates and about the donor blood.

The data results where indeed collected from three independent biological replicates using different donor blood batches. This is now stated in the figure legend. The batches displayed no difference in RBC diameter.

1. It is interesting to see that nutrient-limited conditions increase average nuclear volume but less merozoite numbers. In this experiment, as I understand, complete media was diluted 0.5x, which basically diluted every component of the media by half. From this experiment I can see nutritional deprivation as a whole having an effect and supports the counter mechanism, it would be intriguing to see if there is any effect of a particular nutrient have any effect on progeny division. For example, parasites can be grown in amino acid deprived media (except isoleucine) which makes the parasites fully dependent on host cell amino acids. This sort of specific nutrient deprivation will probably allow the authors to probe for specific nutrients that plays role as counter mechanism factor.

This is indeed a very exciting direction we would like to investigate in more detail in follow-up studies. Our aim for this study was to confirm that nutrient deprivation actually affects “counting” and to provide a workflow to investigate individual nutrients. In the meantime the Mota group, in a study we now cite in the discussion (lines 507ff), actually reported that isoleucine (and possibly methionine) levels are linked to progeny number. A follow-up on this topic using our strains and methodology is certainly worthwhile but requires more detailed analysis in the future.

Minor comments:

1. P. knowlesi is sometimes just written as knowlesi. Please, write P. Knowlesi.

Has been corrected.

1. Supplemental figure 1D, missing x-axis label.

We added the x-axis label.

1. In line 105, define N/C.

Done.

1. In line 205, I assume the authors mean episomally, not episomally.

Thank you for pointing this out. We have replaced “ectopically” with “episomally” throughout the text.

1. In line 275, Duration of Schizont stage was slightly....

Has been corrected.

1. All 'ml' or 'µl' should be 'mL' or 'µL'.

Changes have been made.

1. Define iRPMI.

We added a definition (line 610).

1. In line 475, replace 'as' with 'and'.

Done.

Reviewer #3 (Significance):

The factors that regulate the number of progenies in malaria parasites remain unknown. While there are few previous studies attempting to answer the question, those studies were done on fixed stained cells. In this study, the authors used genetically modified fluorescent P. falciparum and P. knowlesi parasites that enable live microscopy. These parasites coupled with super-resolution time-lapse microscopy the authors attempt to investigate the mechanism(s) at play in regulating progeny division. This manuscript provides data to suggest that external resources might have some role in progeny division and supports the counter mechanism. More careful validation of the transgenic lines that were used to collect data presented needs to be more systematic and rigorous.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Stürmer and colleagues used super-resolution time-lapse microscopy to probe the mechanism regulating the number of merozoites produced by a single cell in Plasmodium falciparum and P. knowlesi. The authors conclude the followings:<br /> - a. P. knowlesi has similar duration of schizont stage to P. falciparum, although having a 24 h intraerythrocytic developmental cycle (IDC) to 48 h of P. falciparum.<br /> - b. Nuclear multiplication dynamics suggests a counter mechanism of division- which is further suggested by a significant relation of merozoite numbers with schizont size at the onset of division.<br /> - c. Nutritional deprivation caused increase in nuclear volume and decrease in merozoite number.<br /> For the most part, the experiments that are presented in this manuscript support the conclusion of the authors. The data are presented in a concise and clear manner. However, some clarification and a couple of experiment (listed below) would improve this manuscript.

Major comments:

1. The authors generated at least 3 transgenic lines for this study, But the did not present any genetic validation of the lines in the manuscript. For completeness, I recommend to provide genetic validation (either pcr genotyping or whole genome sequencing) of the lines that were generated and used in this study in the supplement.
2. In the H2B-GFP lines, the authors ectopically GFP-tagged histone 2B to label the nuclear chromatin for both P. falciparum and P. knowlesi. This provides a very useful parasite line which enables the live time-lapse microscopy. Using these parasite lines, the authors first show that despite having a 24 h IDC in P. knowlesi vs 48 h in P. falciparum, both these parasites have a similar duration of the schizont stage (8.s vs 9.4 h). My concern here is whether this GFP-tagging is influencing the growth dynamics as in slowing down the P. knowlesi parasites. However, if that was the case authors should have seen that for P. falciparum too. Also, for the P. falciparum parasites that episomally express cytosolic GFP and Nuclear mCherry have a higher number of merozoites compared to the H2B-GFP P. falciparum and the authors speculate this is probably because of not tagging Histone 2B. Given this, it is important to show that none of the H2B-GFP parasites show any significant fitness cost due to GFP tagging of histone. I recommend a simple experiment to compare the multiplication rate of H2B-GFP lines to the parental lines in identical growth conditions. This suggested experiment was described in PMID: 35164549 to determine fitness cost of knockout lines. This experiment is vital for validation of the H2B-GFP lines and subsequent interpretation of the data that were presented in this manuscript.
3. The authors used the microtubule live cell dye SPY555-Tubulin in P. falciparum to validate the findings presented in 1D and 1E. They did not do that for P. knowlesi. If there is no unsurmountable technical difficulty, I suggest doing the same with P. knowlesi. This will also address the concern that I have pointed out in #1.
4. The data in Figure 3 shows that merozoite number does not depend on host cell diameter. My question here is, were these data collected using different donor blood? Or were this measured from different biological replicate? These are not clear from the writing. I am not sure about whether blood from various donor would have on the data, however, different preparation of the cells across various biological replicate will have some effect on host cell diameter hence on data. State if these were collected from independent biological replicates and about the donor blood.
5. It is interesting to see that nutrient-limited conditions increase average nuclear volume but less merozoite numbers. In this experiment, as I understand, complete media was diluted 0.5x, which basically diluted every component of the media by half. From this experiment I can see nutritional deprivation as a whole having an effect and supports the counter mechanism, it would be intriguing to see if there is any effect of a particular nutrient have any effect on progeny division. For example, parasites can be grown in amino acid deprived media (except isoleucine) which makes the parasites fully dependent on host cell amino acids. This sort of specific nutrient deprivation will probably allow the authors to probe for specific nutrients that plays role as counter mechanism factor.

Minor comments:

1. P. knowlesi is sometimes just written as knowlesi. Please, write P. Knowlesi.
2. Supplemental figure 1D, missing x-axis label.
3. In line 105, define N/C.
4. In line 205, I assume the authors mean episomally, not ectopically.
5. In line 275, Duration of Schizont stage was slightly....
6. All 'ml' or 'µl' should be 'mL' or 'µL'.
7. Define iRPMI.
8. In line 475, replace 'as' with 'and'.

Significance

The factors that regulate the number of progenies in malaria parasites remain unknown. While there are few previous studies attempting to answer the question, those studies were done on fixed stained cells. In this study, the authors used genetically modified fluorescent P. falciparum and P. knowlesi parasites that enable live microscopy. These parasites coupled with super-resolution time-lapse microscopy the authors attempt to investigate the mechanism(s) at play in regulating progeny division. This manuscript provides data to suggest that external resources might have some role in progeny division and supports the counter mechanism. More careful validation of the transgenic lines that were used to collect data presented needs to be more systematic and rigorous.

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Referee #2

Evidence, reproducibility and clarity

This is a solid study that further characterises the dynamics of nuclear division in Plasmodium falciparum and P. knowlesi. Of two, among potentially several, models for how the number of daughter nuclei, and thus parasites - (called merozoites in this genus), are one that posits nuclei divide until a fixed timer ends, and one that posits that nuclei divide to reach a fixed number that is defined by a cellular counter. I find some practical difficulties in definitive measurement of either model, one issue with the former is that experimental definition of the start of the timer is problematic - we may define the starter's gun (eg by the first nuclear division) but it isn't necessary that the cell is using that same start time. Additionally, as the authors confirm here, being sure when that first nuclear division has occurred is particularly tricky with Plasmodium parasites, in part because the first few nuclei seem to clump together, preventing one from unambiguously calibrating the first division. Furthermore, getting decent replicate numbers is hard because of the difficulties of time lapse microscopy, and most Plasmodium studies (including this one) suffer from low enough numbers that it isn't always clear whether the numbers support one model over another.

Nonetheless, several recent studies, particularly a study from the same institute (Klaus et al., 2022) employing timelapse imaging of nuclei, and timing the nuclear division of parasites, finds poor correlation between the duration of "schizogeny" (although perhaps using a different definition to the one used by the parasite) and the final number or merozoites. They therefore argue that there is poor evidence for a timer, and conclude by elimination that a counter must exist instead. A review by some of the authors of that study and some of this current study (Voß et al 2023), also concludes that the data from Klaus and colleagues "strongly support" a counter model. This current study also concludes that a counter model controls final nuclear/merozoite number in P. falciparum and P. knowlesi. This much at least is not particularly novel given the recent work on this topic, although the addition of the P. knowlesi data is interesting and consistent with the prior P. falciparum work. As above, the authors concede that it is difficult to determine with strong confidence when the first nuclear division has occurred, so it may well be that there is substantial noisiness in the time that they define schizogeny to commence. If that were the case, this would contribute to the poor correlation observed between schizogeny duration and number of merozoites produced, so this could be an important confounding experimental factor. This deserves some more discussion by the authors. Alternative methods to count absolute DNA content (rather than trying to count individual nuclei) might be useful ways of independently confirming this phenomenon. Alternative possibilities for what constitutes the "start" of a possible timer are also warranted - it could be for example, the first division of one of the other organelles.

These and previous authors in any case conclude that a counter model must exist through exclusion of a timer model. I am less convinced that the evidence discounting the timer is conclusive, and that a straight counter model is the only alternative. Indeed I am unconvinced by the suitability of this strictly dichotomous two-model system to categorise the division of unicellular eukaryotes, and these theories are not universally held to be sufficient to describe division. Nonetheless, if a counter exists, what is being counted that determines the final number? The authors consider that this might be a physical object or resource inside the parasite, or an extrinsic/extracellular resource. They investigate this by comparing the final cell number to a number of factors. First, the authors investigate the size of the RBC (by musing the diameter as an indicator)- little information is given about the source of the blood used, but it appears to be from a single donor of unknown age, who has approximately typical variance in RBC diameter (at least, after manipulation and storage). The authors observe little correlation between these variables. Second the authors measure parasite size at the onset of schizogeny, and find that bigger parasites result in more daughter merozoites early in schizogeny (perhaps not surprising, given the earlier mentioned technical problems with measuring the first few steps of schizogeny), but that this different initial cell size doesn't result in a different final merozoite number, or as they describe it "not quite significant anymore". Previous p values were taken as cause for rejecting the timer hypothesis and the timer model. In this case the authors instead interpret the data as suggesting "that the setting of the counter might correlate with parasite cell size". This is inconsistent statistical and analytical handling, and highlights the earlier potential pitfall of rejecting timer-based models based on not gathering data that statistically show a correlation. This needs reworking to highlight that these data are inherently noisy, difficult to measure accurately, and aren't necessarily going strongly reveal a trend even where one biologically exists, and that this ought not be used as grounds for confident rejection of a model.

Finally, the authors grow the parasites in dilute media, and find that they produce fewer daughter parasites. This is anecdotally unsurprising, as most Plasmodium laboratories are aware that sub-optimal growth conditions result in less healthy schizonts with fewer viable merozoites (and lower magnitudes of single-cycle expansion), but is nonetheless an important result that highlights explicitly how much this occurs in the specific conditions of dilute media. Given the lack of investigation of exactly which nutrient, carbon source, or combination thereof leads to the reduced merozoite number, it is unclear if or how much this is relevant to the scenario of a natural infection and realistic levels of that nutrient in a human or primate parasite environment.

Minor issues

The manuscript confuses the terms "less" and "fewer". Fewer should be used for countable nouns (fewer daughter cells, fewer nuclei, fewer merozoites), less for uncountable nouns (e.g. less speed, less volume).

I didn't understand lines 93-95;<br /> "This excluded a timer and thereby confirmed a counter as the mechanism regulating termination of nuclear multiplication (Klaus et al., 2022). A direct correlation between duration of schizont stage and merozoite number is, however, still missing."<br /> If I understand the first sentence concludes that there ought not be a direct correlation between schizont duration and merozoite number, but the second sentence, says that that correlation is "however" missing. Isn't this expected? Perhaps reword for clarity?

Lines 104<br /> "We further uncover that throughout schizogony P. falciparum infringes on the otherwise 105 ubiquitously constant N/C-ratio (Cantwell and Nurse, 2019)" This seems obvious to me, and not something uncovered by this study. In most of the numerous apicomplexans that divide by endoschizogeny, the cells achieve a near final size considerably before the final rounds of nuclear division so the N/C ratio must not remain constant - this is a direct corollary of many previous descriptions and not a novel finding of this study, and this claim here should be made more modest.

I lack specialist statistical knowledge to comment on the statistical analyses performed on the correlation data, and in particular, whether the high p values for t-Tests for correlation are sufficient to support the argument that there is not a correlation, and whether these observations are sufficiently powered to robustly test that hypothesis.

Significance

The manuscript purports to find a counting mechanism that determines parasite merozoite numbers, and that this coutner is set by an externally provided and diffusible resource. Many nutrients are in excess in normal culture media, but not all. If that counted nutrient(s) were normally in excess in the bloodstream, it could hardly be said to be the factor that is counted and that therefore defines merozoite number. Conversely, if the amount of that nutrient were increased in normal media, would parasites make even more merozoites? Further, if the "counted" item is a freely diffusible compound in the media, it should be equally accessible to each parasite in a culture condition, and isn't a reasonable explanation for the variable merozoite numbers in the normal media conditions. To me, it is unsurprising that parasites that are healthy and well fed are able to produce more merozoites, but I don't see this as being the same as support for a counter model where the parasite senses and counts a set number of merozoites to produce in response to a specific external counter. I think the shoehorning of this phenomenon into a paradigm used to describe some other eukaryotes may not be appropriate, and that the rejection of one overly simplistic timer model should not automatically lead to us dichotomously accepting a simple counter method as the alternative. The authors need to do more to either identify a countable input whose gradual increase leads to a predictable and gradual increase in merozoite number, to show that they do use a counter, or provide substantially more caveats to their argument that the parasites are using a counter based on an externally provided resource to determine merozoite number.

Audience - relatively specialised - likely interested audience would combine apicomplexan cell biologists, as well as theorists of cell division mechanism

Advance - limited - confirms phenomenon also described by other researchers in their institute, and extends to another related organism.

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Referee #1

Evidence, reproducibility and clarity

Summary

Malaria parasites replicating in human red blood cells show a striking diversity in the number of progeny per replication cycle. Variation in progeny number can be seen between different species of malaria parasites, between parasite isolates, even between different cells from the same isolate. To date, we have little understanding of what factors influence progeny number, or how mechanistically it is controlled. In this study, the authors try to define how the mechanism that determines progeny number works. They propose two mechanisms, a 'counter' where progeny number is determined by the measurement of some kind of parasite parameter, and a 'timer' where parasite lifecycle length would be proportional to progeny number. Using a combination of long-term live-cell microscopy and mathematical modelling, the authors find consistent support for a 'counter' mechanism. Support for this mechanism was found using both Plasmodium falciparum, the most prominent human malaria parasite, and P. knowlesi, a zoonotic malaria parasite. Of the parameters measured in this study, the only thing that seemed to predict progeny number was parasite size around the onset of mitosis. The authors also found that during their replication inside red blood cells, malaria parasites drastically increase their nuclear to cytoplasmic ratio, a cellular parameter remains consistent in the vast majority of cell-types studied to date.

Major Comments

• It is stated a few times in this study that P. knowlesi has an ~24 hour lifecycle, and while this is the case for in vivo P. knowlesi, it was established in the study when P. knowlesi A1-H1 was adapted to human RBCs (Moon et al., 2013) that this significantly extended the lifecycle to ~27 hours, which should be made clear in the text. As much of this study revolves around lifecycle length and timing, the authors should consider some of their findings with the context that in vitro adaption can significantly alter lifecycle length.
• The dichotomous distinction between 'timer' and 'counter' as mutually exclusive mechanisms seems to be a drastic oversimplification. Considering the drastic variation we see in merozoite number across species, between isolates, and between cells, it seems much more likely that there are factors controlled by both time-sensed and counter-sensed mechanisms that both influence progeny number. Additionally, the only parasite parameter measured in this study, size at time of first nuclear division, explained only a small proportion of the variance observed in merozoite number.
• For modelling of a timer-based mechanism, the designation of t0 is subjective. The authors chose the time of first nuclear division as their t0. It is possible that a timer-based mechanism could not be supported based on this model the chosen t0 differs from when the "parasite's timer" starts. For example, t could also have been designated as the time from merozoite invasion (t0) to egress (tend). It would be unreasonable to suggest the authors repeat experiments with a longer time-frame to address this, but this possibility should be discussed as a limitation of the model. It may also be possible to develop a different model where t0 = merozoite invasion and tend = egress, and test this model against the data already collected in this study.
• The calculation of the multiplication rate is confusingly defined. In Figure 1 it is stated that it is "...based on t and n", which would imply that the multiplication rate is the number of merozoites formed per hour of schizogony, which would give an average value of ~2 for P. falciparum and ~1.5 for P. knowlesi. The averages rate values shown, however, are in the range of 0.15-3. The authors should clarify how these values were determined.
• In Figure 2, the time from tend until egress is calculated, and this is interpreted as the time required for segmentation. In the Rudlaff et al., 2020 study cited in this paper, it is shown that segmentation starts before the final round of nuclear divisions are complete. Considering this, the time from tend until egress is not an appropriate proxy for segmentation time. The authors should consider rewording to something akin to "time from final nuclear division until egress" to more accurately reflect these data.
• There is a significant discrepancy between the data in Figure 5 and Supplementary Figure 8. In Supplementary Figure 8, the authors establish that culturing parasites in media diluted 0.5x has a marginal effect on parasite growth, with no discernible change in parasitaemia over 96 hours. By contrast, in Figure 5a the parasitaemia of parasites cultured in 0.5x diluted media is approximately 5-fold lower than those in 1x media. The authors should explain the significant discrepancy between these results.
• In Supplementary Figure 4, the mask on the cell at t0 shows two distinct objects, but it seems very unlikely that they are two distinct nuclei as they vary approximately 5-fold in diameter. The authors should provide more detail on how their masking was performed for their volumetric analysis. Specifically, whether size thresholds were also applied during object detection.

Minor Comments

• Line 45-48 mentions that merozoite number influences growth rate and virulence, but the corresponding reference (Mancio-Silva et al., 2013) only discusses the relationship between merozoite number and growth rate, not virulence.
• Line 59 states that a 48 hour lifecycle is a baseline from which in vitro cultured parasites deviate. Clinical isolates also show variation in lifecycle length and so it is more accurate to just say that 48 hours is an average, rather than a baseline.
• Line 63 cites a study for the lifecycle length of P. knowlesi (Lee et al., 2022), but there seems to be no mention of lifecycle length in this reference
• If I am interpreting Figure 3B correctly, this is essentially a paired analysis where the same erythrocytes are measured twice, once at t0 and once at tend. If this is the case, this data may be better represented with lines that connect the t0 and tend values.
• Figure 3A seems to imply that to calculate diameter of the erythrocytes, three measurements were made and averaged for each cell. I think this is a nice way to get a more accurate erythrocyte diameter, but if this is the case, it should be specified in the figure legend or methods.
• In Figure 4I it is shown that in P. falciparum merozoite number doesn't correlate with nucleus size, but for P. knowlesi in Supplementary Figure 7c, a significant anticorrelation is observed. The authors should state this in the text and discuss this discrepancy.
• The authors show that merozoite number roughly correlates with cell size at t0 but it would be interesting to see whether cell size at tend also corresponds with cell size at t0. This might help answer whether the cell is larger because it has more merozoites, or whether it has more merozoites because it is larger.
• I don't feel that "nearly identical" is an appropriate summary of erythrocyte indices in Supplementary Figure 9, considering there is a statistically significant increase in mean cell volume. I think it is unlikely that this change is consequential, and performing these haematology analyses is a nice quality control step, but this change should be stated in the text.
• In Supplementary Figure 8, parasitaemia only increases ~2-fold compared to >5-fold the previous two cycles. It seems likely that at the final timepoint on this graph the parasites are starting to crash, and therefore it may be best to end the graph with the 96 hour timepoint.
• The error bars in Figure 5C aren't easily visible, moving them in front of the datapoints may help their visibility.
• In Figure 6D & E, the y-axis labels should be changed to whole integers as all the values in the graph are whole numbers.
• My interpretation of Figure 6 C-E, is that these are the same cells measured at three time points (t-2, t0 and tend). If this is the case, 6C is missing the cell that has a merozoite number of 8, which is presumably why the y-axes are not equalised for the three graphs.

Significance

In the asexual blood-stage of their lifecycle, malaria parasites replicate through a process called schizogony. During schizogony an initially mononucleated parasite undergoes multiple asynchronous rounds of mitosis followed by nuclear division without cytokinesis, producing a variable number of daughter nuclei. Parasites then undergo a specialised cytokinesis, termed segmentation to where nuclei are packaged into merozoites that go on to invade new host cells. While nucleus, and therefore merozoite, number are known to be varied between cells, across isolates, and across species, little is known about the mechanisms regulating merozoite number. In this study, the authors use live-cell microscopy to understand how parasites determine their progeny number. They suggest that parasites regulate their progeny number using a 'counter' mechanism, which would respond to the size or concentration of a cellular parameter, as opposed to a 'timer' mechanism. Long-term live-cell microscopy experiments using malaria parasites are extremely technically challenging, and the authors should be commended for their efforts in this regard. While I agree that the data generated from these experiments are technically sound, I have some reservations expressed above about the interpretation of some of these results. I would strongly encourage the authors to consider rewording some of their interpretations taking into account some of the caveats listed above. I would also consider fitting/testing an additional mathematical model where the time-frame proposed for the 'timer' mechanism begins following merozoite invasion.

This work is of specific interest to anybody who grows malaria parasites, as the dynamics of their growth is obviously important to understand. Further, this work is of interest more generally to cell biologists who study the regulation of progeny number or cell size. I have no experience with the application of mathematical modelling to understand biological systems, and so I cannot comment on the interest of this work to that field.